KUHN:

Wes Sharrock

And

Rupert Read

TABLE OF CONTENTS

Preface 3

Chapter One: Introduction: the legendary Thomas Kuhn 6

Part One: Exposition 34

Chapter Two: The Structure of Scientific Revolutions 34

Chapter Three: The Historical Case-Studies 87

Part Two: Critical Issues 117

Chapter Four: Kuhn and the Methodologists of Science 117

Section A: The Philosophy of Natural Science 117

Section B: The Philosophy of Social Science 148

Chapter Five: Incommensurability 1: relativism about truth and meaning 162

Chapter Six: Incommensurability 2: world changes 195

Chapter Seven: Conclusion: The Unresolved Tension 223

Preface

We believe that Thomas Kuhn is the first person to have found a way of describing the nature of science (of our paradigms of science, and of what resembles them) without grossly falsifying it.. Kuhn aimed to fundamentally reorient the history and philosophy of science. In a way, he succeeded in this – but not in the way that his actual intellectual achievement demanded. We hope in this book to play a part in righting this situation: in making available the
thoughts of Kuhn, in showing to new readers and old the nature of the tremendous achievement Kuhn accomplished, and which demands recognition: the curing of philosophy of science ... and how to begin to take in and move on from that curing.

Our book is concerned above all with the entirety of Kuhn's writings
published during his lifetime, including of course those collected in The
Road Since Structure (TRSS). At his death, Kuhn was still trying to write a
new manuscript (see p.vi and p.2 of TRSS). When that is published in some
form by Kuhn's literary executors (James Conant and John Haugeland), then
some amendment of the story told in this volume may be necessary; but still
not that much. For our book aims in the first instance 'simply' to provide
the first book-length sympathetic rendition of Kuhn's central life-work. We emphasize strongly
that Kuhn's philosophical _ especially his deflationary and therapeutic
ambitions are paramount; _and_ that these are best appreciated by being seen
in continuity with his historical case-studies.


This book has been our joint work throughout – together, we have written, produced and agreed upon every line (and the order in which our names appear on the cover is only thus because Wes, most of whose work is jointly-authored, is fed up with nearly always being listed last due to his surname beginning with an ‘S’!). But wWe wish to thank also the following people for their assistance in various ways, b
big and small, with the work that this book has involved:

Ralph Berry,
Alexander Bird,
Alice Crary,
Wil Coleman,
Jeff Coulter,

Fred D’Agostino

Arthur Danto

Miguel De la Franca
Dave Francis,
Steve Fuller,
Ian Hacking,
Richard Hamilton,
Paul Hoyningen-Huene,
Nick Huggett,
David Johnston,

Keekok Lee,

Bob Lockie,
John Preston,

Angus Ross,
Seamus Simpson,
Thomas Uebel;
audiences at the British Philosophy of Science Society (Sheffield), at
UEA, at Binghamton University, at Colgate University;

the editors of the Harvard Review of Philosophy and of Wittgenstein Studies;
and all the understanding people at Polity Press.

We would particularly like to mention the help we have received from the
following (we like to think) 'fellow-spirits' in returning to the real Kuhn:
James Conant, Stefano Gattei, John Haugeland, Vasso Kindi and Jehane Kuhn.

Rupert owes a special debt to undergraduate classes at the University of
Manchester and at UEA which have helped him to work through portions of the
manuscript; and to the Philosophy Department of the University of Chicago,
where he took a sabbatical as a Visiting Scholar while the book was being
completed, and sat in on Conant and Haugeland's graduate class on Kuhn. The
members of that class provided invaluable assistance, particularly Jay
Elliot, Martin Gustafson, Clinton Tolley, besides of course Conant and Haugeland
themselves.
.
Rupert wishes to thank especially also the following: Glendra and Graham
Read (for love _and_ money), Emma Willmer (for love) and the University of
East Anglia (for money).

Wes owes (as usual) a lot to John Lee.

Rupert Read and Wesley Sharrock,
Norwich (Philosophy, Economic and Social Sciences) and Manchester
(Sociology),
May 2001.

When Thomas Kuhn went to his grave in 1996, he was convinced that his lifework had been misunderstood. He failed to complete a categorical restatement of his position before a fatal illness took his life. We think Kuhn was right about the response to his work, and will here try to set that situation right. If Kuhn was perhaps the most influential philosopher writing in English since 1950, even perhaps the most influential academic in any discipline, the fact that he could rightly feel that both friends and foes had entirely misunderstood him implies a sad comment on the state of contemporary intellectual culture, academic and otherwise.

Kuhn, born in 1922, trained as a physicist, but early turned to the history of science, and then to philosophy of science. He published four books during his lifetime. One of the books, The Essential Tension (1977) collected some of his key papers, whilst two others books, his first The Copernican Revolution (1957) and his last , The Black-body Problem and the Quantum Discontinuity, 1894-1912 (1979,1984) were historical studies of revolutionary periods in the sciences of astronomy and atomic physics respectively. Immense success came with his long-delayed second book, The Structure of Scientific Revolutions (SSR) in 1962. This gave a general and strongly philosophical interpretation of the long-term development of the physical sciences in the West. The book immediately attracted widespread attention, has sold about a million copies, and became one of the very most frequently cited philosophy texts of the twentieth century. It remains, today, as controversial as upon first publication.

Kuhn did not attribute his immense success entirely to his own achievements. He was only one of a number of people, including the French philosophers/historians of science Gaston Bachelard and Georges Canguilhem, and a small number of Anglo-American philosophers such as Mary Hesse, Stephen Toulmin and Norwood Russell Hanson, as well as their German precursor, Ludwig Fleck, whose Genesis of a Scientific Fact, published in 1932, Kuhn acknowledged had partially anticipated his own work. The time had been right, Kuhn had put these new ideas in an accessible way, and the Zeitgeist had taken over from him.

To say that Kuhn has been the most influential philosopher writing in English during the last forty years is all the more striking if a substantial part of his work was in the history , rather than the philosophy, of science. If one excludes the illustrative examples from the key work, The Structure of Scientific Revolutions, then the argumentative content, as distinct from the historical exemplification of that book is scarcely ten thousand words. Further, though Kuhn’s work was in its entirety in either history or philosophy of science, his influence has been extraordinarily widespread, affecting developments in the main stream of philosophy as well as a host of disciplines in the social sciences and humanities, and beyond. Steven Weinberg (writing in the New York Review of Books, October 8, 1998, 48-52) rightly remarked that Kuhn’s historical work alone would not have earned him the household-name status that he now has among the chattering classes. Whether that ‘influence’ has been for good or ill is much debated.

Kuhn was greatly disappointed that even most of those well-disposed toward him misconstrued his work, and he found it necessary to dissociate himself from many of his self-appointed followers, but this does not mark him out as singularly hard to please. Kuhn was as critical of himself as he was of others, and over the years, made repeated attempts to restate, and to an extent, revise them in a way which was he found satisfactory. He was making one further attempt in the years before his death. A letter from Kuhn to the philosopher Guy Robinson ( quoted in Robinson’s Philosophy and Mystification) expresses clearly Kuhn’s sense of having found it hard to make out himself what he was trying to say:

The challenge of getting Kuhn right, then, is not a small one, and confronts us as much as the wider army of commentators and critics.

One important way to rise to that challenge is to recognise the close connection between Kuhn’s history and philosophy of science, a much stronger connection than is usually appreciated, even when Kuhn is numbered among the founders of the ‘historical approach’ to the philosophy of science. Sadly, the key work, The Structure Of Scientific Revolutions is a book that is commonly cited by reference to the whole work, rather than by reference to any specific passages, and his historical studies, though they make up a substantial proportion of his body of work are seldom read in connection with SSR

Whilst Kuhn’s work in the history of science would never have earned him a reputation comparable to that which he holds on the basis of SSR, his concern with the history of science retains an essential connection to his philosophical ideas. If we seek the origins of the things Kuhn says about the philosophy of science in his studies in the history of science, we can start to get a much better grasp on his intended meaning.

Kuhn’s reputation is very much the one that Steven Weinberg (a leading, Nobel prize winning physicist) recently reiterated and decried:

Perhaps readers can recognise in Weinberg’s remarks a manifestation of the acute animosities that have been known as ‘the Science wars’, and that centrally involved hostilities between the relatively new and rapidly burgeoning pursuit of ‘science studies’ which recruited mainly from the humanities and social sciences, and those who – either philosophers and/or scientists – saw themselves as defenders of science against attack from science studies. Kuhn is often regarded as responsible for giving science studies much of its initial impetus.

Weinberg is at least right in supposing that the reasons why he disapproves of Kuhn are much the same ones as certain philosophers, historians etc. have had for making a hero out of him. Both ‘friends’ and ‘foes’ are apt to endow Kuhn with the status of ‘radical sceptic about the achievements of science’.. We could not honestly say that we find nothing in Kuhn that might be symptomatic of radical scepticism about science, but we think that it is only when those ideas or remarks are taken in isolation, and without careful consideration, that they can be construed in that way. There is plenty of evidence that Kuhn did not intend what he had to say as involving scepticism at all (except about ( the traditional) philosophy of science)

Weinberg complains that Kuhn makes change in science seem ‘more like a religious conversion than an exercise of reason’: when one scientific scheme displaces another ‘it is not only our scientific theories which change but the very standards by which scientific theories are judged, so that the [scientific frameworks] which govern successive periods of normal science are incommensurable’. [48] This means that there is no common standard against which to compare rival scientific theories. There is, therefore, no sense in which theories developed after a scientific revolution can be said to add cumulatively to what was known before the revolution. The displacement of one scientific theory by a newer one may mean that ‘when new [scientific] problems arise they will be replaced [only] by new theories that are better at solving those problems’ but that this signifies ‘no overall improvement.’ (48.) It is right to say that Kuhn compares scientific change to conversion, but just wrong to suggest that drastic conclusions are implied. Kuhn does not preclude the possibility of progress in science, but does deny that progress in science is progress toward anything. Weinberg thinks that science does progress toward something, that it ‘brings us closer and closer to objective truth’ and rightly sees that Kuhn would disagree. Weinberg quotes Kuhn himself:

Disputing Weinberg’s idea of what progress involves is not the same as denying that there is any progress.

Now compare Weinberg’s final complaint:

Again, this trivialises Kuhn’s deep reflections upon scientific progress and caricatures absurdly Kuhn’s understanding of the scientific quest. One might wonder why Weinberg would not be much more discouraged by Karl Popper’s philosophy, one that many scientists have greatly admired, but who certainly does dismiss the idea of any ‘permanent parts’ to human knowledge?

When confronted with the various views attributed here to Kuhn, rather than thinking that this sounds either thrillingly provocative, or [like Weinberg] dangerously misguided, one ought to pause for thought about what Kuhn might mean when he says these often provocative things. Even if Kuhn does say that scientific revolutions may be like religious conversions, just how are they like religious conversions? What aspect of a religious conversion is Kuhn drawing attention to in his analogy? And is a religious conversion really the very opposite of ‘an exercise of reason’? Nor should we instantly react to Kuhn’s claim, that

for his purposes, , the ‘notion of reality as it has ordinarily functioned in the philosophy of science’ (TRSS, 115) is of no use. Is it entirely obvious what he is saying here? How did that notion ‘ordinarily function’ in the philosophy of science, and just what reservations does Kuhn have about its use? We should not jump to the conclusion that Kuhn is absurdly denying that there is any ‘real world out there’ (as his foes and, even, sometimes, his friends, like to say). The critical element in the quote from Kuhn just given is that he is rejecting a doctrine in the philosophy of science, and it would be quite wrong to infer, for example, that the notion of ‘reality’ (or of ‘nature’) has no place whatsoever in his account of scientific revolutions

Weinberg’s is a pretty standard critique of the Thomas Kuhn who has become the legendary figure in the folklore of philosophy, the social sciences, the humanities, and beyond, featuring as both a bogeyman with which Realists and neo-positivists scare themselves and try to intimidate their opponents, and, to his admirers, as an adventurous and heroic one . Legendary figures often have little relationship to the actual human beings who were their prototypes, and the legendary Thomas Kuhn may have as little relationship to the real thinker as the legendary Robin Hood had to the person who - if any - occasioned his mythology. We have, however, substantial basis in his own writings for identifying the real Thomas Kuhn.

Alas, that Thomas Kuhn may prove something of a disappointment to the Legend’s admirers and critics alike. Depriving science of its ‘objectivity’ might seem like a transforming achievement on the cultural landscape, revealing that the faith that we have reposed in science is misplaced, and that it is indeed ‘ no better than’ astrology or witchcraft. Whilst Paul Feyerabend, Kuhn’s ‘anarchist’ contemporary, might have raged against the cultural imperialism of science, this part of his critique is not one to which Kuhn gave any sign of assenting. In fact, views described in the manner in which Feyerabend described his own view seemed to Kuhn ‘vaguely obscene’. Devastating the philosophy of science as Kuhn aspired to do is no small achievement in itself, though it need not - and in Kuhn’s view did not - detract one whit from the achievements of science. The critique of scientism - cultural imperialism in the name of science - is something which can be undertaken quite independently of any views that one holds with respect to the ‘objectivity’ or otherwise of science itself. Feyerabend’s real attack is rather more upon scientists than upon science as such, claiming that many scientists, and their cultural advocates, are both ignorant and presumptuous [outside their technical expertise, where they persist in trespassing]. They are ignorant of many of the practices, cultures, and traditions that - ‘in the name of science’ - they seek to condemn and eradicate, and are presumptuous in thinking that their competence in a restricted domain of scientific work [nowadays, a very narrow domain] entitles them to - ironically - oracular status within the wider culture.

If Kuhn is allowed to be even a modestly consistent thinker - and we shall present him as a rather single-minded and dogged one - then he cannot seriously be considered as either radical sceptic or Relativist. There are just too many arguments in his work that are at odds with those words of his that - taken alone! - might seem to justify these attributions. Our defensiveness on Kuhn’s behalf on these matters is no product of uncritical devotion, and we will try to identify the important places where we judge that Kuhn’s argument – his grip on his own words and intentions -- gets into real trouble.

Still, the first vital contribution to critical assessment of Kuhn’s views is to give an accurate specification of them.

We will treat Kuhn, then, as – for far the greater part of his career -- a pretty single-minded thinker, who assiduously pursued what look like two different, interrelated, but, it transpires, unequal, objectives, one historical, the other philosophical. The first objective may seem, when it is explained, an utterly innocuous one, and one that has been pretty well achieved. Indeed, Kuhn has turned out to be more successful than he either anticipated or even finally approved of in promoting a much more authentically historical approach to science. But presented with his historical project alone, one might wonder how Kuhn's work could possibly have drawn the attention that it has. His first objective was to do history of science properly – to help professionalise the history of science. This objective is in immediate service of providing corrections to the history of scientific ideas. Kuhn's other two substantial books (apart from The Structure) each sought to reassess the achievement of a crucial figure in the development of the natural sciences – the eponymous Copernicus in The Copernican Revolution and Max Planck, a candidate for the title ‘founder of quantum physics’ - in Black-Body Theory and the Quantum Discontinuity 1894-1912. However, it was what Kuhn made (in more philosophical terms) of his historical work that gained him his reputation.

Amongst Kuhn’s historical studies The Copernican Revolution could be described as a popular work, but the studies of the quantum revolution in The Black-Body Problem and in a paper (with John Heilbron) on Niels Bohr’s model of the atom are relentlessly technical, no easy read for those without some serious mathematics and physics . Even though these studies carry Kuhn’s general message, they would never have gained him anything like the universal recognition that the racy and readable Structure so quickly won.

The professionalisation of history of science was really meant to provide a platform for Kuhn's major interest, which was to reconstruct the philosophy of science. The historical element was essential to this, but not just because it would ensure the correct attribution of scientific achievements. It would not produce a generalised account of what the course of scientific thought has historically been, but would describe how scientists come to change their ideas, in a way that directly conflicted with the ideas of then-contemporary American philosophy of science that Kuhn inherited The received philosophy of science's central ideas about scientific change were basically mistaken . Kuhn’s ‘case studies’ were meant to show that both this understanding of the facts of succession of scientific ideas themselves and of the ways in which ideas were changed were both misrepresented.

Of Kuhn's two interrelated objectives, the historical is the logically (or at least, strategically and pedagogically) prior one.

Clearly, the proposal is only worth making if it is expected that placing the history of the science in the hands of historians will make a considerable and pervasive difference to the way in which the historical story is told. One of the main ways in which the history of science was distorted was that the nature of changes in specific scientific ideas were being misrepresented. Looking backward, and viewing the thought of past scientists from the vantage point of the present, historians can be handicapped in understanding the actual nature of that thought. The big problem which faced the history of science was much like that which faces anthropology, that of understanding ways of thought which are very different to the researcher's own. Just as anthropologists have painfully learned, the way to solve the problem was to be careful to keep alien thoughts in their proper context, not to isolate them from the very considerations that made them intelligible and plausible to those who accepted and live by them. For historical purposes, the important thing is not the relationship between the thought of some earlier scientist and contemporary scientific ideas. What matters is the relationship between the thought of that scientist and the ideas/procedures/possibilities available to the scientist in his or her own times, that he or she could possibly know about, such as the thought of their scientific contemporaries, the experimental data then available etc. as well as the wider scientific and cultural traditions surrounding and perhaps influential upon the scientist.

Kuhn found it annoying that the thought of scientific predecessors would, viewed with hindsight, but in isolation from the historical context in which it arose, be made out as inexplicably strange or confused . It would be asked: How could anyone 'in their right mind' possibly advance such strange and implausible ideas? How could earlier scientists [or ‘primitive people’ in the anthropological case] fail to see what is so obvious, namely that they are mistaken? The only explanation would seem to be that they are less intelligent than we are: naïve, confused or incompetent? Or, ‘at best’, it would be asked how, given that they were not all wrong, and did get part way toward where we are now, why could they not see where their ideas inevitably lead? Again, What stopped them from seeing what is now entirely obvious to us?

Kuhn thought virtually all such judgements quite unjust or inappropriate, and expected that re-examination of those thoughts in their full historical context would almost certainly revise these negative evaluations. That one might get a better understanding of the development of scientific thought by considering the different periods of science in their own right, rather than as mere stepping stones to our present position, seems a modest, and entirely plausible suggestion. If true, though, it could again have far reaching implications, rewriting the history of scientific ideas themselves, and making considerable substantive difference to the way in which the relationship between the changing ideas of science would be understood.

What do we mean when we say that the disapproved kinds of history of science suffered from ‘benefit’ of hindsight’? Well, a related fault of which 'traditional' history of science stood accused -- by Kuhn -- was that of delivering 'Whig history.' This is a derogatory expression, used to condemn complacency in the writing of history. 'Whig' historians view history as though their own present position and convictions were the very fulfilment of history, the outcome toward which previous periods have been inevitably leading. On this basis, the interest in previous periods is in the degree to which they involved progress in the 'right' direction, namely toward the present state of things . Kuhn’s reaction against this (and much more broadly than in the history of science) was to avoid the projection of present preoccupations into the past, to seek out much more scrupulously the contemporary understanding of the people of the period.

In fact, the attack on ‘Whig history’ is in part a questioning of what had been a ubiquitous notion, that of ‘progress’. If the notion of progress was not to be rejected altogether – and Kuhn never disputed that there was progress in science -- then what was to be abandoned was the idea of 'progress' as the inherent, inexorable and pre-destined movement of history’s own course (Call this ‘P’). It is quite a natural feature of science education, directed as it is toward instilling up-to-date science in its trainees, to look into the past mainly in order to see how the science got here from there. This history is an aid to education in current scientific ideas, rather than any end in itself. It might be acceptable as a part of basic scientific training, but cannot provide a satisfactory approach to real historical studies. The eschewal of Whig history correctively emphasised, then, the contingent and non-special nature of the present, making it merely the latest date in history, not its fulfilment or finale. The rejection of ‘P’- of progress as involving the idea of movement to 'higher' or 'better' outcomes, and the complacent assumptions that one’s own views were not only pre-destined but prove one’s intellectual superiority over one’s predecessors - is a rejection of only one idea of what progress might be.

That Kuhn denies there is progress in these terms does not mean that he denies all actuality or prospect of progress, and one aspect of Kuhn's continuing struggle was to make clear the sense in which he did think that there was progress

In Kuhn's view

• External history [history of the cultural and social circumstances that obtain in the wider environment of the working scientist] was in service of internal history [the recovering of the course of the development of scientific ideas]
• Internal history remained in service of an understanding of the past from the point of view of the present, providing a proper picture of how and why one scientific idea succeeded another.

Kuhn thought that the first problem confronting the history of science was correctly to identify what it is that is to be to be explained). It was here that the deficiencies of 'Whig history' were most critical, for they resulted in mistaken accounts of past scientific work. Before one could explain how changes took place in science, one needed to identify those changes properly. The 'internal history' needed to be done the right way, divesting it of retrospectively induced distortions. 'Internal history' was also the main part of the explanation , for the central task is to explain how, primarily through scientific work and reasoning radically new scientific ideas are proposed , to trace – as far as possible – the step by step transition from one set of ideas to the next. Thus, the way these things are worked out in the scientific documentation provides the main focus of study. An understanding of the transition as a scientific transition must come first, and only after that can 'external' history make its contribution, and show how, if they did, ‘external’, non-scientific conceptions and interests [such as, for example, religious, political or commercial ones] might enter the scientific process. The influence of an area of science and of the wider society upon each other is certainly a bona fide topic of inquiry, but, for Kuhn, the influence of the latter upon changes in the nature of the former can be understood only if the changes in the nature of science itself have first been properly understood. Ensuring this is the task of 'internal history.'

Thus, in BB – which is entirely an exercise in ‘internal history’ Kuhn argued that the origin of the idea of a quantum discontinuity – a cornerstone of contemporary physics – was quite misunderstood by the orthodox historical accounts. These located the break between classical and quantum physics more than half a decade earlier than was correct – and credited the achievement to the wrong man, Max Planck, rather than its true originator, Albert Einstein.

Clearly, these ‘main ideas’ of Kuhn’s about the history of science, as so far presented, do not show how his work could ever be seen as a source of near-apocalyptic intellectual menace. –

Kuhn was, however, undoubtedly captivated by the philosophy of science and thought that proper history of science would implicate profound changes in the philosophy of science. Kuhn’s greatest importance and influence arises not from his campaign for the reformation of history of science, but from his attempt to spell out the philosophical importance of the historical reformation. For philosophy of science, Kuhn might indeed spell ‘apocalypse’.

The history of science, as Kuhn conceived it, is and is bound to remain an esoteric pursuit. Insofar as it is involved in close examination of the history of highly technical scientific thought, then it will not be easily – if at all – understood by those without technical competence. What it shows will often be of little interest or consequence to most people, even contemporary scientists in the area concerned. What difference could it make to most people to know that the break between classical and quantum physics occurred after 1906 not 1900 or that it was Albert Einstein who introduced the modern idea of the quantum, whilst Max Planck only introduced the term? B

Kuhn thought that even the early work on the programme of historical investigation that he supported justified claiming that there was a need to change the general (even popular) image of science. It was Kuhn’s critique of this received ‘image of science’ (i.e. the picture of science dominant in the philosophy of science in the period around and shortly after World War II) which ensured that his work became so controversial. We repeat, the case for reconstructing the history of science was, for Kuhn himself, only a ‘pretext’ [though by no means a ‘mere’ or trivial one] for demanding a thorough revision of the image of [specifically] scientific change, i.e. for attacking the (received) philosophy of science.

That history of science was a stalking horse for philosophy of science in Kuhn’s thought does not explain, however, why the implications of what is surely an otherwise reasonably innocuous programme for work on the history of science should carry such revisionary implications for philosophy of science. In a sense, Kuhn’s one objective in the philosophy of science can be said to be bringing it much more into line with evidence about what scientists actually do. Kuhn’s pursuit of this policy has, we think, the effect of altering the questions that would be asked by the philosophy of science.

It did not mean, for Kuhn, that historical questions should displace philosophical ones. It meant, rather, that the idea of what was philosophically problematic should be drastically changed. It is this that explains some of the confusion which surrounds Kuhn’s arguments, and which confuses those who persist in approaching Kuhn in terms of the more traditional philosophy of science standpoints.

Kuhn’s single-mindedness can be seen, we believe, as consisting in the development, throughout his major work including the case studies, of just one main theme: that the received image of scientific development is of development by logically continuous accumulation, and that this is a systematically-misleading image. Insensitivity to the intellectual and ‘cultural’ differences between different periods in the history of science results in failure to appreciate that differences between successive periods may be much deeper than -- to the cursory inspection -- they appear, and that the transition between one phase of scientific work and its immediate successor is not so much continuing further along the same line of thought, but going off in a different direction. Thus, the cogency of the historical point remains – that there is substantial and significant misrepresentation of the actual course of scientific work, partly out of the desire to get it to conform to the image that the philosophy of science encouraged. This misrepresentation is significant for the things which matter in philosophy of science, to wit, the status of science as knowledge and its standing as the very paradigm of rationality in (or indeed as the basis for the very rationality of) our general culture. Insofar as the philosophy of science draws upon the history of science, and forms its picture of the bona fides and rationality of science on the basis of that history, then if the history is seriously misguided, so too will be the philosophy’ modelled’ on it .

If we treat Kuhn’s work as focussed single-mindedly upon devastating the view of science as development-by [smooth, continuous]-accumulation, no serious injustice will be done to the range and variety of his writings, for the view of development-by-accumulation is ramified, and his criticism of it necessarily many sided. But it will facilitate our account of Kuhn’s confrontation with the received image of development-by-accumulation if it is constantly borne in mind that Kuhn’s attack is upon views in the philosophy of science, and not upon science itself. It is to the profit of various positions in philosophy (though usually to the disadvantage of reasoned discussion with them) to identify themselves with science (to wrap themselves in its flag, so to speak), to the extent that they can make it seem that rejection of their views will diminish the standing of science itself. Thus, if one argues against their view of what makes science rational one is likely to be accused of denying that science is rational at all. If one rejects their view of what comprises or ensures scientific progress, that will be treated as being just the same as denying that science makes progress at all. Similarly, questioning their idea of the nature of scientific knowledge will be responded to as a ‘radical scepticism’ casting doubt on whether science can ever attain true knowledge.

Those with more traditional views in the philosophy of science are perhaps rather prone to over-reaction -some, certainly, are very easily outraged. However, there is no reason to be intimidated by their often fierce insistence that science will lose its credibility if their views are rejected.

Kuhn argues: if we go along with the received conception of science as development by accumulation, then we will subscribe to the received conceptions of rationality, scientific progress, the growth of knowledge and of the requirements for knowledge of natural reality even though these notions involve serious misconceptions about what scientific change has really been like.

Kuhn’s arguments tell not against the achievements of science, nor against its prospects for rationality, progress, growth and the expansion of our knowledge. They tell only against one rendition of these concepts, the (received, in practice ahistorical, and mostly formalistic) philosophy of science.

What then is sensational about Kuhn? Is he actually proposing any ‘sensational’ theses or theories or claims at all? Or is what (if anything) is ‘revolutionary’ in his approach and its implications really in quite another register?

First, though: what exactly is the received image that Kuhn proposes should be given up? We have (following Suppes, 1977) dubbed it ‘the received view’. (We are not trying to give an account of this received view as it would perhaps be expounded by its supporters, but rather an account of the enemy as perceived by Kuhn. But we do believe that the received view accurately reflects substantial elements of the position in the philosophy of science of Logical Positivism and its successors, and also some important elements of the views of Falsificationists and of ‘ Realists’. ‘The received view’ is probably what many lay people, especially those informed chiefly by ‘popular science’ or popular philosophy of science, understand still as science-in-itself.)

As is plain, this reviewed view supposes that science develops by accumulation. The trouble with such a characterisation is, though, that it is neither clear nor specific, and needs to be spelled out a bit. Kuhn’s claim is that science does not develop only by accumulation, that it does not develop by constant or linear or logically smooth accumulation . If this is what Kuhn is arguing then the perceived opposition to him must be maintaining not merely that science develops by accumulation, but that science develops by constant, continuing, linear accumulation. We need to go further into what ‘development by accumulation’ means – we need to explore the views of Kuhn’s perceived opponents further.

Here is Ian Hacking on the matter. He picks upon Carnap as a representative Verificationist, and then ‘opposes’ his views to Popper’s, in a clear manner and one quite sufficient for our present purposes:

" Carnap thought that meanings and a theory of language matter to the philosophy of science. Popper despised them as scholastic. Carnap favoured verification to distinguish science from non-science. Popper urged falsification. Carnap tried to explicate good reason in terms of a theory of confirmation; Popper held that rationality consists in method. Carnap thought that knowledge has foundations; Popper urged that there are no foundations and that all our knowledge is fallible. Carnap believed in induction; Popper held that there is no logic except deduction.

All this makes it look as though there were no standard ‘image’ of science [‘received view’] in the decade before Kuhn wrote. On the contrary, whenever we find two philosophers who line up exactly opposite on a series of half a dozen points, we know that in fact they agree about almost everything else. If two people genuinely disagreed about great issues, they would not find enough common ground to dispute specifics one by one’’ . .

Carnap and Popper share a basic image of science, the one rejected by Kuhn.

What then is the common ground between the two? Hacking again:

"Both think there is a pretty sharp distinction between observation and theory. Both think that the growth of knowledge is by and large cumulative. Popper may be on the lookout for refutations, but he thinks of science as…tending towards the one true theory of the universe. Both think that science has a pretty tight deductive structure. Both held that scientific terminology is or ought to be rather precise. Both believed in the unity of science…

Both agreed that there is a fundamental difference between the context of justification and the context of discovery. …in the case of a discovery, historians…sociologists or psychologists will ask a battery of questions: Who made the discovery? When? Was it a lucky guess, an idea filched from a rival, or the pay-off for 20 years of ceaseless toil?… These are all questions about the context of discovery.

Now consider the intellectual end-product: an hypothesis, theory or belief. Is it reasonable, supported by the evidence, confirmed by experiment, corroborated by stringent testing? These are questions about justification… Philosophers care about justification, logic, reason, soundness, methodology. The historical circumstances of discovery, the psychological quirks, the social interactions… are no professional concern of Popper or Carnap. …[T]he philosophies of Carnap and Popper are timeless: outside time, outside history."

Kuhn can be seen as disagreeing with the entirety of the Popper-Carnap common ground. His antagonism to the received view is manifest in the list of denials that Hacking attributes to Kuhn:

"There is no sharp distinction between observation and theory.

Science is not cumulative.

A live science does not have a tight deductive structure.

Living scientific concepts are not particularly precise.

Methodological unity of science is false: there are lots of disconnected tools used for various kinds of inquiry.

The sciences themselves are disunited. They are composed of a large number of only loosely overlapping little disciplines many of which in the course of time cannot even comprehend each other…

The context of justification cannot be separated from the context of discovery.

Science is in time, and is essentially historical ."

One way of construing the development of natural science would be to see science as just the steady addition of new scientific results to a vast stockpiling of results. This is certainly a view that Kuhn eschews, since it doesn’t take much thought to appreciate that the development of science does not consist in just producing new findings to put together with the old, stacking them up in no particular order. Obviously, an important part of science is putting those findings into an organised form, connecting them together through systems of theory for example. Many of the major achievements in science have been other than producing empirical results. They have involved contriving new ways of thinking about scientific problems and new ways of investigating phenomena. Hence, if science does develop it does not do so just by further addition but also by re-arrangement and perhaps by subtraction. More important still, in the development of science, especially in respect of the formation of major theories, new theories displace old ones. Everyone knows that Einstein’s theories have in some sense displaced Newton’s, but only in the sense, perhaps, that Newton’s theory has been swallowed up into Einstein’s. Newton’s theory has only disappeared as a distinct entity for it is now subsumed in Einstein’s There are significant changes in science, even great ‘revolutions’, but these can – on the views that Kuhn will contest -- be seen not as fundamental changes in the nature of scientific thought but as ‘great leaps forward’ (to borrow another political metaphor) which carry science further in the same general direction. This is what is meant by the idea of development as ‘linear’ -- that the advance of science does come about through substantial shifts in ways of thinking, but ones which carry the same line of thought further in a logically continuous direction, taking science ever closer to its final, or ultimate, objective.

This promises to give one a way of seeing scientific change as truly a case of development.

So much has this been taken for granted, that we have scarcely even explicitly mentioned it, yet – the idea that change in science is (overwhelmingly) some form of improvement (i.e. development, in a positive sense). Science gets better, science just knows more. In some sense, this idea surely demands to be accepted. Does science, though, just go on adding more and more findings to a stockpile which is capable of expanding endlessly? Or is there some ‘end’ or ‘aim’ for science? Is science’s line of development directed toward some terminus at which point it might be said to have finally and fully achieved its objective? One positive answer often given to this question is that science is indeed advancing on an objective, which is that science keeps moving toward the complete and final truth, getting ever closer, if not (as Karl Popper was apt to think) ever actually getting there . Over time it does approximate ever more closely to this final target. The succeeding ideas are, then, each measured against the same target, and the latest ideas are accepted because they are nearer to, or have even hit, that target.

Thus arises another element that can be involved in a conception of the continuity of science. The move from one stage of a science to another can be considered as a rational progress. There is – perhaps -- a constancy throughout in the development of science in that the means which scientists use to decide whether to take a particular next step or not involve applying the same general criteria. The decision as to whether or not to take a particular step in science is presumably one of the premier instances of the application of reason! Scientists do not decide whether to adopt a new idea or to accept a new result on the basis of violent armed (or even unarmed) physical struggle, or drawing lots, or conducting opinion polls. They try to decide by thinking through -- by logically reasoning and arguing about-- the differences between the old and the new . But a strong influence in philosophy is the idea that the exercise of reason, if done properly, is done in accord with rules for its direction. There must be very general considerations which comprise the proper application of reason, and which can be spelled out. This is much the same as the idea that knowledge is a product of method, and that if science is the very paradigm of knowledge, the unparalleled example of the systematic accumulation of knowledge, then there must be some general ‘scientific method’ that is followed in all cases in which science is successful. And if there is such a method then, of course, once identified it provides a sure fire method of getting the right results, of ensuring that knowledge is what obtains, and it can be administered in all those areas in which it has not yet found application. Further, if the thinking is done ‘rationally’ all rational beings will be compelled to accept its conclusions: this is the ‘universalism’ which is often attributed to scientific method.

If science is indeed a progress of better over worse, then it ought to be possible to spell out the scientific method as a kind of ‘algorithm’. That is, a set of rules which would specify how, confronted with an established scientific idea and an upstart idea, one should decide between them, whether to stick with the old or side with the new. The rules would dictate one’s choice, specifying which of the two ideas was closer to the truth Thus, the results of the algorithmic selection of one scientific idea over another would be ‘objective’ in the sense of being indisputably correct. No rational person could dissent from these decisions.

The above has been a very simplified account of some of the main ways in which the idea of development-by-accumulation is cashed out, some of the forms that the supposed continuity can be said to take. The positions included in this compact package are obviously often more complicated and sophisticated than this bare summation can depict. We are only trying to suggest why Kuhn’s concentration on critiquing the notion of development-by-accumulation could wreak such havoc in the philosophy of science, for it could – and it does – call all of these contentions into question. He claims that these are not – that they cannot be – descriptions of the ways in which scientists actually choose whether to move on or stay put in their science. Indeed, it is significantly misleading, if not entirely inaccurate, even to say that scientists are involved in choosing between one big scientific idea and another.

An important role which many see for the ‘received view’ is that it provides us with assurance. It provides us with assurance that our contemporary science truly is what it appears to be, namely the best available account of what natural reality is like. It assures us then that we are right to repose in it the very high level of trust that we (or, at least, very many of us) do. There is no equivalent or better account of natural reality to be found in either previous historical periods or in any of the other societies currently in existence. The ‘received view’ apparently gives us such assurance for it tells us both that

1. there is progress in science itself, with the result that the latest science is the best science- and, of course, has advanced over and improved upon prior science, and upon all pre-scientific modes of thought and
2. since natural reality has a determinate character, then any characterisation which truly says as science does how natural reality is can have no competitor. Natural reality can be one way only. Hence, given that our natural science tells us how natural reality is, our science can have no rival.

These reassurances are deemed very important. Given the great weight which we place upon science in our practical existence and in the formation of our self-conception, they justify us in thinking not just of science as advanced, but of ourselves as an advanced and enlightened people (not because we are ourselves active contributors to science, but because we are the – fortunate- inhabitants of a culture pervaded by and properly respectful of the scientific spirit). Naturally, for anyone holding such views, it is incumbent upon them to speak out on behalf of science in the face of any denial of science’s premier position – they think that far reaching and deleterious consequences follow on its demotion.

These latter convictions have lately felt themselves much embattled, faced with a rising tide of ‘irrationalism’ which threatens both science and our civilisation. Those who would defend them do so perhaps the more vigorously because they see them so seriously threatened.

Scepticism about these very convictions is an important part of so-called ‘postmodernism’, and for those who resist it the rise of postmodernism is a major manifestation of the resurgence of the feared ‘irrationalism’. ‘Irrationalism’ is a force to be resisted all the more because its previous prominent manifestations have allegedly been the totalitarian extremisms of the Nazi Germany and Soviet Communism. Thomas Kuhn is readily and regularly blamed for his major role in this (supposed) contemporary irrationalist resurgence and is seen to represent a serious political danger.

Kuhn is unquestionably telling us that science is not what we have believed it to be ( insofar as we have believed what we have been told by philosophy of science and its popularisations). If we accepted that science is the sole and unqualified paradigm of rationality, and that its results are uniquely successful in telling us about natural reality , then the easiest conclusions to draw would be that Kuhn is undercutting this image by promoting its very opposite. In that case, Kuhn must be telling us either

• that science does not tell us about the nature of natural reality at all or
• that science is not uniquely successful in telling us about natural reality, and that there are other, perhaps very different, ways of talking about natural reality which are (or are capable of being) at least as successful as our natural science.

To those holding the received view such suggestions seem not merely dangerous, but preposterous, which adds to the accusatory and intemperate tone often taken toward Kuhn. He is blamed for taking away the supports of our faith in science (and ultimately in our superior, enlightened way of life ) without putting anything in their place. And it is for precisely this reason that some of his more ‘radical’ postmodernist ‘fans’ think that he is worth following.

What of the question of ‘foundationalism’ in philosophy? Is Kuhn an ‘anti-foundationalist’? And if he is, could that too make him (appear to be) dangerous? ‘Anti-foundationalism’ is another buzz-word of contemporary thought, identifying opposition to the classic notion that knowledge must be ‘founded’ upon a basis of absolute certainty. That view is now in relatively bad repute, and Kuhn is not alone or even particularly distinctive amongst the distinguished philosophers of science in eschewing it (for example, Popper too rejects foundationalism). He rejects what had been the traditional, empiricist, source of certainty, namely our direct access to our sensory experiences which provide, after all, the most immediate and uncontaminated contact with the external world. In the empiricist philosophy of science, this idea took the form of a distinction between two languages, that made up of ‘theoretical terms’ and another consisting of ‘observation terms.’ (See SSR 113-129) The latter would speak directly of our sensory experiences, and should, therefore, characterise those experiences quite independently of theoretical terms and in ways which should be the same from one observer to another. This was a putative basis for the rationality and objectivity of scientific choices. After all, if the observation language provided a constant in the face of the diversity – and rivalry – of scientific theories, it would then be something by means of which those rival theories could be unequivocally compared. One could tell whether or not what one theory said did, as its rival did not, correspond with what, in the observation language, could be reported as actually and certainly observed to be the case. Kuhn – though not original in doing so [ e.g. Hanson, 1958.]– questioned the value of the distinction between observational and theoretical terms , denying that there are any theory neutral - reports of what is observed Kuhn eschews the observation language/theory language distinction and does indeed say that science never involves direct comparison of a theory with nature itself. Is this too a ‘dangerous’ view to have, risking perhaps the thought that our world is only a world because it is a world-for-us, a world dependent in some way upon being perceived? That would be philosophical Idealism.

On these matters Kuhn is for sure anti-foundationalist . And in another way too. This other sense is one in which philosophy often strives to provide science with an external foundation, with an independent rational justification. Those who develop the received view think that they are engaged in providing a philosophical foundation for natural science, are securing, proving, the claims of science to be a rational, objective and cumulative pursuit. Kuhn effectively denies that science can have such external philosophical justification, casting doubt on whether there can be any external basis – philosophical or otherwise - for judging the success or otherwise of science. Kuhn’s line in a way disposes with the idea that the philosophy of science is important, that it can either justify or second-guess scientific results. No wonder many philosophers of science are often enraged .

Kuhn does then dissent, and in almost every particular, from the ‘received view’ of science, but he does so not on the basis of simply negating claims that science is rational, cumulative, or gives us knowledge of natural reality. He does so, rather, on the basis of challenging the terms of his opponent’s arguments, refusing to conceive the conditions for rationality, cumulation and knowledge in the sciences in the way the received view has done. If Kuhn is right, that the historical facts about scientific change, when viewed aright, just do not conform with the ‘image’ projected by the received view, then it is not necessary to conclude that science is irrational but is possible to argue that to the (great) extent that science is rational, but in a wa y very different to what the received view can conceive.

Thus, Kuhn has been most prominently criticised – and sometimes equally praised - for

• irrationalism
• relativism and
• Idealism

and most of the opposition to his work has been premised on the assumption he is guilty of one or more of these offences. However, much of this is a waste of time, for Kuhn was none of the above, except perhaps in the most modest and reasonable fashion . Kuhn is only seriously open to construal as a Relativist, irrationalist or idealist if one supposes that must take the the received view as one’s starting point, and then construes Kuhn’s writings as if they were designed to satisfy the requirements of the received view. But why they should need to is what is up for argument.

Kuhn’s account of The Structure of Scientific Revolutions contains a sketch of how to think about the general manner in which the natural sciences in the West developed. Before turning to give rather more detail in our chapter-by-chapter exegesis of SSR, let us briefly outline that ‘schematic’.

Disciplines that have ended up amongst the developed or mature sciences that we now have - and there is no necessity that any discipline that comes into existence will end up included in that collection -- are, in their early life as disciplines, made up of thinkers and investigators whose work is only tenuously, and often competitively, linked to each other’s. Often, these thinkers divide into rival sub-groupings (or ‘schools’) that are rival bidders in attempts to elect themselves as the group which defines the whole discipline for everyone else, but they are ineffectual, and no one of them is able to mark itself out as sufficiently distinctive and successful as to attract more than a modest proportion of those working in the area. The work visibly fails to make anything the participants can recognise as real progress, frequently with the resulting feeling that it is going about things in basically the wrong way, and that what is needed is a thorough rethink of the whole way the discipline might be done. Thus, whilst empirical work may get done, much of what goes on involves disputing the fundamentals, the whole approach of the discipline,and as long as those are constantly being debated then work is not going to move very far from first base.

UNIFICATION. Out of this factional strife within the discipline and amongst schools, there may appear some achievement which is sufficiently attractive to a large proportion of the participants in the field that one can begin to talk about the discipline as being unified. (Fundamentally, such a novel achievement is what Kuhn is talking about when he uses the word ‘paradigm’, probably the most famous of all his expressions – more on this in the next chapter.) This does not mean that everyone in the field has gone over to this new position, but that the balance has shifted, and that many of those in the field can conduct themselves on the basis that they can assume agreement on fundamentals with most of their colleagues, and they can give up either reiterating or arguing about those fundamentals. There may remain a minority who would still contest the fundamentals, but these individuals will eventually be ‘frozen out’ by the others. They will not necessarily be brought to stop their activities, but they will just be disregarded. Those who have opted in to the now prevailing agreement will take each other seriously, but cease to take any further interest in the work of those who refuse to sign up. Where the discipline previously may have been open to all who possess some scholarship in the field, the development of fundamental agreement brings with it a more exclusive attitude, and the development of its organisation in a more professional direction i.e. one which has an internal system of control, which includes a monopoly over the training which is made essential to recognition as a bona fide practitioner in the field.

Before the development of this extensive agreement on fundamentals, the discipline could be described as being a discipline without a ‘paradigm’.

Once a field has developed a paradigm in the above sense, then the consequences of forming settled fundamentals will come into play. Work within the field can start to build on those fundamentals, and still other work will build upon that. There will be a (relatively) clear and standard sense of what an achievement in the field can look like, and a (relatively) coherent body of knowledge articulated, to which the results of appropriately conducted studies will count as additions. Thus knowledge-by-accumulation becomes possible – and this, when it happens, is surely a fine thing.

A paradigm, facilitating such cumulation, will not however remain in place forever. Much, but not all, of what goes on in the discipline will be incorporated into the paradigm, but there will always be things which do not comfortably fit within it - results which do not conform to what the principles and orthodox practices of the science would lead one to expect. At some point, the incongruity between those results and their paradigm will likely encourage doubt as to whether there is not some flaw in the fundamentals, and whether they need - in whole or major part - to be rethought. If those incongruities - call them anomalies - that do not comfortably conform to the paradigm are seen as raising serious questions about the continuing viability of those fundamentals, then the discipline is likely to exhibit again some of the behaviour which it showed in the period before the fundamentals were settled, and to involve, again, internal division . However, the extent to which this happens will now be more limited than in the days before there was agreement, for even though those in the field are prepared to wonder about, and even re-examine those fundamentals, they will not abandon them until they see some alternative fundamentals that have the prospect of replacing those now in question. They do not regress to the stage in which the discipline collapses back into rival schools, but move into a period of ‘revolution’ in which there will be division between those who want to stick with the old fundamentals, and those who want to follow the new way. From their competition a new and prevailing consensus will emerge - or a group will break off and form a new discipline around the new conception of the fundamentals - and a new and different paradigm will come to dominate - as before, marginalising those who do not sign up to it. After perhaps a transitional period of some disorganisation – perhaps even of revolutionary struggle for control of it - the discipline will reform itself in a reorganised way. Much of what the discipline had achieved before will be rethought, rearranged or forgotten, but, more importantly, the discipline develops new possibilities that could not have been imagined or taken seriously in the discipline as previously constituted,. Now, on the basis of radically revised fundamentals, a new phase of building is possible (unless and until, of course, the possibility of serious doubt about the viability of the latest set of fundamentals arises).

Here is Hacking’s account of the situation, after a revolution in a science: "[Any] new theory … is born refuted. A new generation of workers gets down to its anomalies. There is a new normal science. Off we go again, puzzle-solving, making applications, articulating mathematics, elaborating experimental phenomena, measuring." And as Hacking observes, and as we have noted, the process of change in fundamentals will in all likelihood sometime begin again: "Kuhn invites the idea that every normal science has the seeds of its own destruction." (p.9) For if a paradigmatic theory is born refuted, as Kuhn thinks, then there will always be room for working on it – and always scope for wanting or ‘needing’ to overthrow it.

This pattern, which Kuhn (and Hacking) describe, of ‘dialectical movement’ in the natural science disciplines has among other things brought about a broader pattern in which there is long term advance for some disciplines, and a general expansion in the range of disciplines, as well as an increased level of specialisation within and amongst them. The possibility of ‘long term advance’ is present in the business of paradigm succession, for though the change of paradigm results in rejection of the previous paradigm as such, this does not involve completely throwing out all its achievements, for many are reincorporated within the new paradigm, albeit typically in radically reconsidered terms (as we shall make clear later, this is a central source of the true radicalism of Kuhn’s philosophical account of science). The new paradigm achieves its acclaim by raising the level of scientific performance, by being acknowledged as generating some, and promising many more, achievements that do not merely equal but surpass (in terms not merely of finding out new things, but of doing so in more technically demanding ways) those of the previous paradigm. Within the paradigm, too, of course, there is the capacity for advance, with the objective being to work out the paradigm better, and to make its generalities more inclusive, the findings more precise and so on.

In sum, Kuhn provides a historical-cum-sociological sketch/account of the development of natural science which lays the groundwork for his philosophical innovations. Those innovations – as they truly were and are, not as various philosophers and others have caricatured them, missing both their subtlety and the true nature of their philosophically revolutionary character -- are what, above all, we shall endeavour to describe and assess in the pages which follow. We wish to explicate Kuhn’s ‘schematic’, and show thereby both its reasonableness and its revolutionary effects.

PART I

EXPOSITION

INTRODUCTION :

In this part of the book we go in, mainly, for exposition of Kuhn’s first three major works, The Copernican Revolution (CR), The Structure of Scientific Revolutions(SSR), and Black-body Theory and the Quantum Discontinuity,1894-1912 (BB). We do not follow the historical sequences of their production and publication, but begin with SSR, next the Copernican case, and then the quantum revolution. It seems that hardly anyone, even authors giving lengthy accounts of Kuhn’s work, reads Kuhn’s historical studies in conjunction with SSR, and this is, we think, one reason why the understanding of Kuhn is characteristically so poor. SSR is packed with historical examples, it is true, but these are brief and used to illustrate specific points of argument, and they do not give sufficient guidance to the difference that Kuhn’s ideas were meant to make to the history of science. The failure to understand how the ideas in SSR cash out in the historical studies almost invariably signals a failure to understand both. Exposition of Kuhn’s main case studies is, then, in practice, an essential to explaining what it is that Kuhn is talking about in SSR. Thus, we set out the main lines of [relatively] abstract argument first as this will make it easier to draw out the connections with Kuhn’s general approach. This will, we hope, also make it easier to see that Kuhn’s arguments cannot be so absurd as they are often accused of being. Much or all of what Kuhn says about the Copernican and quantum cases may [ as a matter of historical claim] be partly or even wholly false but it will be seen that the kinds of claims he makes are intelligible enough, and propose nothing that is bizarre or fantastical. Kuhn’s claims are, it is worth remembering throughout, claims about the working practices of natural scientists and only about that.

CHAPTER TWO:

Our presentation of SSR will itself be in two parts. In the first we explicate some of the main elements of Kuhn’s account of the dynamics of natural science in the West, paying particular attention to those which have been provocative or have spawned confusion. In the second part, we introduce some of the philosophical ‘matters arising’ from that sketch of scientific change. (These ‘matters arising’ we will then deal with more critically in Part Two of the book.) We structure our account by roughly correlating it with sections in SSR itself. (We deal with Kuhn’s amendments to the main body of SSR, (including the important post-script added to the revised edition of 1969) later in our book.) In the first part of the chapter we deal with Kuhn’s central – and, we think, fairly straightforward – concepts for depicting the main kind of changes that take place in natural science: paradigm, normal science, and scientific revolution provide our key words. In the later part of the chapter, we deal with what are ostensibly the more problematical parts of Kuhn’s case, in which he introduces some [initially at least] very strange sounding ideas: those of ‘world changes’, ‘phenomenal worlds’, ‘incommensurability’, not to mention his rejection of the idea of ‘a fixed nature.’ These elements are all, as will be seen, interconnected. We will make a first attempt to show that these ideas are not necessarily as strange as they might seem, although that is a long way from maintaining that they are entirely free of difficulties. Whether the difficulties they involve are such as to basically invalidate Kuhn’s approach is dealt with in the following, second half of our book.

If we are right that Kuhn’s image of science is as ‘innocuous’ as we say, then how is it possible for his work to carry the extreme implications that are regularly attributed to it? We have already suggested that this is less because of what he says than because of what, in saying what he does, he undermines :- various popular and ingrained and academically ‘respectable’ views about the sciences. He thoroughly undermines not the sciences themselves, but entrenched assumptions about them. And that is not felt, by those he is questioning, challenging, subverting, to be innocuous.

But what does he actually say? And what does he mean by it?

His central platform is set out in The Structure of Scientific Revolutions . With some comparatively minor modifications, this is the one to which he adhered in the rest of the work published in his lifetime.

In the Preface to SSR, Kuhn writes the following autobiographical note, which we take to be absolutely central and essential to understanding his project:

Thus, the difference so important to Kuhn’s thought is one which he first notes in connection with contemporary work and the division between natural and social sciences, and which he realises can be projected back into the history of the natural sciences themselves.

Further down the same page, Kuhn adds that SSR is "an essay rather than the full-scale book my subject will ultimately demand." Kuhn never wrote that book. A first step toward ‘constructing’ it is to gain a thorough base-level understanding of SSR. When that is combined with Kuhn’s later (and earlier) work, a thorough picture of how that book might at least be virtually constructed is possible.

Let us begin by mentioning again the central issue of the succession of major theories in science. Kuhn takes the received view in the philosophy of science to be making certain big claims about what criteria are and should be used to choose one scientific theory over another, and argues that these claims are ‘falsified’ by the historical record. Thus, a main purpose of The Structure of Scientific Revolutions (hereafter, SSR) is to make a case as to how scientists do in fact come to replace one theory with another. This makes it sound as though SSR is one of his historical studies, but it is not that. How, then, is the historical stuff a ‘stalking horse’ for the philosophical; how is this latter aspect dominant in SSR? SSR differs from his properly historical studies for Kuhn is not, here, primarily concerned to detail what, as a matter of historical fact, occurred in various specific episodes in the history of science, but seeks, instead, to say how the events in such episodes should be philosophically construed.

In the Introduction to SSR, Kuhn noted that he was already implicitly or explicitly querying such verities as, for example,

He ends the Introduction with the following, ringing question, a question, which seeks rhetorically to insinuate that the needed transformation of philosophy of science has already begun; "How could history of science fail to be a source of phenomena to which theories about knowledge may legitimately be asked to apply?"

It is important to emphasise that Kuhn is mainly concerned in SSR with the revolutionary transformation(s) of mature sciences, and not with the initial transition from immature science to mature one: the latter is only a preliminary, though important concern, highlighting the difference between a situation in which no real cumulation of knowledge takes place, and one in which it pretty persistently does so, albeit with temporary disruptions.

When Kuhn remarks (10) that ‘normal’ science is what most scientists spend most of their time doing, he is talking about operating within a setting in which there is some kind of ‘agreement on fundamentals already in place, the possession of such agreement on fundamentals being the hallmark of a mature science. In the first instance, the notions of ‘paradigm’ and ‘normal science’ are not meant to express the difference of ‘normal’ science from ‘extraordinary - i.e. revolutionary - science’ but to capture, rather, the difference between sciences that do and do not have this kind of fundamental agreement. . The first contrast that needs to be kept firmly in mind, then – is that between,

(a) , those areas of study in which a good many things are settled, and where there is some kind of broad consensus on the nature, main business and prevailing approaches of the enterprise and

(b) those pursuits in which there is little if anything is settled .

The contrast between physics and sociology over the past three hundred years, is a good example of what Kuhn has in mind here. There have been massive ‘revolutionary’ upheavals in physics but in between these revolutions there has been a stable and extensively shared frame of reference that encompasses the vast majority of physicists.

The same certainly could not be said of sociology, for example, which though two hundred and more years old, is still very far from attaining anything approaching general unification. The notion of ‘paradigm’ is meant, then, to serve in the first instance to illustrate (or constitute) the contrast between a science like post-seventeenth century physics and a would-be science like sociology (SSR 15).

The great difference from the point of view of the practice of science is, for Kuhn, that it is only when there is extensive agreement amongst them, in their suppositions and practice, that scientists can really get on full time with the job of empirical research, rather than being diverted from this by the need to argue about the justification and rationale of what they do the whole of the time.

In this context the notion of ‘paradigm’ functions actually in at least two distinct ways – and in his 1970 Post-Script to SSR, Kuhn accepted that he had not demarcated the two ways as clearly as he might. (He would later adopt ‘disciplinary matrix’ as the equivalent of the usage of ‘paradigm’ to refer to the encompassing and extensively (though not utterly and ubiquitously uniform) body of assumptions and ‘world-view’ shared within a mature discipline. He attempted to restrict the word ‘paradigm’ to the paradigms – exemplary achievements – which founded sciences and around which subsequent revolutions were built (via their function as models of scientific ‘good practice’)).

Kuhn argues that many of the natural sciences started off being more like sociology than like physics after Newton. Sciences often begin with a phase in which they are like the contemporary social sciences, in which there is no fundamental agreement, when people keep on trying to rebuild the science all over again, tearing up existing views of its nature and purpose, and trying to make a completely fresh start with the whole thing. Some of the natural sciences that we now have, and that did start off that way, at some point decisively left this pre- agreement [pre-paradigmatic as it is sometimes called] state behind them, never to return to it. Kuhn recounts the changes in physics’ view of the nature of light which succeeded each other since Newton: light was conceived as corpuscular, then as waves and then as photons. Each was, in its turn, and for a time, the generally accepted view within physics. However, until Newton

So, the contrast is between the period prior to Newton, before the seventeenth century, when there was no general agreement in optics as to the nature of the phenomenon of light, but only different competing views, and the period after Newton when, over time, there were drastic changes in the conception of the nature of light, but, at any one time, there was pretty general agreement on a current view.

Returning to pre-Newtonian physicists: Kuhn holds that these predecessors of physics are rightly considered scientists, and they ‘made significant contributions of the body of concepts, phenomena and techniques from which Newton drew the first nearly uniformly accepted paradigm for physical optics’ (13). But, whilst ‘these men were scientists’, anyone

Not much serious cumulation in such a case, then! Clearly,- the force of the contrast between the ventures with and ventures without paradigms is meant to highlight the difference between

1. the case in which there is, proportionately speaking, relatively little real scientific work [in the sense of empirical investigation] and where that work is not in any real sense cumulative but is, rather, somewhat randomly assorted, being undirected and uncoordinated, with no real integration between results of one study and another, between the work of one scientist and another in the same field, and with no possibility of building further investigations upon established techniques and accepted findings; and
2. the case in which the there is unity and coherence in the investigations carried out, with generally accepted ideas and procedures and where the findings of one study build directly on those made by another.

Development by Accumulation, again.

Kuhn may be a severe critic of the image of development-by-accumulation, but, as we suggested earlier, he does accept to a significant extent the picture of science as involving the stockpiling of knowledge. However he does so on the basis that:

1. the cumulation takes place against the background of a considerable measure of agreement on fundamentals, and on the basis of treating certain past achievements as generally exemplary, as a guide to how to do further work, that provides the framework within which meaningful accumulation is possible, and in which each scientist no longer need be involved in beginning all over again for him or her self; and
2. that the paradigm is seen to have been a crucially missing element from the simple stereotypical (‘received’) picture of development-by-accumulation, but which is in practice taken-for-granted in that picture, as it is in normal scientific work itself .
3. Occasionally paradigms are overthrown and the ‘development by accumulation’ has to begin again, from a different – but ‘upgraded’ - starting point

Whilst a scientific field may develop out of a ‘pre-paradigmatic’ phase, once it has developed a paradigm, thereafter new disciplines and specialisms may spin off from that area of work without themselves having a prior pre-paradigmatic phase.

The emergence of a paradigm shifts the situation within the field, creating a more rigid and exclusionary situation; some people go along with the new paradigm, others die off having been unable even to the end to reconcile themselves to the change . The group associated with the now dominant paradigm is transformed from a group with a shared scholarly interest into a profession with all its appurtenances, with journals, specialist societies and a control over education and qualification in its field. Specialisation’s ‘paraphernalia’ now becomes prestigious Textbooks ,not the working scientist, take on the job of spelling out the science’s fundamentals. Advanced research becomes interesting and accessible only to specialised colleagues and the scientific paper, rather than the book becomes the means of communication within the profession. (20).

The importance of organisation now becomes very clear. It is not as if other philosophers of science had denied the existence of this professionalising tendency of science, they just didn’t seem to be very interested in it. Though even common sense might be assumed to have noticed it since, as the following quotation avers, ‘it has become customary to deplore’ this development, and to regret

The concept of ‘paradigm’

Kuhn’s most famous concept is that of a ‘paradigm’. Not one that he initially coined, it has, however, very much caught on since he made use of it. One hears almost endlessly nowadays of ‘new paradigms’ arising or being needed in every area from Geology or Child Psychology or Management Science to the ‘New Age’. Of course, just this ubiquity should be a cause of concern for us. What concept could it possibly be that could be understood and serve so widely?

Naturally enough, it turns out on closer examination barely to be Kuhn’s concept at all. For the first point that must be borne in mind here is that, even in Kuhn’s own work, the term ‘paradigm’ stands for several very different things.

Let us begin by looking at where Kuhn begins, at the point where the term ‘paradigm’ -- in Kuhn’s particular sense(s) of it -- gets introduced:

In this essay, ‘normal science’ means research firmly based upon one or more past scientific achievements, achievements that some particular scientific community acknowledges for a time as supplying the foundation for its further practice. Today such achievements are recounted...by science textbooks... . Before such books became popular...many of the famous classics of science fulfilled a similar function. ...Ptolemy’s Almagest, Newton’s Principia and Opticks..., Lavoisier’s Chemistry... -- these and many other works ... shared two essential characteristics. Their achievement was sufficiently unprecedented to attract an enduring group away from competing modes of scientific activity. Simultaneously, it was sufficiently open-ended to leave all sorts of problems for the redefined group of practitioners to resolve.

Achievements that share these two characteristics I shall henceforth refer to as ‘paradigms,’ a term that relates closely to ‘normal science’. By choosing it, I mean to suggest that some accepted examples of actual scientific practice -- examples which include law, theory, application, and instrumentation together -- provide models from which spring coherent traditions of scientific research. These are the traditions which the historian describes under such rubrics as ‘Ptolemaic astronomy’ (or ‘copernican’), ‘Aristotelian dynamics’ (or ‘newtonian’), ‘corpuscular optics’ (or ‘wave optics’), and so on. (SSR 10)

It is interesting to note how strongly this, Kuhn’s initial account of paradigms, draws on the ‘literary’ aspect of science -- Kuhn emphasizes the importance of classics (then) and textbooks (now) -- virtually no natural scientists read the classics any more, ( having no need to) in defining their field(s). Textbooks, written works, play a major role in laying down what a paradigmatic scientific achievement is, how it is to be understood, how it is to be taken and used.

Also emphasized is the sharedness and indeed compulsoriness of the paradigmatic. This is already a strong hint that any suggestion that one can choose to have or even to try to have a scientific revolution, to move to another paradigm, is going to be wrong-headed. One is enormously constrained -- by the world in one’s lab ... and by one’s tradition and community.

The two sense of ‘paradigm’:

When Kuhn was clarifying what he meant by paradigm in 1969, he gave the name of ‘disciplinary matrix’ to this first sense of paradigm -- and thereafter he did not use the word ‘paradigm’ in this sense!

This is roughly the second ((2)) of the senses of paradigm, paradigms as exemplary, as acknowledged achievements providing, models to follow, laws to explore and find new versions of in new sets of circumstances, etc. .

This usage of the term ‘paradigm’ is derived originally from the usage of the term in teaching grammar. A paradigm in grammar is quite literally an example which one is supposed to be able -- once one has understood it -- analogically to apply in new circumstances. For (a very simple) example: If one is given the endings to a verb in French (e.g. bouger), and then told that these are the endings to all such verbs -- to all verbs ending in -er -- then one has been given a paradigm for creating such verbs in the first, second and third persons (etc.) oneself in future.

Similarly, Kuhn thought, in science, though with an important proviso:

In the standard application[, in grammar,], the paradigm functions by permitting the replication of examples any one of which could in principle serve to replace it. In a science, on the other hand, a paradigm is rarely an object for replication. Instead, like an accepted judicial decision in the common law, it is an object for further articulation and specification under new or more stringent conditions.

Just as with the disciplinary matrix, so with the exemplars which form a vital part of the former, the extent to which they actually are fully-mutually-understood is, according to Kuhn, uncertain prior to this being tested at a time of crisis. Then it may turn out that they were always to some extent understood differently by different scientists -- but the difference was never an issue, for the relevant cases never arose, the shared understanding and application of the paradigm, of the exemplar, never needed to be in question.

This is perhaps because rules of scientific procedure are rarely explicitly taught, for they are rather absorbed with the paradigms – thus the particular way in which the paradigms are presented and instilled may vary from one educational setting to another, and that variation, in its turn may lead to variable understandings as to how exactly to go on from the paradigm. By hypothesis, being always potentially on the cutting edge of research, it must have unapplied instances easily within reach, and one must be ready for scientists to find that they do not agree quite as much as they thought they did, that when it comes to this new case, they diverge in their judgements of what the right thing to do is [though whether or not this will matter or ever be noticed will depend on circumstances].

Kuhn’s use of the term paradigm can seem quite unsatisfactory in its ambiguity -- though certainly not as unsatisfactory as Margaret Masterman has led people to believe -- but it would help, perhaps, to notice the crudity of the exercises that we are involved in here. Kuhn’s account of the development of science is a pretty gross one. It is no more gross than any other philosopher of science’s account, however, because discussion of this kind will unavoidably be carried on at such a gross level – it will consist of pretty wide ranging and largely and unavoidably unsubstantiated generalisations.

We do not think that Kuhn’s use of the notion of ‘paradigm’ is really meant to set us out on the meticulous ennumeration and classification of the different kinds and degrees of agreement that that there might be within science, across and within disciplines. It is not a sociological term of art. The notion of paradigms is, in the first instance, meant to highlight a very stark contrast, between early stages in the development and later ones, and between the natural sciences [pretty much] and the social ‘sciences’ [pretty much]: in other words, between the pursuits that have some kind of unity, as opposed to those that are in disarray. The ‘disciplinary matrix’ aspect of the term carries the burden of this significance, and points to the more diffuse kind of agreement which unifies such a branch of the sciences. This contrasts with the ‘exemplar’ usage, which highlights the degree to which there is quite specific agreement across the discipline or sub-discipline, the extent to which one piece of work can stand as a guide to good practice, and enable the quite close relations that there can be between one bit of scientific inquiry and another in the same part of the discipline, the way in which studies in the natural sciences can often fit together in ways that studies in the social sciences seldom, if ever, do. At the same time, this should not be overdone: the extent of agreement and disagreement is not to be treated as some absolute, for as is plain, agreement is commonly and unproblematically [outside the world of philosophical fantasy] a matter of more-or-less: if one is involved in a relatively superficial transaction with others, then one might be in full argrgeement with them, but if one goes more fully and deeply into the terms of one’s agreement one may find that the agreement is not quite so close as it seemed, or that there is much in the attempt at further and fuller specification of the agreement to disagree about.

As explained above, the notion of ‘paradigm’ is one which Kuhn was later to concede was employed in The Structure with two distinct uses.

The importance of paradigms (exemplars), in the initial instance, is that they give scientists (real) work to do. The fact that they contribute impressive solutions to existing problems is what makes them deserving of scientists’ attention. , but though the fact that they solve some key problems is crucial to their attractiveness and acceptance another important source of their appeal is that they provide a rich source of new problems. Thus the paradigm is, we might say, a challenge – the challenge is to make it work as well as it can. Consider, for example, the attainments of the quantum physicists in the early part of the twentieth century, or even those of Darwin in the mid-nineteenth century. These contributions have provided problems that have kept large numbers of scientists seriously and purposefully occupied full-time at least into the early part of the twenty first century, though paradigms do not normally last forever, and there assuredly will be further (conceptual) change. And this brings us to the main element of Kuhn’s historical reconstruction, his discussion of the reasons why and the ways in which paradigms regularly displace one another. In SSR Kuhn is emphasising the way in which one paradigm would displace another within the same scientific specialism, but he later came to think that paradigm change often involved the spawning of a breakaway specialism, and that this was the more important fact.

From the point of view of Kuhn’s overall argument, we now reach the crucial point at which Kuhn’s concept of ‘normal science’ is laid out. But we think that, in order to understand why this is a crucial point, it will help to anticipate Kuhn’s ‘complementary’ account of ‘scientific revolutions’, which we shall now do.

The introduction of a new paradigm into a science with a paradigm is characteristically at the expense of that established paradigm (though separation and thereby greater specialisation is another possibility) , and successful installation of the new paradigm is the outcome of controversy. This displacement of one paradigm by another, and the controversy which is usually associated with it is what Kuhn calls a ‘scientific’ revolution.

Scientific revolutions can, when completed¸ often be described as total. The previously dominant paradigm is often [eventually] abandoned altogether, driven out by the replacement paradigm and its advocates. It may take some time [varying from case to case] before the triumph is complete, but victory, when it comes, is in such cases decisive. (These remarks are simply glosses on Kuhn’s oft-repeated remark that scientific revolutions are irreversible.) However, it is equally important to Kuhn to stress that the basis on which such a clear cut outcome is produced are not necessarily ones which are themselves all that clear cut. The received view encourages the idea that scientists switch their loyalties from one scientific idea to another because they have established unequivocally that the new idea is better than the old, that new work decisively refutes prior work. Kuhn does not deny that the switch of a discipline’s loyalties from an older to a newer idea, approach etc. will eventually turn out to be absolute, and looking back it might, therefore, seem obvious to suppose that it was because of the plain, indisputable, advantages of the new paradigm that it was universally preferred. But any such impression, Kuhn argues, may well be entirely false to the historical record, and the choice between the disputed paradigms may have been anything but starkly obvious during the revolution.

Kuhn’s first interest in ‘scientific revolutions’ then is in showing that the decisive results of these controversies may well stem from what were, at the time, less than conclusive reasons: the triumphs were not the ‘knock out’ ones they might later come to seem (the boxing metaphor is ours, not Kuhn’s). Any fair minded historical comparison of the scientific rivals might give something rather closer to an ‘on points’ verdict, and recognise that the decision may have been ‘a damn close run thing’ and akin, even, to a split decision. The fact that the verdict (e.g. in boxing) may involve a ‘split decision’ does not, however, make it any less final - its beneficiary is the winner, and the other is the loser. Thus, it does not have to be – and in fact never is -- that there is nothing whatsoever to be said for the scientific paradigm that loses out (see SSR 99-100, and 107, for Kuhn’s partial defence, in explication of this point, of the "much maligned phlogiston theory" in chemistry). The victorious paradigm may well have won out over the other contender(s) on only a few points.

For a paradigm to be successful is not for it to be ‘either completely successful with a single problem or notably successful with any large number.’ (23)

The differences – the decisive ones – between the paradigm that is installed as the new exemplar for up-to-date scientific practice and the one which it outmodes may be only a few marginal ones from a point of view outside the science, but this is difference enough. Kuhn’s interest is in assessing what considerations did at the time play a part in driving the change; it is the depiction of the bases on which scientists satisfied themselves that they were doing the right thing that is his business.

Kuhn is not here saying that one paradigm is demonstrably just as good as another, and that there is no sense in which the election of one over another may ever be vindicated. It is worth remembering that Kuhn’s concern is with reconstructing the historical situation at the time, without recourse to how things later turned out [a vital aspect of his rejection of ‘Whiggism’.

Kuhn makes an important distinction between the fantasy of a completely successful paradigm on the one hand and what are in actuality encountered -- relatively (more) successful ones -- on the other. (p.23). In doing so he echoes a more general conviction that the thorough and deep exploration of nature is a task that can be pursued virtually indefinitely, and that the continuous carrying through of the exploration will pose more – and more heterogeneous – problems than can be solved within any single framework of inquiry. The scientific attempt is to capture the complexity of nature within a simple scheme, and the complexity of nature will always, in the end, overflow that scheme.A new paradigm can be admirable or notable in that it can solve problems that are known to be more difficult than have been encountered before, or which have long proven intractable. It may identify a whole range of interesting new problems and have every prospect of satisfying them, but in all probability it will, in its turn, encounter numerous problems that are not satisfactorily soluble in its terms.

Victorious paradigms, therefore, offer largely a promise of success, to which the achievement represents an initial guide.

The history of science after the formulation of a paradigm can be very roughly but nevertheless profitably seen as an alternation of ‘normal’ and ‘revolutionary’ science.Normal science is that kind of science which takes place on the basis of a paradigm, within a disciplinary matrix, and on the basis of accepted exemplars, is the science which is done at those times when the fundamentals stand beyond question.

The idea of ‘normal science’ is one which can easily seen unappealing, making scientific work sound routine, dull and unimaginative, but this is an utterly false impression ‘Normal science’ is the condition under which most of the achievements of science are made, and the one under which the much vaunted accumulation of scientific results take place. Normal science is the expression of a humble truth at the heart of Kuhn’s image of science – that investigation of nature is a complex task, and one that is most effectively pursued through a division of labour. It is only when the areas under investigation are ‘typically miniscule’ and where individual scientists operate with ‘drastically restricted vision’ – their attention entirely on developing and pursuing their specific research studies, not distracted from this by arguing over the fundamentals or having to justify their whole approach each time they take it up - that a detailed and focused investigation of nature ‘in ways that would otherwise be unimaginable’ (24) becomes possible.

Most importantly, Kuhn insists, that during ‘normal science’, scientists are not in search of fundamental innovations. They are, so to speak, working within pretty well defined limits with respect to what can be brought into question – what they need to question. Their scientific activity really amounts to the realisation of the potential that the paradigm is expected to provide, and that has been one of the bases drawing scientists to the paradigm to begin with. The development of the paradigm is improvement on its initial formulation, enhancing its precision and extending its scope. This is where the cumulation in knowledge takes place in something like the fashion envisaged by many philosophers of science (especially prominently perhaps in Logical Empiricism and its heirs), as a continuous addition.

To say that the aim of all this scientific work under conditions of ‘normal science’ is improving the precision and scope of the paradigm may make it sound rather less than it is, and stated in this bare way does not really suggest why scientists should display ‘the enthusiasm and devotion’ (36) that they clearly have for their work. Kuhn asserts that the individual scientist is almost never involved in doing the things that people perhaps stereotypically imagine is the greater part of scientific work, namely,

* seeking useful findings just because they will be useful

* opening up wholly new territory to investigation or

* testing well established belief.

(See e.g. SSR 37-8, 64-6, 77, 97.)- and again compare with sociology.

Scientists, according to Kuhn, are normally preoccupied in a quite inward looking way with the technicalities of solving the problems left over by an earlier, and very striking, achievement in their area of work.

What scientists find in the work, again, is a challenge to their ingenuity. Weinberg’s charge, cited in our Introduction, that Kuhn has no explanation as to why scientists bother with these problems is thus falsified. We might paraphrase Kuhn as saying that people often take up scientific problems because they find them deeply intriguing, and they badly want to investigate what is going on; that, in many cases, they just can’t leave these problems alone. Kuhn does not, however, identify any necessary further purpose, above and beyond the satisfaction of having solved a difficult problem, and this is perhaps what Weinberg seeks: one has solved a difficult problem and thereby made a permanent contribution to human knowledge.

Before you start reacting against the idea of normal science, pause to think - about those libraries full of natural scientific periodicals, and of what the content of those must be. They must mostly fall somewhere between direct repetition of paradigm achievements and fundamental novelties. They can’t be full of the same stuff being done over and over. Sociologists of scientific knowledge have made a big, and rather empty, fuss about the fact that natural scientists don’t replicate [much, if at all]. But ask yourself, who with any minimal idea of how the natural sciences work thought they did, that they were endlessly re-doing each other’s experiments? A simple, stereotypical familiarity with the peer review process in a discipline like physics tells you that there are no rewards for coming second, that doing something over is only of value where something of importance may hinge on it. A paper will get rejected just because the work has already been done: see Yazmina Reza’s play LifeX3 ((2001) for a portrayal of the terror struck into an astronomer by being told that a paper on the same subject he is currently writing on has already been submitted to a journal. His reaction: two years of his work has been completely destroyed by this news.

Therefore: what is in the scientific periodicals must be stuff that produces novelty – it can’t be straightforward repetition. At the same time, it can’t all be ground breaking, fundamental changing novelty – the kind of ‘fundamental novelties’ that we more or less non-scientific punters [nonetheless ones who try to keep up with the popularised stuff on science] do hear about are relatively few. Hence, most of what must be in those journals must be ‘normal science’: it does something that makes it worthwhile publishing for the others in the same field, but it doesn’t by any means turn everything upside down.

Thus, normal science is a what Kuhn calls puzzle solving [because it is – under normal science conditions – like ordinary puzzle solving situation, where one is confident that there is, that there has to be, a solution and the only problem is to work out what it is] and the interest is only in those problems which can be assumed to have a solution. Problems will be set aside by scientists if it seems that they cannot be solved.(37)

The analogy with puzzle solving (36) is made to drive home the point that there are several strong constraints on what a scientist must do to solve a scientific problem in the context of normal science. Amongst those constraints there are the conceptual, theoretical, instrumental and methodological commitments already in place within the scientific community. (40) Also, scientific inquiry involves a demand for a continual ‘raising of the game’: any result that is to be acknowledged as an achievement must improve the scope and./or precision of the paradigm. The analogy with puzzle solving is very important vis-a-vis saying what science is for scientists

In short, Kuhn suggests that one try seeing normal science as puzzle-solving – and that the results of doing so are illuminating, and have unfortunately been occluded from and by nearly all pre-Kuhnian (and much ‘post-Kuhnian’) philosophy of science.

Kuhn now introduces another important element in his argument: the importance of training within the framework of normal science. The notion of the paradigm as ‘exemplar’ plays a part in challenging the idea that there is any ‘scientific method’ which could be specified as a set of rules which would prescribe in significant detail how a scientist should go about the business of inquiry. Certainly, no such set of rules is to be found spelled out in the scientific literature. Nor is instruction in such rules any part of the training of newcomers to a science, though these will then practice the science effectively without having been taught any rules. Their training, in significant part, involves confronting them with ‘exemplars’ (in the textbook, the lecture and the laboratory – or equivalent). It is from the close study of these exemplars that trainees learn how to carry out scientific work (within their speciality).

There is a sense in which Kuhn is saying that science is dogmatic rather than critical, a score on which Popper strongly objects. However, we must be careful not to take the idea that it is authoritarian too far [and see the discussion of Kuhn’s relation to Popper below, 000]. Certainly graduate training in the natural sciences can be dogmatic in the sense that students are presented with current science in a take it or leave it form: if they can’t master and accept the current ways of doing things then they will not be admitted to a professional career in the field.

In sum: paradigms are ‘logically prior’ to the research work that goes on within them. And, to continue with Kuhn’s metaphor from gestalt psychology, they are the ground against which innovations, anomalies etc. can emerge as the figure. One can only see anomalies "against the background provided by the paradigm" (SSR 65).

According to Kuhn, the role of fundamental discovery, of fundamental factual or theoretical novelty, has been overstated. Truly novel discoveries are not what are actually sought in the work of normal science, and the necessity for them is usually only reluctantly recognised. We need to emphasise again that this does not say that normal science is hack work, that scientists are going for easy solutions – the work that is done in normal science is creative, productive, and innovative, but innovation in the fundamentals of the discipline is relatively rare.

Fundamental novelty brings about changes in the way in which the science ‘looks at the world’:

The change involved here is, and this is what Kuhn’s entire approach is insisting, is neither a matter of accumulating, nor one of accumulating facts. There is the implication in this passage that the change is of a different kind, one that he sometimes terms a change in ‘worldview’, and that part of this change involves altering the considerations that delimit what kind of a thing could possibly be accepted as a fact within the discipline. The change is not one that involves new findings as such, but one which – in accord with the idea that it involves a paradigm-shift, involves a change in the idea of what kinds of things are properly scientific problems and how they are to be solved.

The key to fundamental novelty is, for Kuhn, the occurrence of ‘anomalies’, a term that precisely captures the vital implication that, again, novelties are novelties only relative to some paradigm, are things which somehow do not fit within the existing scheme.

An example is what occurred in the 1770s vis-à-vis chemistry. Here is Kuhn:

"In 1774 [Priestley] identified the gas [produced by heated red oxide of mercury] …as common air with less than its usual quantity of phlogiston. … Early in 1775 Lavoisier reported that the gas obtained by heating the red oxide of mercury was "air itself entire without alteration [except that] . . . it comes out more pure, more respirable."" (53-4)

One can see the burgeoning anomaly right there, in Lavoisier’s peculiar, almost tortured language. What Lavoisier eventually proposed – and what, as it happens, Priestley could never accept – was that the gas being produced here was not something which could be neatly fitted into the boxes provided by the paradigm of the time, ‘phlogistic’ chemistry. Kuhn concludes that "Only when all the relevant conceptual categories are prepared in advance" can we intelligibly speak of discovery as a point event. (55) As it was, the revolution from ‘phlogistic’ to ‘modern’ chemistry involved a massive revolution in conceptual categories (and so, Kuhn suggests, it is misleading to depict it as happening at a particular place and time, and as being carried out by a single person . One could describe the discovery of (say) krypton or xenon like that, once the periodic table had become well-established – but not the discovery of oxygen, for which no place had been prepared in the chemistry which preceded it.).

Here Kuhn makes an important move, taking a first step toward the expression of what seems to many a very troubling idea – the rejection of the idea of a ‘fixed nature.’ [see below 000].

It is perhaps here worth drawing out something which is largely implicit in but very important to Kuhn’s whole argument, which is the idea that evaluating a paradigm is a complex operation, that any pair of rival paradigms can be matched against each other in many different respects, and that it is not realistically to be expected that either of the two will compare favourably in all (important) respects with the other. There will be, at the very least, pros and cons for each of the two.

A crucial point in Kuhn’s argument, one that is broadly Pragmatist in nature, is the idea that ‘radical critique’ alone is an idle wheel (77). Thus, scientists only give up an accepted paradigm when there is some alternative that they can attach themselves to: that there are some things the paradigm cannot do does not detract from the fact that there are many things it can do. That there are things which the paradigm cannot do is, Kuhn is suggesting, a normal situation, even a necessary situation in something that is (still) a science, and not, of itself, a fateful flaw. The fact that there are things which do not fit an existing paradigm does not result in withdrawal of the paradigm, which makes plain why there are anomalies – if scientists followed the strict ‘logic of science’ (as it is according to Popper for example, a logic of refutation, where a single negative instance can - ideally - invalidate a whole theory), then, when they found something which did not fit with the paradigm they would reject the paradigm and go back to square one, meaning, of course, that there would be no such things as anomalies in Kuhn’s sense. But this is not what scientists do.

Kuhn on the chemical revolution example once again.: many things lose weight upon being burned. Well, at least, they appear to. If one investigates very carefully, collecting all the ash and the water vapour released and the smoke particles etc., one finds that they become heavier. As Kuhn writes,

Ah, so there was a clear refutation of the phlogiston theory available, and in fact it had been available for ages? Not so fast. For while it is true that "In the seventeenth century several investigators had concluded from this fact that a roasted metal takes up some ingredient from the atmosphere", still "that conclusion seemed unnecessary to most chemists." (71) Why? Well, for example, "If chemical reactions could alter the volume, color, texture of the ingredients, why should they not alter weight as well? Weight was not always taken to be the measure of quantity of matter. Besides weight-gain on roasting remained an isolated phenomenon. Most natural bodies (e.g. wood) lose weight on roasting as the phlogiston theory [said] they should." (71) Long-standing anomalies are usually just: things to ignore – for now at least.

When weighing became more accurate (leading to more and more cases of weight-gain being identified), and when "the gradual assimilation of Newton’s gravitational theory led chemists to insist that gain in weight must mean gain in quantity of matter", then phlogistic chemistry started to look pretty bad. Even then, phlogiston was not done for, "for that theory could be adjusted in many ways. Perhaps phlogiston had negative weight, or perhaps fire particles or something else entered the roasted body as phlogiston left it." (71) But phlogistic chemistry became less and less attractive, especially to newcomers to the discipline.

It requires, then, more than the mere existence of anomalies to set scientists to re-examining the fundamentals of their work, of searching for solutions outside what the paradigm will allow. .

So, what do scientists do when their discipline seems to be in some kind of crisis?:

"[We should note first] what scientists never do when confronted by even severe and prolonged anomalies. …[T]hey do not renounce the paradigm that has led them into crisis. They do not, that is, treat anomalies as counter-instances, though in the vocabulary of [Carnapian, Popperian, etc.] philosophy of science, that is what they are." (77, italics ours)

We hope it is quite obvious, now, that this should not be taken to mean that theories in science can proceed merrily by themselves, without regard for how things are in the world, for how one’s experiments are going, etc. There is no reason why anyone should misread Kuhn’s claim that the history of science has never yet revealed anything which resembles ‘that methodological stereotype of falsification by direct comparison with nature’ (77) as suggesting that comparison with nature has nothing whatever to do with it. It ought to be clear that comparison with nature takes place in the context of a comparison of paradigms, and on the terms provided by provided by these paradigms. In a period of normal science, there is regular comparison of the paradigm’s expectations with nature, for this is, of course, what puzzle-solving often consists in, seeing that, and how well, the paradigm works out in further cases. What else are the anomalies except the cases in which the paradigm’s expectations are not satisfied, instances in which nature clearly does not behave according to the paradigm, and the scientists can understand, plainly enough, that this is not what they were expecting?

The search for fundamental novelty is provoked, if at all, by the existence of anomalies, but, since anomalies always exist and do not provoke such quests, the question still remains: what makes an anomaly seem worth concentrated scrutiny? The answer is: it depends completely on the specifics of the case. There is no algorithm for fundamental scientific change: this is a point which fundamentally disappoints rival philosophers like the Logical Empiricists or Imre Lakatos, and contemporary critics like Weinberg. In the ‘extraordinary’ period in science leading up to a scientific revolution, some scientists no longer depend upon and work within the paradigm in the same unquestioning way, but, in their attempts to work out just what it is about the anomaly that is anomalous, attempt to sharpen the tension between the anomaly and the paradigm. They are thus apt to put the usual practices deliberately under strain. Since the capacity of the paradigm to serve as a reliable guide in exploring the area of the anomaly is what is in doubt, the scientists’ behaviour will be somewhat less well directed than under ‘normal science’ conditions, and will once again be a bit more like the random casting about characteristic of the pre-paradigmatic case (with even occasionally explicit argument over fundamentals, or behaviour or thought more like that of a philosopher than of a normal scientist (87-9)).

In an attempt to clarify what is involved in the substitution of one paradigm for another Kuhn makes an ultimately somewhat ill-fated analogy with the ‘Gestalt switch’ in which people are able to alternate between two discrete perceptions of the same thing. The ‘gestalt switch’ is commonly identified in psychology by the ‘duck/rabbit’ in which a schematic drawing can alternately be seen as a duck and a rabbit, or by a picture in which the image of two faces alternate with that of a vase. It was an analogy which Kuhn only cautiously made (albeit, as it proved, hardly cautiously enough). The analogy’s crucial value is in emphasising that paradigms are rivals in the sense that scientists can accept either the prevailing paradigm or its proposed alternate as valid, but cannot simultaneously entertain or accept both (85) The central limitation on the analogy is that in the usual case people can switch back and forth between the two perceptions, - now they see the image as a duck, then as a rabbit, and now they revert again to perception of it as a rabbit. Scientists cannot engage in this kind of reversion, for when they move from one alternate to the other they have given up the first in favour of the second. It is a permanent onetime-only Gestalt switch. A connected disanology applies - the Gestalt idea involves talk of people ‘seeing things as’ this or that (i.e. seeing this now as a duck, now as a rabbit, now as a duck again) which has an inappropriately provisional character in comparison with the categorical ways in which scientists express themselves: they do not – at least when committed to a paradigm, speak of themselves as seeing things ‘as this’ or ‘as that’, but just assert that they see those things. (85; cf. also 114-5)

Scientific revolutions are those times at which one paradigm replaces another, or, as Kuhn later came to emphasise, a new area of research spins off from an established one on the basis of a new exemplar. Obviously, the consideration of how these revolutions take place is critical to Kuhn’s attack on the received image. Given what we have said so far, it ought to be clear that one thing Kuhn will certainly decline to argue is that a scientific revolution is characteristically a dispute between an obviously right party on the one side and an obviously mistaken one on the other. Further, since the paradigm provides the means in terms of which disagreements in scientific results can be settled, if the paradigm itself is in dispute, then the usual means – the only means, in a way – for settling disagreements amongst scientists are out of order. During such revolutionary periods, the situation in the science may be more like the pre-paradigmatic condition than it ever is in periods of normal science: fundamentals are in question, there are meaningful possibilities of seeking out fundamental novelty, there is a lack of focus and a sense of casting-about within the community. However, whilst this is more like the pre-paradigmatic situation, this is not a return to any such condition, and is certainly not going to involve any starting completely afresh and all over again. .

The founding analogy -- with political revolutions -- is seriously and multifariously intended, but should not be taken too far (Kuhn’s rhetoric perhaps gets a little strong on p.93, for example). The analogy’s main value to Kuhn is to provide a reminder that the conflict between the defenders of a political status quo and their revolutionary opponents is one that cannot be resolved by neutral, authoritative adjudication. Where the society once had authorities who would settle disputes , in a time of revolution there is no longer any authority that is recognised by both sides to the struggle, and the only resolution possible is therefore outright defeat of one or other party. Kuhn

One of the key things that Kuhn wants to say about scientific revolutions is that their dynamics have to be understood at the level of the scientific grouping, rather than as a matter of individual choice (again like political revolutions, they involve choices between "incompatible modes of community life" (94)). Considered at the level of the scientific community, scientific revolutions don’t take place through – certainly not only through - a switching of allegiances on the part of individual scientists. In Kuhn’s considered view (this is obviously largely an empirical question), many individual scientists just don’t switch allegiances at all. Those who have been trained and have pursued their careers on the basis of the established paradigm may not give up their allegiance, and it is their resistance to the attempts at change which makes the attempt to bring in the new paradigm a revolutionary struggle. Equally, the protagonists of innovation have not switched their allegiances either – most never were attached to the older paradigm, but have entered the profession with the proposed innovation. Thus, the revolutionaries are often made up of younger scientists, the more recent recruits.

This is not to say that individuals can’t switch, nor that they never do . The point of Kuhn’s argument is that understanding what such individuals do is not the exclusive key to understanding scientific revolutions. Such revolutions are shifts in the collective balance within an area of scientific work, where a small minority may enter and eventually triumph over what was previously the as-near-a-complete-consensus-as-you-will-ever-get Here, the idea is that the revolution takes place within the same field of scientific work, that the old paradigm is thrown out and the area of work reconstituted on the basis of the new paradigm. As mentioned, though, Kuhn later came to think that a common and [from his point of view] very important result of scientific revolutions was a break-away from the original discipline and the foundation of a new specialism .

We don’t have to worry too much about whether all, or even some big proportion of scientific revolutions are really like Kuhn’s picture . (Nor indeed to worry about which candidate-revolutions were ‘really revolutions’. Kuhn is providing one with a tool-kit, not an encyclopedia of truths – see pp.000 of our discussion of BB, below) The relevance here is with respect to Kuhn’s argument, which is that the transition between one paradigm and another is not necessarily a matter of what has traditionally been imagined to be a rational choice.??. To the extent that it involves a changing balance in the composition of the profession, it is not a matter of individual choice at all. Neither, of course, is it a collective decision in that all have been parties to making some kind of collective agreement, it is simply an emergent outcome of the exigencies of the struggle between the rival camps. The idea of the community arriving at a decision by means of explicit rational and conclusive debate is one that Kuhn is mocking. This is not to say that there is not debate, for there surely is, still less to deny that there is rationality, of which ‘science’ even at times of revolution could arguably be seen as a set of paradigms; but the idea of scientific debate effectively and purely ‘rationally’ persuading people across from the old to the new view is, at best, oversimplifying. There is plenty of debate,but where the debate does affect people, and induce change, it does not do so in the way that the received view imagined. The change in those who do switch allegiance is [notoriously, as Weinberg complained] more like a religious conversion than it is like a rational i.e. impartial, reflection on and appraisal of two rival points of view. It is a good question as to how much this debate features actual and direct disagreement rather than arguing in circles, begging the question, or just talking past each other? This is why scientists can’t simply, by good logical and evidential proofs, establish to each other’s general satisfaction which of two rival positions is the correct one.

The debate in a scientific revolution is, like that in a political revolution, often circular. There is a real obstacle to mutual persuasion in that each party is appealing to principles that the other contests. For example, in order to accept a conclusion you have to subscribe to the premises from which it is drawn, but this is just what the parties involved do not do (Consider for example the face-off between the divine right of kings and the principle of democracy in France around 1789-92). In the scientific case, each group depends on its own presuppositions to justify and evaluate its results, but a convincing proof can only be given to someone who will concede the premises to begin with, and thus the disputants cannot prove to their rivals’ satisfaction that they – the rivals - are wrong . This explains why there are many who are unaffected by the arguments of their rivals, but it does not follow that argument has no persuasive effects at all, though these may have an impressive rather than a logical force. Arguments can provide a clear and vivid display of what the vision of the new paradigms, of what scientific practice will be like for those who adopt its view of nature, and some people may indeed respond to this. It cannot, however, be made compelling ‘for those who refuse to step into the circle.’ (94)

So: It is hard for the controversialists in these debates to understand each other, to be able to appreciate each other’s point of view, and the fact is, Kuhn argues, that in one way or another, and in one or more ways, they often don’t. Whilst the scientists are adamantly refusing to change sides, it may be that they are under misconceptions about what the position they are rejecting actually is. It is not that the controversialists find each other’s positions to be hard to believe, they often find them hard to understand in that they cannot see that what the other says makes any real sense. This is a crucial innovation of Kuhn’s: emphasising that deep scientific disputes involve questions of sense/meaning just as much as (in fact, more than) questions of true and false, questions of simple fact. If this is so, then the two sides – to some greater or less extent – are handicapped in being able to explain their respective positions to each other, to appreciate each other’s points of view.

Does it have to be this way? Must it really be that some new phenomena or theory absolutely cannot be assimilated to the existing paradigm? If the anomaly could be smoothly integrated into the existing paradigm, then the stereotype of science that Kuhn has rejected, as developing in a ‘fully cumulative manner’, would be true. But the stereotype does not fit the facts:

There are good reasons why this is so. Normal science research is cumulative, but novelty of the sort at issue here can only exist to the extent that it does not square with the logical consequences of the paradigm in place. So, there must be a conflict [a ‘logical gap’; a gap, that is, between two logically coherent but distinct systems] between the existing paradigm in terms of which the anomaly is truly that, and the new paradigm in relation to which the phenomenon is no longer an anomaly but, rather, amongst its logical derivatives. (97) The differences between them, further, are not just substantive, for the new paradigm brings about a reorganisation (or ‘cannibalisation’) of old science in the relevant discipline, perhaps re-allocating some of its problems to another discipline, declaring others unscientific, and promoting things previously deemed not to be problems or to be only trivial to pride of place. (103) In the Copernican context we will remark on Kuhn’s talk of the ‘hard core of knowledge’ that remained constant across scientific changes, noting the extent to which the content of the previous paradigm is not entirely abandoned, that ‘old science’ is carried over into the new context. However, in line with the Gestalt-switch analogy, there is in SSR, much greater, or at least more explicit (than in CR), emphasis on the extent to which the ‘preserved old science’ undergoes a change of character : what is carried over will be extensively altered by its transplantation.

Once again, then, we need to bear in mind Kuhn’s emphasis on the issue of complexity of paradigm-to-paradigm comparison. It is not that there are not quite general criteria which may be used for invidiously comparing paradigms,but there are three things to be borne in mind: [a] that in real science people are characteristically already signed up to one or another paradigm when they start making these comparisons [b] that there are real obstacles of properly identifying the characteristics of the respective paradigms in the revolutionary situation and [c] that there is a plurality of general criteria, and that any one paradigm will score well only on some of these and [d] that there is, in any case, no formula which dictates which of these criteria should be given priority or how they should be traded off against each other. Using the same criteria people could end up [as they do, Kuhn claims] drawing quite different conclusions as to which is – in an overall judgement – the better paradigm. There are rules for comparing paradigms, but there is no formula for applying them conjointly.

SECTION B ((?)):

Toward the end of SSR Kuhn begins to draw out some more philosophical implications of his argument, to reformulate in more philosophical-seeming terms what his case amounts to. There are four such moments which were especially fateful for the fate of this work, and whose deeper discussion will figure large in the later part of this book. These are the ideas of ‘world changes’, of the ‘two moments’ doctrine of perception’ and ‘incommensurability,’ and [as we have mentioned] his rejection of the idea of ‘ ‘a fixed nature’.

In the latter sections of SSR, Kuhn starts to say some strange-sounding things, ones which seem at least troubling to many, if not outright bizarre.. Having considered how

paradigms ‘constitute’ science -- i.e. give order and structure to its inquiries – he announces that he now wants to explore the ‘sense in which they [paradigms] are constitutive of nature as well’ as science. (110) Rather than being ready to hasten to agreement with or dissent from this statement, readers might well hesitate to reflect that it is already qualified in light of the mention that it applies ‘in a sense’. Rather than flatly and forcefully affirming: ‘paradigms are constitutive of nature’ Kuhn is himself pondering what, in saying such a thing, he might mean – and does say that he is not yet sure what even he means by it: ‘I am convinced that we must learn to make sense of statements that at least resemble these.’ (p.121) (see also "electric displacement", top of 109) Next , another crucial, but also crucially qualified statement:

It is clear, noting that Kuhn is speaking of what the historian might conclude, and if one attends carefully to his phrasing, that Kuhn is largely but not entirely aware that saying that ‘when paradigms change, the world itself changes with them’ is a facon de parler only. He is somewhat uncertain as to whether this is only a resume of what he has argued thus far, or is saying something rather more than this, that has got at least some quasi-metaphysical anxieties attached to it – what we will shortly identify as the phenomenal worlds problem.

As far as we are concerned, Kuhn’s formulation is acceptable only insofar as he, Kuhn, is searching for a form of words that will rid us of our main temptations to misunderstand the history of science – he is not issuing a metaphysical thesis. What he gives here is a formulation that can emphasise (perhaps even exaggerate for thought-provocative purposes) the impact which scientific revolutions have on the outlooks of scientists, to help in overcoming the received view.

For the scientist, the world might be said to change. As a descriptive characterisation of the differences which the historian, comparing two successive periods, notices it is more unproblematically intelligible: it is as though there had been a change in nature itself, so very different are the pre-scientific and post-scientific environments. Before the revolution the scientists would talk prominently and a great deal about a certain phenomenon which after the revolution they would never mention again. And, reciprocally, after the revolution, scientists would start talking about phenomena that had never figured at all in their discourse before it. However, though these are only strong metaphors to give a flavour of the changes paradigm shifts engender, Kuhn is often understood as if he implied something more substantial than this, as if we was indeed saying in a more literal way that ‘paradigms do constitute nature’, and that, therefore, when a paradigm changes the world literally changes with it. .Thus, one can see how the ‘world changes’ issue gains its name.

We are not saying, at this point, Kuhn is wrongly understood as intending something more literal than metaphoric with talk of such world changes, for we think that he is drawn to the idea that more than a pure facon de parler is involved. Even so, we think that his work is clearly dissociated from any such drastic conception as that changing a scientific theory brings about changes in the natural world itself. However, there is an important change of gear taking place here, as the notion of ‘different worlds’ slips from being an idiomatic expression into a philosophical one, where ‘world’ often means much the same as ‘reality’ or, even, ‘natural reality’ – as in ‘there is a world out there.’

Kuhn’s attraction to saying that the world changes with paradigms leads him into a problematic as a result of the way in which he conceptualises perception, and, therefore, observation. Kuhn is driven toward the conceptualisation, we think, because of the implications of his arguments about paradigm shifts, considered in relation to the empiricist tradition in philosophy of science from which is trying to make a complete break – but not quite managing to do so.

Given Kuhn’s views about the historical relation between an earlier and a later paradigm, we argue, means that he feels compelled to say that, descriptively, the Aristotelian perception [of a pendulum’s motion] is just as accurate (119) as Galileo’s – and, indeed, that the triumph of the latter over the former was something of a swindle – Galileo’s preconceptions about pendulum motion ‘led him to see far more regularity than we can now discover there’ (119). From his point of view, it seems that we have to say that both the Aristotelian and Galileo himself, observing the same case of motion [say a stone swinging on a stick], will both make observations that are, in their terms, largely, if not entirely accurate. We cannot, given the constraint of Kuhn’s anti-Whiggism resort to what might otherwise be the ready solution: to take Galileo’s description of the case as identifying what is there to be observed, and deeming, therefore, that the Aristotelian has failed to observe correctly to just the extent that his description deviates from Galileo So, we can’t say one of the two parties, Galileo, correctly observed the facts, and the Aristotelian failed to do so.] Without some independent and definitive source which says what the facts are, how are we to say whether one person has observed the facts more correctly, more accurately, than the other. We can actually say, or Kuhn does say, that the two describe the facts equally well. Thus, we seem compelled to say that each party did observe what they reported themselves as observing; - but they both observed something different in the same place.

Having made an attempt to deal with the issue by allowing that each did observe what they said they observed Kuhn has not eased the pressure on his situation, but intensified it. What are we now to say about the situation in which two scientists, confronted with the same phenomena – a swinging stone on a string – observe something different – cases of constrained fall and pendulum motion respectively? Having gotten this far into a hole, the Wittgensteinian philosopher would advise that we stop digging, but Kuhn is not that much of a Wittgensteinian. He keeps digging. Kuhn seeks his way out of his difficulties by declining to treat the question ‘do they observe the same thing or something different?’ as calling for a yes or no answer, and proposes instead to answer it with: yes and no: they do and do not see the same thing.

This alone is O.K., but Kuhn now thinks he needs an account of perception/observation. He adopts what we will call a ‘two moments doctrine’ ; in a philosophical terminology Kuhn does not himself use, this involves the staple of empiricist though, the ‘given’ and its interpretation. Kuhn wants to escape from the untenable consequences of belief in a given – this is what his terminological contortions are about – but he often, as here, falls back into thinking that some kind of world – or even some set of sensations – is given. There is only one physical world out there, Kuhn (with virtually everyone else) wants to say, this does not change with scientific theories, and Kuhn is not, and never did, suggest otherwise. Therefore there is one and the same natural world, having its natural effects on the scientists who observe it, and, since they are biologically similar creatures, affecting them in pretty much the same way. There is one and the same shining light up there in the sky that scientists from two different astronomical paradigms do see. So each sees something, and in these terms, they both see the same thing. However, we cannot say in a scientifically neutral way what it is that each sees, just because the identity of the (source of) light is what is in dispute between them. What they see, what they can possibly say they see, is – in scientific terms – not at all the same thing, and whether one says he or she observes a planet where the other says he or she observes a star will depend entirely upon the scientific tradition to which they respectively belong. Without the appropriate tradition, one cannot say that one sees a planet or a star, and what, therefore, the scientists actually observes is a composite, made up of the input from nature, and from the resources of the paradigm.

Kuhn therefore feels driven to say this kind of thing :

but is puzzled enough by his own expressions in such case to have to ask :

.

Kuhn feels himself forced to continue with these strange locutions though he is ‘acutely aware of the difficulties I am creating’ in so doing. Consequently, he sees no choice but to reaffirm that

Even so, again, he does not convey a sense of a clear and confident understanding of what he is using these strange locutions to say. Kuhn is perhaps clearer on what he is trying to get away from, than of what he is trying to put in its place, but he has not yet perhaps got far enough away from some of the things that philosophers of science used to say, and as a result is creating a puzzle for himself, compelling himself to adopt strange expressions. . Though perhaps this is in substantial part a good thing. Kuhn’s strange locutions are, he thinks, forced upon him chiefly by his desire to avoid the language of the largely discredited empiricist tradition, and (more generally) of the ‘received view’ in the philosophy of science. Kuhn is seeking a way to avoid the doctrine of ‘the given’. This is something that he has in common with most major philosophers of recent times, notably Sellars and Davidson (though Davidson misses this agreement, and in doing so misses Kuhn). Our point is in part: Kuhn has not found a way of avoiding the myth of ‘the given’ which does not yield new philosophical perplexities.

The empiricist tradition had not depended upon the ‘hypothetical fixed nature’ but rather the ‘fixed experience’ as the ‘court of final appeal’ in its analysis of scientific dispute. The notion of an ‘observation language’, which is distinct from the ‘theoretical language’ of a science, and is meant in philosophy of science to be what is used to describe scientists’ experience, can describe what they observe in a way which is ‘neutral’ between competing scientific theories.Rival theories can be compared with experience described in the observation language, a language that is independent of both their terminologies. But, following Kuhn’s arguments, this cannot be so, either – we will see, in the Copernicus case, how deeply (in Kuhn’s view) the ‘interpretation’ goes relative to the observation. Indeed, given the ‘doctrine’ of the ‘two moments of perception’, the interpetation penetrates the observation. (If the two moments are only notionally separable, this is another way in which Kuhn is genuinely endeavouring to free us of the myth of the given.) Kuhn is arguing that if one is going to talk about anything that might be called scientific observations then one cannot disentangle the given from its interpretation in any effective way. What counts as an observation in science is, for Kuhn a composite of a given input from nature and of an interpretive capacity supplied by training in a scientific paradigm.

Furthermore, the ‘given’ in the laboratory should actually be termed ‘the collected with difficulty’ (126). It takes a full and deep absorption of the paradigm, plus the kind of acuity and intelligence required to practice normal science effectively, before a scientist is in any position to observe the kinds of things that are actually of interest to other scientists on the frontiers of research. Near those frontiers especially, there is no way in which scientists’ experiences can be decomposed into any more elemental form – direct reports of bare sense experience, divested of all the paradigm-based learning that is the precondition to the scientist being let loose in the lab at all (126-128) – which would allow specification of what they observed in a way which would not draw upon the ‘theoretical’ language of a paradigm. Thus, Kuhn insists, scientists are right to treat such things as pendulums and oxygen as ‘fundamental ingredients’ of their immediate experience, and not as theoretical construals of any more basic experience. But this means that there is no stable or common experience that can be appealed to in adjudication of paradigms either, because the experience itself is partially composed of the interpretation. Here Kuhn is most definitely not saying that one perceives an input from nature, and then gives it an interpretation. What he is saying is: that the scientist’s perception itself is composed of both the input from nature and the interpretation. For the purposes of scientific observation, then, the experience cannot possibly be extricated from the interpretation, and therefore the scientists cannot have recourse to the pure, extricated element of ‘the given’ in their experience. Thus, the observational materials – the data – available to scientists cannot be said to remain stable across changes of paradigms, because the observational materials are irreducibly characterised in terms which draw upon a paradigm. Thus :

Kuhn has denied that the staple of the empiricist approach, a distinction of some kind between observation language and theory language, can be of any use in the understanding of scientific change, but he has not thereby entirely abandoned the distinction, between the given and the interpreted that this distinction was meant to express. What we have been intimating is that in fact he has not been completely clear and consistent about this; he has not succeeded in abandoning the myth of the given (and far be it from us to suggest that it is easy so to succeed). He has retained in some measure the distinction between the given and the interpreted, but has shifted the point at which the dividing line between them can be drawn. The line is no longer drawn between what is given in nature or in perception, providing ‘sense data’ and the interpretation that is then applied to that given, for, on Kuhn’s account, the given and the interpreted are both combined in perception, in what can meaningfully be called – in respect of scientific observation – sense data. Our view is that this is progress; though better progress still would be to find a way to give up the very idea of ‘the given’. However, it is retained, and its retention provides further encouragement to maintain that two disputing scientists do indeed both make genuine observations, for whilst they are observing something different they are nonetheless observing something that is the same: the same bits of the natural world enter into their perceptions in each case, and we cannot therefore say that one scientist does observe something, and that the other does not observe anything at all. Both observe something which is real, but the way in which they experience what they observe differs [as a result of their different backgrounds. Therefore, neither of them observes the external world of nature in itself , but we cannot, on those grounds, say that they do not make valid observations. At the same time, we cannot invidiously contrast the different experiences that their observations generate, for we have no way of saying that one of them observes nature in itself more closely or accurately than the other. Therefore, there is the temptation, to which KuhnKuhn succumbs, to say that the respective scientists each observe something real, that the world observed by one is no more or less real than the other, and that, therefore, each observes a reality, each lives in a real, but different, world. The worlds found in the respective scientists’ experiences are not, however, to be confused with the real world in itself, they are kept distinct: one way in which to express this [in accord with the Kantian connection] is to say that the scientists inhabit phenomenal realities, that they occupy different phenomenal worlds.

What the beginning scientist learns to see is determined jointly by the environment and the particular normal-scientific tradition that the student has been trained to pursue. (112))

If part of what perception is dependent upon changes, namely, what previous ‘visual conceptual experience’ has taught, because important – especially conceptual -- parts have been withdrawn and replaced, then the scientist’s perception must be re-educated, which among other things means acquiring a new Gestalt. This is another reason why discussion between different paradigms is always at least slightly at cross purposes.

These considerations, whatever the merits of particular forms of words via which Kuhn (and we) try to adduce them, are clearly meant to fill out the analogy with revolution, and with the absence of any authority to adjudicate between the two sides. Kuhn has eliminated the empiricist’s sole source of final authority – raw sense data – and, given the general pre-eminence of empiricism in Anglo-American philosophy of science, has removed from the philosophy of science the notion of an authority external to the scientific schemes themselves.

b The idea of a ‘fixed nature’ can have no part to play in an historical understanding of scientific change of the sort that Kuhn envisages. The idea of ‘world changes’ is not, itself, a denial that there is any such thing as a ‘fixed nature’, compatible with a superficial interpretation of the claim that when the world according to science changes, nature itself changes with it. As we have said Kuhn accepts the idea that nature itself does not itself change with every scientific revolution, since that world out there is one of the two moments of perception, the common ‘given’ that scientists allied with different paradigms differentially interpret. ‘The world out there’ retains a certain constancy throughout; stars do not transmute into planets, mixtures do not mutate into compounds. However, whilst we may be confident that nature does not alter with each paradigm shift, we have no way of saying what it is that remains constant throughout. The question of what it is that remains constant throughout is the question over which the paradigms are contesting: is it, and was it always, a planet or is it really a star, is it, and has it always been, a compound, not a mixture? Thus, whilst we might accept that there is a ‘fixed nature’ in this sense, it is not one that we can appeal to as an independent point of reference against which competing paradigms may be compared, which can play the kind of role as a final authority that philosophy of science had required of it. To attempt to say, in any substantive way, what is actually ‘out there’ as the object of scientific contest would be to make an [at least tacit] identification with one side of the argument or the other. A ‘fixed nature’ would be a useless ornament on, not a working addition to Kuhn’s model of scientific change. What he is really doing is saying that the idea of a ‘fixed nature’ is a kind of idealisation which plays a distorting role in understanding these problems – i.e. the problems of the philosopher and the historian, not necessarily the problems of the scientist themselves.

His appreciation that he is resorting to a ‘strange locution’ indicates Kuhn’s unease.

The notion of ‘different worlds’ has been backed up by the doctrine of the two moments of perception and the rejection of the idea of a fixed nature, and this now gives rise to what is perhaps Kuhn’s most fateful, and certainly his most controversial, conception, that of incommensurability.

Incommensurability – which literally means ‘cannot be compared by a common measure’ -- has been involved in the argument about the discontinuities between successive paradigms, both in the discussion of paradigm shifts, and of the ‘world changes’ issue. There is no independent, neutral standard against which two competing paradigms can respectively be compared. They can only be compared with each other, though the idea of doing that is complicated, and does not provide the kind of comparison that philosophers of science needed – the one which adjudicates which of the two is most closely in accord with empirical reality. The idea that philosophers can make that kind of comparison, standing transcendentally to the hurly burly of scientific dispute, is being exploded.

Perhaps the most important of all Kuhn’s thoughts with respect to philosophy of science is this: he asks whether economics is the most successful social science as a result of economists knowing more about science and truth than, say, sociologists do. Or is it that they know more about economics than sociologists do about society? Generalised, this question asks: could philosophers, who know about ‘truth’ and about ‘science’ possibly know more about what scientists should do than can the scientists who know, after all, nothing about truth and science in the sense that philosophers do, for the latter only know about black holes, or quarks for example. From Kuhn’s point of view this is a rhetorical question.

We have not yet paid attention to the second respect in which incommensurability matters to Kuhn, and that is as a source of misunderstanding between competing scientists. Far from rival scientists taking the true measure of each other’s positions, Kuhn maintains, they often misunderstand each others views, and, as a result, in scientific revolutions sometimes do not really critically engage with each other, but talk past each other – after the revolution is over the losers are simply forgotten..

"communication across the revolutionary divide is inevitably partial", he remarks (in)famously, at one point (149).

to see just what Kuhn means here,, however, let us see what else Kuhn actually says. On p. 112 he remarks

And now some very lengthy quotation, though since the issue of incommensurability is so important, access to Kuhn’s own words is surely justified here:

First, then:

And, shortly after,

And, finally,

tThat Kuhn’s formulation of the idea of incommensurability was, at the time of SSR, quite unspecific on a very important point, namely, just how great are the misunderstandings between scientists? Is it the case that scientists from different paradigms are hardly able to make sense of each other at all, that they misunderstand each other on almost every point, no matter how small or great? One could certainly read these passages as licensing such a reading, yielding a picture of scientific revolutions as almost farcical episodes of mutual incomprehension. On the other hand, one can read the same passages as claiming something much more modest, and less far reaching, namely, that incommensurability means that failure of mutual understanding is an exigency of revolutions, that there almost certainly will be times when minds do not meet, but that these will be occasional, on particular points, either major or minor. Kuhn eventually clarified that the latter reading was his intended and preferred one.

From these remarks, one thing is however certain: Kuhn is not saying that incommensurable theories cannot be compared - what they can’t be is compared in terms of a system of common measure. He very plainly says that they can be compared, and he reiterates this repeatedly in later work, in a (mostly in vain) effort to avert the crude and sometimes catastrophic misinterpretations he suffered from mainstream philosophers and post-modern relativists alike. Integral to - though tacit in - his point in saying this is that paradigms are complex constructions and that comparison of them is a multidimensional affair; he is considering theories as theoretical (or ‘conceptual’) schemes rather than e.g. unconfirmed conjectures. Thus, it is not as if a theory can be individually accepted or rejected simply on the basis of fitting the facts because, as we have explained before, in Kuhn’s view any scientific scheme that has had any support both will and will not ‘fit the facts.’ (see pp.79-83 in SSR) There are always abundant - but largely inconsequential - anomalies to any theory, but there are also lots of instances which – in its terms - fit the theory too. Hence, the question cannot be asked, does this theory fit the facts, the only meaningful question is; does this theory fit the facts better than this other one. So, the two can be compared, and it can be eventually fairly conclusively decided by the science- , at least in the case of Priestley vs. Lavoisier - that the latter’s approach fitted the facts better than the former’s. But to say this offers no comfort to Whig historians or traditional philosophers of science. To say that Lavoisier fitted the facts better is of course what Lavoisier’s heirs (i.e. all of us, in so far as we have chemical knowledge) will say.

The importance of incommensurability for Kuhn is not that it presents a problem for science. It does not. The misunderstandings between scientists are not mutually experienced as such; it is not that scientists will be brought to a grinding halt by the realisation that they really cannot understand each other, and that they need to establish real reciprocal understanding before they go any further. It is important in other connections for Kuhn that, of course, the scientists do not usually realise that they are talking at cross purposes. They think that they are in straightforward disagreement, that they understand the other’s position well enough, and that they can see just what is wrong with it. Thus, it may be on the basis of [some] misconceptions about the usurped paradigm that its replacement wins out, but the verdict is irreversible.

Incommensurability presents a problem for the philosophy of science. What Kuhn is denying – as a cumulative result of the arguments about revolutions and the world changes and phenomenal worlds – is that it is possible to compare scientific theories in the way that philosophers of science have imagined that they could, that they can be matched by those with a only a spectator’s interest in science, such as philosophers, against each other in some decisive way. Thus, Kuhn is denying that two theories can be jointly compared against any independent, neutral standard or set of facts. He is also denying, and this is the distinctiveness of the notion of incommensurability, that the two theories lined up against each other as though disagreeing on the answers that they give to a list of common questions, such that we could assess which gives the right and which gives the wrong answer to these questions.

And even to speak of Kuhn ‘denying’ claims in the philosophy of science may be misleading. For Kuhn aimed usually to establish the nonsensicality of the claims he was rejecting. In roughly the following sense: he aimed to get his interlocutors to see that there was nothing that they really could want to mean by comparison point by point of theories across major changes in science. That they would fail to understand the predecessor science as science, and/or simply fail to understand it, if they insisted upon such comparison, ‘translation’. (We address this point in more detail in Chapter 65, below; see also ‘Commensurability, comparability, communicability’ in TRSS ) for a fine example of Kuhn trying to persuade his opponents (in this case, Kitcher, and, by extension, Davidson and Quine) that they should themselves give up their anti-incommensurabilism, when they realize that it will make a complete nonsense of any attempt to render phlogistic chemistry in terms that we can actually understand, and still be understanding phlogistic chemistry.)

. Here is one example of why Kuhn thinks that point-by-point comparison is not possible between paradigms

If a point-by-point comparison is imagined as a matter of placing the assertions made by the empirical part of rival theories in ‘conjunction’ with each other and with cogent evidence bearing on the truth of each, then such point-by-point comparison would involve comparing Newton’s answer to the question of what was the cause of attraction between particles with Descartes’ or Einstein’s answers to these questions. Aristotle says that this is the cause of the attraction, Newton says that and Einstein says the other;- now which, if any, is nearest to being right?

However, Newton does not give any such cause but not because he overlooks to do so.–. Newton does not accept that his predecessors have identified the cause, but not because they have been wrong about what the actual cause is, and he is now about to give them the right answer to this question.He disagrees with them over whether or not you need an answer to the question, over whether your account is significantly incomplete if you don’t feature a cause of attraction. And that of course brings up in turn other differences between Newton and the others. There is comparison, here, but it is not ‘point for point’, For the difference between Newton’s theory and its predecessors - and its successor(s) - is not that it has a different answer to the question than they do, but that his scheme leaves no space for the question that they want to ask.

We mentioned the need to be wary with the use of the term ‘coincide’ to represent the point at which there are empirical results that can be compared between paradigms; a major effect of incommensurability, is to mislead, that even when paradigms look as though they are in important respects directly comparable in a point to point way, this may be a false impression. It is one of the key suppositions of Kuhn’s whole enterprise that resemblances between paradigms are often far more superficial than they appear - the paradigms only seem to be in agreement, and the scientists who adhere(d) to them to be making assertions which only look like they are mutually empirically contradictory, and thus at least straightforwardly comparable, (If one assertion contradicts another, then they are at least in the same ballpark) Let us try to understand an example that Kuhn himself gives.

Take the case of his remark ( (SSR 102)) that mass a la Newton and a la Einstein can be measured in the same way at low velocity but ‘must not be conceived to be the same’. This is surely illustrative of what Kuhn means by incommensurability. It might be objected against us (and Kuhn): If the measurements given, i.e. the quantities specified, are specified in the same units before and after the Einsteinian revolution, and, in those units, give the same values, then how could they not be the same? Certainly Kuhn will not deny that these units and measures appear identical, but he is arguing this is just the kind of confusion that motivates his whole enterprise – they may look like they are just the same, butone had better not treat them as if they actually are. Attempting to identify these parts of Newton’s scheme without understanding the way in which they fit into and make up Newton’s scheme first will only result in a neglect of the fact that they do not really involve the same scientific ideas at all. The difference is not in the values yielded, but in what it is that the values yielded are measuring. It is perfectly correct, from an Einsteinian point of view, to say that the correspondence in quantifications with Newtonian measurements is good enough at low velocities. However, this is itself an Einsteinian, not a Newtonian way of talking. To say that Newtonian calculations are correct when measuring mass at low velocities is to misrepresent what Newtonians are doing in Newtonian terms. Mass is a fixed quantity in the Newtonian scheme, and so when it has been correctly measured or calculated, that is what mass is . The velocities at which mass was measured were not conceived in the Newtonian scheme as ‘low’ velocities, for there was no physically relevant conception of high velocities - such as approaching the speed of light - with which to contrast them. So, though it is perfectly correct in Einsteinian terms to say that the Newtonian scheme works perfectly well for masses measured at low velocities, this is not a correct characterisation of what, in Newtonian terms, was going on. Thus, when Newtonians use ‘mass’, its ‘grammar’ is of a fixed quantity which is conserved. Just think of the difference between ‘football’ in ‘association football’ and ‘rugby football’, and between ‘goal’ in the former, and ‘goal’ in the latter (and in ‘American football’, too). Going ‘over the bar’ in one qualifies it for a goal, in the other, it disqualifies it as one. Wrestling with ‘reference’ does not really help, we think; -the difference is in what you can say and mean in the language- and with the way in which expressions fit in with other expressions - in the context of rugby football, ‘Its over the bar’ means ‘He’s scored’, in association football, it means ‘He’s missed.

To get away from any sense of fatal paradox or irremediable confusion here remember that the point is just to denumerate the respective characteristics of Newton’s and Einstein’s theory, to see that these are using the same words in such a way as to mislead the unwary into overlooking the fact that the parallels in those uses are limited, and go along with divergences between them. [And: what we (after Kuhn) are doing has a metaphilosophical point; it is not intended as a set of theoretical claims. We mean to contradict the (would-be) propositions of the philosophers of science that came before us still less than Einstein can intelligibly be said simply and directly either to agree with or to contradict Newton.] The idea of them being rivals is rather a restricted one if it is taken to mean that one must make contradictory claims, when, in fact, the rivalry is, of course, of a different kind - that e.g. the Einsteinian calls for reformation of the Newtonian vocabulary so as to raise questions that couldn’t be raised within the Newtonian scheme, and, as such to displace Newtonian usage, so that e.g. Newtonian ‘mass’ becomes ‘mass at low speed’ (which is certainly not what it originally meant.). Thus, it is indeed ok to say that ‘the two theories remain conflicting accounts of the same thing’ (Sankey 161) so long as we remember that this means they are conflicting accounts of mass, and that mass in Einstein is by no means simply the same thing it is in Newton! There is no contradiction in saying this - if one understands Kuhn’s ‘position’ appropriately.

In sum: Newton and Einstein are definitely in competition with one another – that’s why you can only have one of them, not one of them as a special case of the other. But, to help avoid confusion we must insist that Newton and Einstein do not contradict each other – not because they agree (at all), but because the nature of their ‘disagreement’ involves them necessarily talking across each other (See SSR 149 and 98).

So: What is plain about Kuhn’s presentation of ‘incommensurability’ is that it raises issues that have to do with the mutual comprehensibility of rival paradigms to the scientists who are involved, in a partisan way, with them. Clearly, incommensurability has considerable bearing with respect to the actual, not the perceived understanding of some scientists by others. If an Einsteinian scientist employs the Newtonian calculations to determine mass-at-low-velocities then he is not actually using the Newtonian method, since those do not calculate mass-at-low-velocities, but just calculate mass. If the scientist is indeed operating in this way, then he or she is working on a misconception, is not using the pure Newtonian ideas, but only those ideas reconstrued in Einsteinian terms. Of course, it makes no material difference to the scientist’s science (only to their image of their activity, their sense of their position in history, etc.) that he/she uses this way of calculating as a convenience, nor that, in order to do so he/she has stripped them off its specifically Newtonian aspects. It is not, either, at all possible for the Einsteinian scientist to do otherwise. The Einsteinian knows that it makes a difference whether a mass is being accelerated through low velocities or toward the very high ones, and cannot operate the Newtonian techniques save on the basis of this knowledge. They cannot have the sense, for the Einsteinian, of calculations of mass, period, but only of calculations of mass-at-low-velocities. As used by the Einsteinian, these calculations are in the historical sense, not-really-Newtonian, only ‘sort of’ or ‘partially’ Newtonian. Thus, the claim that Einsteinian physics has incorporated Newtonian physics as a special case is erroneous, for it has rejigged Newtonian physics or, in another metaphor, it has cannibalised it; or, as we ourselves would more commonly put it, has changed its grammar. Einsteinian physics is a different language-game: though of course ‘language game’ is a term involving the activities with which these words are bound up. Science isn’t just words.

How significant is this in Kuhn’s thought? It is important to Kuhn, for it is a main basis for his central historical contention, that the degree of continuity between succeeding paradigms is apt to be exaggerated, and the extent of conceptual discrepancy between them to be under-appreciated.

We now come to the last of the strange or outrageous things that Kuhn says in the latter part of SSR, and one of the main topics which has been provocative of most subsequent debate, namely, the sense in which THE developments of science, especially those changes which yield or constitute ‘revolutions’ can be regarded as ‘making progress’. In a way, Kuhn’s previous discussion has straightforwardly and effectively answered the question as to the sense in which science can be said to make progress - his description of the way in which paradigms replace one another (in concert with his earlier description of the accretion of knowledge in science under normal conditions) itself describes the way in which science can be said to make progress. What Kuhn has already done is, in a way, to describe how the community of scientists determine that they are making progress by showing how they opt for one paradigm over another. The import of this is that once this has been shown and understood, then further questions about progress -- and progress ‘toward Truth’ -- are effectively empty. What Kuhn is effectively doing by excluding ‘truth’ – as it has traditionally functioned in the philosophy of science – and making, rather, such observations as those listed is rejecting the idea that science is any kind of fulfilment of the aims of metaphysics. Realists are apt to treat science as though it has delivered or will deliver what metaphysics sought for, namely a depiction of what there really or finally is, and the question then is, for them, how close is science to rendering this final, ultimate description. Kuhn does not, however, accept that this metaphysical notion can have any role in characterising the results of science, meaning that he cannot pose, let alone answer, the question that the Realists would want him to.

Now, Kuhn holds that the assertion that ‘science makes progress’ is to a not inconsiderable extent a circular one, for something does not qualify as a true science unless it makes progress. But how can such a claim (as Kuhn’s here) be justified? If we are to accede even to this claim, do we not want some independent measure of progress to ensure that ‘making progress’ is different from ‘just substituting one paradigm for another’? But this is just what we cannot have. If we understand the relationship between scientific work and the scientific community then

One can’t - at least Kuhn says he can’t, and that he doesn’t believe he needs to - find a way, independently of that scientific community, of saying whether a science is making progress. It is that ‘independently of that scientific community’ which is the crucial component. It is not as if scientists decide to replace one paradigm with another and then ask themselves whether, having done so, they have made progress. A paradigm is being displaced because the relevant scientists have decided that some alternative to it is progressive , and they have decided this on the basis of the considerations integral to the science itself. Thus, viewed from within any scientific community, with its set of problems, its strict standards, its checks and balances, the result of its work just is progress.This is not quite a matter of tautology, but of understanding the extent to which, for any science, the content of any notion of progress is provided by the practice of the science itself, and by the sense in which criteria for progress just are those which count for and against candidate paradigms. A mature science possesses ‘unparalleled insulation’ from external standards just because the application of meaningful standards of assessment depends upon a familiarity with the technical complexities of the science. There is an intense collective assessment of work but this is done by the cognoscenti. The science decides both what the worthwhile problems are, and what can count as a solution to them. How can someone who cannot understand just what, scientifically, is going on (e.g. a ‘methodologist’ who is not themselves a practising scientist in the field) possibly contribute to this?

Further, saying that the scientific community judges progress overlooks the fact that the scientific community itself is defined through the replacement of paradigms, through the (eventual) marginalisation and elimination of those who are unregenerately attached to a sidelined paradigm. Thus, the scientific community is made up of the (current) victors, and they will control the history of the science, will automatically regard their triumph as the measure of progress. This is not, however, to offer any cynical view of the matter as though might simply makes right, and as though the rivalry of paradigms is a bare power struggle, for to say that would be to ignore the fact that these are scientific revolutions, and that dispute over the scientific merits of the rival paradigms is the stuff of their opposition, that the triumph consists in the reconfiguring of the science itself . So, we truly do have scientific revolutions, and Kuhn can be called ‘the philosopher of scientific revolutions’ , although he could equally well, perhaps even more so, be called ‘the philosopher of ordinary science’. but this gives no support to those in sociology who think that now Sociology (or Philosophy) can lord it over the sciences: and it gives no support to those in the Science Wars who would like to overthrow or eliminate (what they see as) the epistemological authority of science. Kuhn was right to be deeply wary of his ‘followers.’

We might gesture at -- point to -- how progress in science generally, can be indicated just in the expansion of the sciences , their division of labour, the dense content of their textbooks, and the sophisticated level of their puzzle solving. Such pointing is utterly gross and scientifically entirely superficial, and therefore quite different from being able to say, in any particular instance of paradigm substitution, in any situation where the question as to where to stand in the science is still ‘live’, what the specific features of the transition are which merit the description of the substitution as one of progress, without possession of considerable competence in the technicalities of the science in which the paradigm displacement took place. And, of course, to engage substantively in the comparison of the two paradigms would be to engage in the scientific argumentation itself , not to engage in some separate philosophical adjudication of scientific argumentation.,

(So) Kuhn is more ‘moderate’ than he has been seen, by friends and foes in philosophy and the social sciences; but he is more ‘radical’ in a wholly different direction. Radical in the way that Wittgenstein, Peter Winch, much Ethnomethodology (and perhaps much of Foucault) are radical.

We would like to close this account of SSR by sketching out a model for how to understand Kuhn’s image of scientific development,a model we seriously hope will be explanatorily/pedagogically useful.

The model starts with the notion of ‘the tree of knowledge’. This hoary old metaphor has been used time and time again to picture scientific progress. But often it is understood in quite different ways by its different proponents.

Consider for instance a logical empiricist version of the image of scientific knowledge as a tree. This tree simply grows and grows, with occasional prunings of errant branches. More and more growth – branches, thicknesses of trunk, etc. – accretes to the tree.

Now consider a falsificationist version of the image. Here, again, the tree grows and grows. Popper liked to speak of the growth of knowledge in just such ways as this. But the important thing for Popper was that most of the branches and twigs are endlessly being pruned, often in a manner which prevents further growth in a given sub-branch, and forces the tree to start growing vigorously again from a lower/different point. So, whereas for a positivist (say), the growth of the tree is mostly steady and outward, for a falsificationist all that matters is the pruning of the tree (falsifications) and the encouragement which that produces for fresh growth. (Strictly speaking, there is no positive accumulation of knowledge (growth of tree) at all, for a Popperian. The tree is a kind of a ghost, and only the prunings (the falsifications) have any substance.)

Another feature of the Popperian tree, a feature standardly missing from the empiricist tree, is that it is growing toward something. It is working its way into the shape pre-destined for it by nature. This is Popper’s controversial ‘verisimilitude’ (which we discuss in detail in Chapters 3 and 4 and 5, below; we argue that Popper should have dispensed with the idle wheel that is ‘verisimilitude’ or ‘correspondencism’). The tree is gradually growing toward its proper shape, even if it will never exactly reach it; its branches which have been pruned the most and grown the most are reaching toward the true shape of the universe. (This feature of the falsificationist picture of the growth of knowledge is of course shared by all Metaphysical Realist (correspondencist) philosophies of science.)

Now, what of Kuhn’s philosophy of science – and his tree of knowledge? The metaphor Kuhn actually chiefly uses is that of evolution: "Can we not account for both science’s existence and its success in terms of evolution from the community’s state of knowledge at any given time?" (SSR 171; see also 171-3, 205-7). Now, what happens as one goes up this tree a little way (i.e. in normal science) looks at first glance rather like the empiricist picture. But there is a crucial difference. Every so often, a twig or a branch ‘mutates’. There is a sudden growth in a surprisingly different direction (or in more than one such direction). And when this happens, not only is it sometimes quite sudden (to help us picture this aspect of the model, we might think precisely of contemporary Darwinism, for example Stephen J. Gould), but (unlike in biological evolution) it appears to alter retrospectively all that has come before it. We have to imagine a tree, then, whose branches sometimes alter their nature, mutate perhaps – and that it is very difficult then to avoid then seeing the lower parts of the tree as suddenly different than they were before. Unlike in all the received philosophies of science which it challenged, Kuhn’s picture of scientific development involves the possibility not just of forward-looking but also of backward-looking alteration of knowledge.

Thus there is pruning (selection) in Kuhn’s ‘model’ as in Popper’s; but unlike the Popperians and Metaphysical Realists, Kuhn’s quasi-Pragmatist evolutionary picture of the tree of knowledge grows toward no telos. There is accretion in Kuhn’s ‘model’, as in for instance the empiricist picture, but unlike in their picture, Kuhn’s tree radically mutates at times. And after these times, (earlier parts of) the whole tree will be implicitly/unconsciously re-read by scientists. This element of the model is unique to Kuhn. A proper view of the tree – a sound historical/philosophical perspective – will see that some lower parts of the tree are actually more similar in some interesting ways to some upper parts of it than either are to some of the parts in between (205-6). Or perhaps the metaphor works better at this point if we imagine the tree as itself more radically shape-shifting. Progress is our finding the shape of the tree more adequate to our purposes, including our purpose of having the best and most accurate science possible; but the shape of the tree long ago in some ways resembled its shape nowmore than it did somewhat recently (we are thinking here, for instance, of the shift from Aristotle through Newton ‘back’ to Einstein). Given that, what sense can be made of permanent knowledge by accretion? Or of verisimilitude? Kuhn’s ‘evolutionary’ version of the tree of knowledge shows fairly strikingly the uselessness, ultimately, of both Carnapianish and Popperianish philosophies of science…

One way of putting the reason for this is that only Kuhn (and at times Feyerabend) among the twentieth century’s major philosophers of science recognised (the nature of) scientific revolutions. Paradigms turn around (‘revolve’) and replace their predecessors. As Wittgenstein put it, in the somewhat similar case of the need for a major philosophical rethink: "The axis of reference of our examination must be rotated, but around the fixed point of our real need."

We might summarize a key moral to be drawn from the above exposition as follows:

Already one can see that Kuhn is likely to be ill-characterised, if he is termed a relativist. There are of course some passages in his (early) works, especially SSR, that might seem to explicitly affirm that he is a relativist about meaning, or about truth: we have already suggested how reasonably close interpretation/attention to Kuhn’s text and strategy serves in the great majority of cases to dispel this impression.

As we shall see in greater detail below, the relativist impression of Kuhn is even less plausible if

one reads him after going through his later work. His attack in the Structure was not meant to be on the rationality of theory appraisal and theory choice. He only contested a kind of algorithmic

rationality: the ‘rationality’ that holds that given certain data, we are always able to decide whether a

theory is better or worse than another, and if we all adopt a "rational"

attitude we must all come necessarily to the same conclusion. (And this, incidentally, is why

Kuhn introduced "values" as part of the paradigm / disciplinary matrix: there are

many factors which determine our choice, and each of us gives each factor a

different weight; thus, we can all be rational even if we don't come to the

same conclusion. In other words, Kuhn stressed the possibility of rational

disagreement in science and criticized those (such as Popper) who were

defending a correspondence theory of truth, and "verisimilitude".)

His main aim (as it is clear already from the closing pages of The

Structure) was to challenge contemporary ‘realist’ and ‘rationalist’ fantasies of science: Kuhn criticized not

the rationality of theory choice, but the epistemic (and indeed metaphysical) character of the chosen

theory (or theories). In no way can we usefully say that the theory we choose is "closer" to the

Truth, or represents a step further in our approaching the Truth, the

"world-in-itself" or what is "out there". We do best to speak of progress from what we know, and not insist that such progress is toward what we wish to know and will know. For the form of the knowledge we will eventually arrive at is likely to be deeply different from what we can come up with, if we try imagining it now, even if the ‘we’ in this case is ‘the best scientists there are’ in a given field. In this sense, then, scientific development is quite reasonably and usefully compared to Darwinian change, properly (unteleologically) understood..

Our’s is more or less a new way of seeing Kuhn. We see Kuhn as someone both much more modest than and, in a different sense, somewhat more revolutionary than, he has been (mis-)understood as being. We see him as a great philosopher; as someone who came to philosophy (of science) from outside, and revolutionised it. We think that most of his ‘foes’ and ‘friends’ only dimly sense his greatness, and try to trump it with their ‘refutations’ and ‘corrections’ – or with their ‘creative application’ – of his ideas and insights. We will try to avoid doing this – while not avoiding criticism, where necessary (and sometimes it is quite necessary).

CHAPTER THREE

When we were planning this book, we did not intend to devote much space to the exposition of Kuhn’s case studies but were forced to change our mind. Kuhn’s historical case studies are, we insist, very important to understanding the meaning of his work overall, and to getting a clear picture of what SSR actually means. We would urge those interested in knowing what Kuhn has to say about the philosophy etc. of science to read (some of) Kuhn’s historical studies, if they are able to do so, and to use this chapter as an ‘orientating device’ / companion to such readings. The two (book-length) studies we principally discuss in this chapter -- a chapter which we hope will establish securely our sense of the salience of Kuhn’s historical work to his objectives not only within but also beyond the historiography of science -- are the main ones he undertook, and they are both attempts at revisionist histories. Kuhn claims to have shown that Nicholas Copernicus and Max Planck each failed to solve the technical scientific problem that they had set themselves, and with which they were engaged when they did the scientific work that resulted in their being generally acknowledged as bringing about scientific revolutions. Kuhn further argues that neither Copernicus nor Planck actually produced the scientific achievement that is supposed to have earnt them their revolutionary title: Copernicus did not establish that the earth moves around the sun, nor did Planck actually introduce the modern idea of the quantum into twentieth century physics. In these cases, Kuhn deals with two major periods in the formation of modern science, the so-called Copernican revolution perhaps marking the beginnings of modern science and certainly of modern astronomy, the quantum revolution marking the break between classical and modern physics. If Kuhn can justify his claim that two such momentous instances of scientific change have been extensively misunderstood, then this is surely proof positive for his general thesis about the risk of misunderstanding in the historiography of scientific developments generally.

There is an almost paradoxical aspect to Kuhn’s treatment of the key figures, Copernicus and Planck. His studies are meant to do justice to each of these figures by achieving a faithful understanding of their actual contribution to science, which is to be achieved by respecting the integrity of their scientific thought. The near paradoxical aspect: in each case doing justice to them involves divesting them of the credit for their supposedly most momentous achievement. Again, we should note how Kuhn’s fame as the philosopher of scientific revolution risks being considerably misleading: a central move of Kuhn’s, as regards Copernicus and Planck and several other scientific heroes besides, is to suggest that these heroes were in central respects barely revolutionaries at all.

We say of the Copernican revolution that it is so-called because Kuhn’s argument is that the revolution in astronomy which replaced the earth-centred conception of the cosmos was only in (comparatively) small part due to anything original to Copernicus himself. In essence, Copernicus’ (vital) contribution was to give mathematical cogency to the (by no means utterly unprecedented) idea that the earth itself might be mobile, as an accidental by-product of his attempt to preserve, not undermine, most of the previous Ptolemaic scheme of astronomical thought. The Copernican revolution belonged as much to those who came after Copernicus, and these were not necessarily that enamoured of Copernicus’ own efforts: hence the actual revolution in astronomy takes place over quite a long time, and involves several other important contributors in addition to Copernicus, though even they were not necessarily motivated by the desire to promote Copernicus’ work.

Kuhn’s CR devotes relatively little attention (some fifty from the total 280 pages) to Copernicus himself. Over half the book is given over to trying to persuade us of the plausibility of the pre-Copernican astronomy to those who lived with it. That conception, essentially a ‘two-sphere’ conception of the Cosmos, produced out of a combination of Ptolemy’s astronomy and Aristotle’s physics, was one that, Kuhn seeks to show, ‘the Ancients’ were every bit as justified by their lights in thinking themselves to be the possessors of the truth about the nature of the universe as we now think ourselves as being. Over half the book is given over to trying to show

• That the Ptolemiac system was, observationally, a very successful and highly technical astronomy, with a good quantitative grasp upon the positions and movements of the stars.
• That the theoretical structure of the Ptolemaic system provided a coherent and plausible interpretation of the observational record and that
• The idea that the earth could be a planet was pretty near meaningless within the Ptolemaic tradition.

By the 4^th century B. C there was dominant consensus that the earth was a sphere suspended at the centre of a much greater rotating sphere which was the location of the stars. The sun was within the space between the inner and outer spheres. This was the 'two-sphere' model which, though not unique, became the predominant conception. (Just to avoid possible confusion, let us note that there are two different ways of using the expression ‘two spheres’. One is to talk of the earth being the innermost sphere, and the spherical movement of the stars the outermost, with Venus, the Sun, Jupiter etc. being (‘on’ spheres) in between. A different use, more associated with specifically Aristotelian ideas, is that the earth and the heavens are drastically different realms in respect of the forces which govern them -- the sub-lunar realm, including the earth, has a drastically different nature than the super-lunar realm, and these two realms (or spheres) are governed by different principles.)

Kuhn argues that this conception translates well into quite ordinary, looking-up-into-the-sky, observation, which was all that was available to observers before Galileo and the telescope, and insists, for example, that the idea of a dome-shaped sky is compatible with observation to the extent that, looking up into the sky, one sees that it does indeed ‘look domed’. If it is further conceived that the semi-spherical appearance of the sky we can see is only half of a completed sphere, then there is intellectual closure to the idea. In addition, if – as it was- the idea of symmetry is itself greatly valued, then the idea of the sphere also offers a perfectly symmetrical shape, and this could be deemed a sign of spiritual perfection.

Thus, Kuhn asserts (CR p. 30): 'In astronomy, the two-sphere cosmology (in the first of the above two senses) works and works very well.' He means, by this, that the two-sphere model systematically captures a multiplicity of the diverse geometrical relations amongst astronomical observations, as he seeks to show by working through some details of the scheme. That it is a scheme is an important fact, for Kuhn, recognition of which encourages acceptance of a crucial general point about the nature of science (which will bear – see below 000 – on the critical issue of ‘incommensurability’.) It should be borne in mind that these more or less practical considerations are what encourages Kuhn to talk about ‘conceptual schemes’. He is not, we would suggest, arbitrarily picking a term which will help him to reach a philosophical theory/position.

Conceptual schemes, on Kuhn’s view provide compact summaries of observational materials, interconnecting those that would be otherwise unrelated, and thus ease the burden on memory in that specific observational facts need not be remembered, but can be derived from the scheme. The conceptual scheme goes beyond the facts it summarises, for from it can also be derived conclusions about how (if one accepts the premises of the scheme) various other things ought to be, making it (CR p.39) 'a tool for predicting and exploring the unknown'. The two-sphere universe was sound enough as a summary of observation to be used, and an economical enough device to be still used even today, as the basis for navigational computations, in preference to the more complex, less economical [with respect to computational effort] post-Copernican scheme. At the time the two-sphere universe was also a fertile source of predictions and inspiration to researches, but then scientific inquirers could (indeed, virtually had to) accept its premises. That, of course, is no longer the case. At the time, however, the two-sphere model both fitted very well with the observations of the naked eye and seemed like a perfectly natural way to explain things (i.e. it fitted with both the observations and also with other ideas [religious, philosophical, scientific] then generally influential upon thought). The idea that the earth was in motion would then seem absurd, almost inconceivable. It is important to bear in mind that it is the sort of scientific system that Kuhn has in mind when he talks about ‘conceptual schemes’ since, as will be seen in Chapters 4 and 5 and 6, pp. 000, one of Kuhn’s most heavyweight critics, Donald Davidson, just misses this fact, with fatal consequences for his objections.

Having argued for the plausible way in which the two-sphere scheme fitted within the framework of thought at the time, Kuhn then emphasises the worm in the bud: that the two sphere scheme, best condensed in Ptolemy’s astronomy, ‘never quite worked [completely]’. Ptolemy had brought together an apparatus of ad hoc devices into

Given the two-sphere scheme, and given the importance attached to the idea of sphericity that reflects the value given to symmetry, it was natural enough to attempt to resolve the problem of planetary motion by distributing the planets amongst concentric orbits in between the inner and outer spheres. Given that the outer sphere of the Universe was a rotating spherical shell, then it would be easy enough to infer that the planets were also contained in similar shells, and this is where the physical structure of the universe comes in. Simple circular motion of the planets, however, was insufficient to capture the irregularities of observed planetary motion, and so, toward that necessity, the astronomical system acquired a further apparatus of deferents, epicycles, erratics and equants, that ‘elaborated’ on circular motion.

A deferent is a circular orbit centred upon the Earth, which a planet is following as it moves around the earth. However, it can be conceived that the planet is also involved in an additional circular movement, relative to the deferent, this circle being centred on the point at which the planet is located on the deferent. This circle is an 'epicycle'. The introduction of epicycles means that the planet traverses an orbit even as it follows the general line of the deferent, and its overall pattern of movement is not simply circular, but acquires a looping structure whose precise character will depend upon the number of epicyclic orbits the planet is conceived to complete during a complete rotation around the deferent. This basis for calculation could be used to eliminate the grossest anomaly of planetary motion – retrogression [going back on its orbital motion] -but other, lesser, anomalies remained. 'Erratics' and 'equants' were both used to reconcile the general model with observed behaviour. Erratics were deferents that were not centred upon the earth, which would, of course, give a distinctive geographic configuration to the pattern of planetary motion, whilst equants were contrived to accommodate the apparent variations in the rate of planetary motion.

The equant involved a different assumption to the one that held that the motion of the planet should be constant relative to the geometric centre provided by the centre of the Earth. Instead, the rate of motion was assumed to be constant relative to a point displaced from the Earth. It was this apparatus of ad hoc devices that Ptolemy brought into a relatively coherent scheme, but even the apparatus of erratics, equants and the rest could not regularise all the observational data.

These recalcitrant observations – which, when sufficiently worrisome, constituted what Kuhn later termed ‘anomalies’ – were not taken as a basis for throwing out Ptolemy’s whole scheme, but rather as a reason for persisting in it, in the following sense: they gave astronomers an apparently worthwhile task. Persistent efforts to refine the system, by Ptolemy and many able successors, could not engender a version of the system that ‘ever withstood the test of additional refined observation’ (73). In the words of SSR, the Ptolemaic system was a notable success, but never a complete one. In those of CR: it never quite worked.

In CR, this spawned two complementary questions for Kuhn: Given the 'success' of the Ptolemaic scheme, why was it eventually overthrown? Given the persistent 'failure' of the Ptolemaic scheme, why was it not overthrown long before its actual demise? These are the questions that arise for Kuhn from the situation as he has pictured it, but they are not ones that can be answered by the history of the scientific ideas themselves. They pertain to what he calls 'the anatomy of scientific belief' (CR pp.72-76; see also CR p.182f.), to the things that affect scientists' inclination to continue in or abandon scientific beliefs. The fact that many scientists accepted the Ptolemaic system is, presumably, accounted for by the fact that it was such an impressive achievement, to which no one had proposed a comparable [i.e. comparably impressive ] alternative, and one which was, in the absence of alternatives, prima facie persuasive. And once the basic suppositions of the scheme have been accepted, then the anomalies can seem to require only minor – albeit elusive - modifications within those suppositions to accommodate them. Apart from this general tendency to 'inertia', it was a feature of the Ptolemaic scheme that it was interwoven with the mightily prestigious physics of Aristotle.

The conceptions of motion and of the four elements in Aristotle’s physics reinforced the idea that the earth must be at the centre of the universe. Within the universe there is no vacuum, all of space is occupied by matter. The substance of the universe outside the orbit of the moon is the aether, out of which are made the planets and stars, and the set of concentric shells within which they are distributed, and whose motions propel them. The celestial and earthly domains are different, not least in that the former is a domain of perfection and permanence, the latter a realm of change and decay. The celestial realm is formed from one pure, unchangeable substance, the Aether, but the earth and its immediate lunar space is formed of four elements which (because of the moon's movements) are intermixed, rather than, as they would otherwise tend to do, separating themselves out. Within this context, we find the heart of Aristotle's conception of motion, and of the natural tendency of elements and the bodies they make up to seek their natural position -- if the four elements were not continually intermixed, then fire would have risen to the highest, outermost level, and earth the lowest. Thus the natural motion of the earthly composites is toward the centre of the universe (a universe which is assumed to be spherical) , and it is therefore in that position that the earth must reside. It would be against the nature of the element of earth to move away from the centre.

Astrology, then immensely widespread and influential, as well as Aristotle’s physics, backed up Ptolemy’s scheme: astronomers and astrologers were often one and the same, for astronomical observations were used to construe the significance of the heavens for life on earth. In short, there were, at the time, plenty of well entrenched reasons, in science and in religion, to find the two-sphere world view entirely credible, and though people would, even then, propose the idea of a moving earth, they could not offer the kind of rationale for it that could disturb this mutually reinforcing complex of reasons behind the Ptolemaic scheme.

The passage of many centuries before the ‘rediscovery’ of the Ptolemaic tradition, after the long decline in learning between 2 B.C and the 12^th Century, loosened the interconnections between these mutually supporting elements.

The rediscoverers laboured under misconceptions about the historical depth and diversity of 'Ancient thought', and thus were apt to treat temporally remote and intellectually very different traditions as if they were elements in a single system, with divergences between them being looked upon as logical discrepancies (See Chapter 4 of CR). Thus, for example, the mutually supporting interconnection of Aristotelian and Ptolemaic thought was eroded in connection with astronomy, where the qualitative character of Aristotle's arguments was seen to be in conflict with the quantitative attainments of the Ptolemaic tradition. The rediscovery further led to the incorporation of the Artistotelian cosmology into the Christian one, though there were already critics of Aristotelian astronomy, whose work anticipated Copernicus. But they did not then gain much recognition, nor achieve any great impact, until after Copernicus. This, plus the intellectual turmoil created by the wide ranging and multifarious social changes of the Renaissance period provided a context in which there could be reduced resistance to some fundamental rethinking because of the way the turbulence was loosening the hold of established ideas generally. It also created conditions that would ensure receptiveness toward Copernicus. Indirect 'humanist' influences upon some natural scientists (including Copernicus) inclined them toward a belief in the importance of mathematics in understanding nature, and a view of the Sun as 'the source of all vital principles and forces in the universe' [ref.?]. This had affinities with the rather mystical views of mathematics and about the sun as an expression of deity which were derived from Plato by some of the philosophical opponents of Aristotle.

It was largely not internal developments within astronomy, then, which triggered the first stage of the Copernican revolution, but such diverse historical and social changes in conditions.

'[T]he very process of rediscovery, the medieval integration of science and theology, the centuries of scholastic criticism, and the new currents of Renaissance life and thought, all had combined to change men's attitude toward the scientific heritage that they learned in school. Just how great, and yet how strangely small, this essential change could be we shall discover' (CR 132, emphasis added).

Copernicus’ own intervention, according to Kuhn, was not meant to overthrow the Ptolemaic system but essentially to restore (and improve) it. The very attempts of Ptolemy and his followers to make their scheme a complete success had attenuated the integrity of the whole, effectively tending to disintegrate it into a plurality of different schemes, thus comprising a scientific scandal. Copernicus wanted to reunify the Ptolemaic system by making relatively minor adjustments of a mostly mathematical character to it. The proposal that the earth be allowed to move, that the earth be reconceived as a planet, was not necessarily intended as anything other than a purely mathematical step to effect a closer fit with observational data on a more mathematically coherent basis. Neither Plank nor Copernicus intended the step that earned them their revolutionary reputation as a serious empirical hypothesis, only in the first instance as a device to achieve a technical solution, namely, to get rid of the ‘equant’ which Copernicus regarded as one ad hoc device too many. The presumptions which had originally held the Ptolemaic system in place had, as we have said, been loosened by social etc. change in Europe after its rediscovery, but, in any case, Copernicus was not in a scientifically-significant way restrained by these changes says Kuhn, because they were external to his very narrow and specific focus. This focus was on precisely what it would take to get the mathematics right, without thought for any further consequences or their perturbing effects.

Copernicus had, then, a quite a specific problem within the Ptolemaic scheme, the problem of the planets, i.e. getting the formulae of the system exhaustively to capture their apparent motion. This was, says Kuhn, both a highly technical and apparently petty problem, far removed from the everyday life that it was eventually to affect significantly. But if it was a petty problem, why was Copernicus making such an effort with it? Kuhn’s answer: whilst it might be a small anomaly ‘in itself’, it could be an intense irritant to someone of a mathematically precise turn of mind. It made the astonomical system seem ‘monstrous’, and generally unsatisfactory.

The innovative aspect of the Copernican system over the Ptolemaic is dealt with in only five pages, and these pages are not all that complimentary. In respect of cosmology, Copernicus’ system adhered to the two-sphere universe [in the first sense only]. And one could dispense with the major epicycles if 'retrograde' planetary motion transformed into a merely apparent phenomenon resulting from the orbital motion of the earth.

Copernicus’s supporting arguments for his proposal were not very adventurous. They largely align him with the Aristotelian tradition, from which, in proposing that the Earth be considered to move, he makes only very limited deviations. Indeed, he sought to make out that the proposal of a moving earth was an application of the core principle of the tradition, that spherical shape is intrinsically associated with motion. If, then, the spherical shape of the Earth is shared with the celestial bodies, why should not the Earth also share in the ubiquity of circular motion? Nor were these arguments prima facie all that convincing: Kuhn virtually sides with those who made mock of Copernicus, for the weakness of the previous supporting arguments, and further argues that Copernicus’ model was no more than arguably more economical than Ptolemy's. Copernicus might dispense with major epicycles and with equants, but he retained epicycles and erratics, and required as many circles (over 30) as did Ptolemy to achieve results which were themselves often only approximations to observations.

The real advantage that the Copernican system initially had was not an astronomically practical one, but - Kuhn holds - mainly aesthetic in nature. The geometrically neat and coherent account yielded by Copernicus’ sun-centred system, would appeal to those who could recognise that neatness. This particular strength (most crucially in making the order of distribution of the planets and the relative size of their orbits calculable from observation, without the addition of further, rather arbitrary assumptions as required in Ptolemaic astronomy) appealed to only a few astronomers, but gave them the motivation to develop Copernicus’s work into the simple and accurate solution that he had to some extent wrongly claimed to have presented.

The place of the planets within the 'two sphere' scheme was the critical ‘moment’ upon which Copernicus made his intervention. We can see, here, something that might tempt Kuhn into some later forms of expression that proved to be hostages to fortune, but we can also see why these locutions might have seemed very useful. We could [and not falsely] say that Copernicus' astronomical achievement was to make the Earth a planet. We could say [again, not falsely]: prior to Copernicus, the Earth was not a planet, but after his work was accepted, it was. If the [deflationary] voice or tone in which such a suggestion might be made is appreciated, then it will be entirely clear that Copernicus is not being credited with a physical transformation of a body, with making a heavenly body go through some kind of physical transformation, turning it from one kind of physical thing into another. Copernicus is being credited with a change to the outlook of astronomy, with altering the way in which we identify something: with a fundamental reclassification (in astronomical terms) of the Earth, with making thinkable what had previously been unthinkable (and, pretty soon, vice versa).

Thus, before Copernicus, the Earth was not counted as a planet, it did not satisfy the current criteria for classification as one. The planets were then identified not by their material composition, but by the pattern of their motion; 'planet' meant 'wanderer', and the movements of the planets, relative to those of the stars, were wandering movements. Since the Earth was the fixed centre of the universe, since it did not move, it did not wander and so could not be a planet. Some of the Ancients, including Aristotle, held (for good reason) that the Earth was a sphere, but not a moving one. The Earth, being at the centre of the two sphere universe could not move. Thus, in the pre-Copernican scheme, the Earth was not a planet. The effect of Copernicus' proposal to view the Earth as moving would be to change its fundamental classification; it changed from being (in the Ancient scheme of things) a body that did not move, to one which, like Saturn, Jupiter, Venus, and others, did move. It had ‘become’ a planet.

But why use this form of expression at all, for it surely does dangerously offer hostages to fortune? Well, this form of expression does provide a thumping emphasis on the point that Kuhn wants to make about the difference between the pre- and post-Copernican ages: in the earlier age there was rock solid confidence that the earth was not and could not be a planet, whilst in our own time there is equally solid confidence that it is a planet. On such rocks is science built.

Eventual publication of Copernicus ideas in the year of his death did not precipitate any immediate and strong reaction. His work was largely inaccessible to those without technical astronomical competence (see CR 185), and amongst those it could be recognised as an impressive achievement, but that was not necessarily enough to encourage adoption of its radical proposal. Copernicus' work and techniques could be used without accepting that the Earth really did move, and over the next generation they were to find increasing use amongst astronomers, this further reducing resistance to the idea of a mobile Earth.

Copernicus could argue that the mathematics required for his calculations were compatible with the view that the Earth's orbit was at around or near the centre of the spherical universe, but, this had a knock-on mathematical, and therefore, eventually, astronomical, consequence; it required a considerable increase in the ratio of space between the outermost planet and the stars. The occurrence of a vast gap between the outer planet and the stars effectively deprives the nested shell version of the universe of it’s (the neatness of) its rationale (but does not refute it, note), and gives the opportunity to raise a question as to the rational purpose of so much empty space. Copernicus had provided a basis for rendering the two sphere conception problematical, but it was down to others to raise questions against it, ones that Copernicus himself never explored, nor was necessarily even aware that he had made it possible, and eventually pressing, to ask.

Copernicus’ successors (over about 150 years) brought out these implications and brought about the downfall of the Ptolemaic system. Tycho Brahe opposed the idea of the earth's motion, but both his observational work and his investigations of transient phenomena such as comets further eroded the authority of the traditional cosmology of the unchanging heavens. These latter observations did not depend upon any astronomical breakthroughs, and could have been made long before. In the new context, they acquired a significance they did not have before. Kepler, a convinced Copernican (and, like Copernicus, one of NeoPlatonist persuasion), was critical of, and rationalised the scheme's structure. Seeing an inconsistency between the residue of traditional astronomy which retained a somewhat special place within the system for the Earth, and the main achievements of the scheme, Kepler reworked the mathematics to give equivalent treatment to all planets, thus producing a simpler and more accurate scheme. Attempting to rise to the new, higher standard of observation set by Brahe, Kepler eventually found that the solution to many outstanding problems arose from replacing the circular motion (which Copernicus had held as dear or even dearer to his heart than had his predecessors) with elliptical motion. At last the epicycles and erratics could be dispensed with. With Kepler, the Copernican revolution was nearly ‘complete’; Kuhn finds its final completion in Newton’s system.

Galileo's introduction of the telescope into astronomy provided (we can say, retrospectively) a final blow against the Ptolemaic tradition as an equal contender in the debate. Kuhn argues, though, that the observational evidence produced by it did not provide genuine independent evidence for Copernicanism (and added little over the following hundred years or so, as far as the technically proficient were concerned, that was more convincing that what was to be shown/seen in Kepler's tables). It provided powerful propaganda for the emerging traditions. That evidence could perhaps have been rendered compatible with the Ptolemaic system, but the heart had gone out of that system, and the effort required to square Ptolemaic astronomy with the new evidence often made it seem easier just to go over to Copernicanism. Opposition to Copernicanism did not simply collapse, but persisted, and only gradually faded away over the 150 years after the death of Galileo in 1642.

Kuhn has thus tried to demonstrate three major ‘incongruities’ in the case of Copernicus:

• that such narrowly focussed mathematical preoccupations could and did have such far reaching scientific and even socio-cultural consequences (143)
• that the Copernican revolution as we know it is hardly to be found in Copernicus’ own writings (155) and
• that Copernicus work could not have triumphed over Ptolemy’s on the grounds that it was more accurate, more consistent , and less unnecessarily complex since it was itself inaccurate, overcomplicated and just as inconsistent.(171)

The Copernican Revolution accessibly provides Kuhn’s first in-depth account of how the image of science by which most extant history, philosophy and popularisation of science are possessed is badly off, insofar as these three incongruities (and more besides) are not reckoned with. The Quantum Revolution book, written nearly a generation later, and after the fame of Structure, but forbiddingly technical and austere, seems on casual inspection to be a very different kettle of fish. Is it?

This is another piece of revisionist history. Again, it is meant to re-evaluate a prevailing judgement on one individual, in this case, Max Planck. According to, for example, Isaac Asimov’s popular history of physics

This states just the position Kuhn is out to refute: 1900 was not the dividing point between ‘classical’ and ‘quantum’ physics, and Planck’s theory did not, contrary to Asimov’s suggestion, introduce the idea that energy is discontinuous. The story is, in many ways, the same as that of Copernicus, of a scientist who sought to solve a specific problem and failed to do so, but who, in the attempt to find a solution, was driven by technical necessities to resort to a particular step – the introduction of an idea, ‘the quantum’ - which he did not himself take fully seriously, regarding it as a temporary solution to a still unresolved difficulty. It fell to others subsequently to take the steps that would introduce the modern idea of the quantum into physics, an idea which Planck himself found it hard to accept. In this case, though, and probably largely because of the much greater degree of specialisation, mathematicisation, and use of technology in high science three hundred years and more after Copernicus, any emphasis on the wider cultural environment of Planck’s thought is altogether diminished, and attention is entirely focussed upon the course of Planck’s own struggles with his problem, and of the scientific materials that he drew upon in grappling with it, as well as relevant developments in the wider science. This, at least, is the matter of the first main part of Kuhn’s study, the second part being concerned with the aftermath of Planck’s ‘black body’ work so as to show how, in physics, the quantum idea actually emerged and took hold, and to show how Planck’s subsequent work demonstrates his difficulties with the idea of the quantum. The credit for its introduction, if one has to choose one person to give the laurel to, having, actually, to go to Albert Einstein.

Kuhn offers this dilemma for the prevailing view of Planck’s achievement: either one can hold that the idea of the quantum was the one present in Planck’s work of 1900 or one can accept that it was not present, and that this idea was later introduced by Einstein. In either case, Planck must lose credit for its introduction, for if it was present in that work, then this would be an idea that Planck did not originate, but which he picked up through using the work of a distinguished predecessor, Boltzmann.

The black-body researches were the means Planck used to come to grips with what he regarded as the real problem, that of Maxwell’s demon. In accord with Kuhn’s general thinking, Planck was not seeking fundamental novelty and like Copernicus, was setting out to take measures which would sustain, not challenge, the assumptions of classical physics. It was Planck’s expectation that Maxwell’s demon could be reconciled with classical physics, that the ‘threat’ which it posed was not a real, but rather a purely theoretical one, and that it would, therefore, eventually, if not necessarily easily, be shown to be compatible with the classical framework.

When Kuhn published, some thirteen years after SSR, his book on the topic, The Black-Body Theory and The Quantum Discontinuity 1894-1912, those who had enthusiastically awaiting it were often disappointed. The book’s contents certainly looked as dry-as-dust as its title, and the book is relentlessly involved with pretty technical physics in a fashion very different even to CR. Anyone looking for lively and accessible polemics to follow up SSR would not find them, nor would they find even the jargon of SSR in this new book. The key words are just not there. However, all the ideas from SSR are present [even if Kuhn had to write a paper just five years after the book to explain how this was so.] We mention this now because it should be clear, given our account above of SSR, that Maxwell’s demon was or at least can now be sensibly regarded as an anomaly, as an occasion for research, and just possibly for re-tooling. Here is a respectable piece of scientific work which does not work out the way that, in the framework of classical physics, it should. It provides Planck with a challenging opportunity for puzzle solving. Though there must, in the framework of classical physics, be something wrong with Maxwell’s arguments, Planck cannot see what this is. As remarked, he does not think the problem one which requires the re-thinking of classical physics, for the difficulty it represents is one which seems very inconsequential to the physics, but Planck is not content to set the worry aside: he wants to dispose of it in a principled way. And this is what he tries to do. And what he actually fails to do. Quantum physics originates in rejection of the idea that a principled reconciliation of classical physics and Maxwell’s demon is possible. Thus, Maxwell’s demon poses a highly technical puzzle that deeply troubles someone who is unhappy with the lack of a rigorous solution to a principled problem.

‘Maxwell’s demon’ is a paradigm in the exemplar sense, a ‘solved problem’ … but one which offers a solution that is at odds with the prevailing paradigms, particularly the laws of entropy. The new [quantum] paradigm develops the idea that matter be considered discontinuous, that it be conceived of in terms of discrete particles. It thus conflicts with the prevailing idea that matter is continuous. The idea that matter was made up of particles was itself one that developed within classical [i.e. pre-quantum] physics, but in a way which kept it consistent with the idea that matter is also continuous, for whilst matter may be made up of particles, those particles themselves are embedded in the ether which fills the whole of space. Working out what the assumption of particulate matter might mean, Maxwell produces the kind of solution which is not acceptable in the contemporary physics as an acceptable solution, for it is statistical in nature. It can, for Planck, be only a half-way house on the road to a proper explanation that will be given through ‘mechanics’, through the examination of the way in which constituents of matter interact with one another in a causal, and strictly determined, way [the assumption that this kind of explanation is the only proper, acceptable kind, being exemplary of the idea of paradigm, this time roughly in its disciplinary matrix aspect, in the deep or ‘meta’ commitments of a given discipline, or thought-collective]. In the ideal case, knowing the initial positions of all the atoms composing some body, gas or liquid, assuming that body, gas or liquid to be isolated from all external influences, and knowing the laws which govern the behaviour of those atoms, one could [in principle, at least] determinately predict all its subsequent states.

Treating heat as a matter of atomistic interactions, of the behaviour of molecules, Maxwell created a thought experiment: imagine a demon who regulated the exchange of molecules between two bodies, as though controlling a pipeline between them through which the molecules must pass from one body to the other. The internal composition of each body is to be understood as being composed of a distribution of differentially energetic molecules, some of which are ‘hotter’, i.e. more energetic and faster moving, than others - a hot liquid is not at uniform temperature throughout. The average molecules will obviously provide a great preponderance of those making up the liquid, but there will be ones which are hotter or colder than the average. The demon could, therefore, open and close the pipeline selectively, such that when the ‘hotter’ molecules in the colder body approached the pipeline, those would be let through to the hot body, whilst, reciprocally, only the ‘coldest’ molecules would pass to the hot body from the colder one. The overall effect would be that the temperature of the hot body would rise, and that of the cold one fall, in contravention of the second law of thermodynamics. This law insists that such a transfer of heat can never happen. Maxwell’s thought experiment entails that because the number of ‘hot’ molecules in the cold body and of ‘cold’ ones in the hot body must be considerably fewer than the average, then the odds against this contravention occurring by natural processes and without the intervention of a demon must be very, very long indeed. However, extraordinarily long odds against is not the same as being ruled out as impossible by a law.

The fact that the possibility the thought experiment allows is very remote means that Planck regarded it as something that would never happen, and as something that resulted only from idealisations treating of a limiting case to the argument. But still, the logic of Maxwell’s argument from the idea of particulate matter looks pretty sound, and so Planck does not just set the problem aside: there must be a proof in physics, rather than by statistics, that it is wrong.

Planck sets himself conditions under which the proof is to be achieved. First, he will give the proof in terms of ‘conservation laws’ which then governed energy-transfer and which are ‘reversible’ in the sense that it makes no difference to the laws in which direction a process is moving, the equations governing interactions ‘look the same’ whether two molecules are moving toward a collision with each other, or bouncing away from each other after the collision. Planck’s ambition was to establish in terms of those ‘reversible’ laws a proof that the process of heat transfer from the hotter to the cooler body is an ‘irreversible’ process, one i.e. that the colder body cannot get colder, nor the hot one hotter, though the logic of Maxwell’s argument allows this ]. Thus, the form which Planck’s task of proving the irreversibility of entropic processes took became that of showing why the time reversible equations did not, in actual physical cases, apply in that way. The laws themselves were reversible, and so there was nothing intrinsic to them directly to rebut Maxwell’s argument. This was the first of two constraints Planck imposed upon himself, the second being that in the black-body work was that he would make no ‘special assumptions’ about the constituents of matter, that, in other words, his proof would in no way depend upon assumptions about the nature of constituent elements, other than that they were particulate. Thus, again in accord with Kuhn’s ideas about normal science etc., Planck is setting technical and high standards for his solution, is giving himself a very difficult puzzle.

The connection between Maxwell’s demon and the black-body problem, as mentioned above, is the second law of thermodynamics. That famous law relates to the absorption and emission of light, and arises in connection with consideration of the quantitative relations between the temperature of a body and the amount of energy (including light) radiated by the body as it is heated. The 'black body' itself is a thought-experimental tool, proposed as a polar condition for understanding the relationship. The 'black body' would be one that would absorb all the light at all frequencies that fell upon it and would reflect no light at any frequency. If the body is rendered incandescent, then at that point it would release all the light which it had absorbed in all of its frequencies. The problem was to work out a quantitative expression of the relationship between the distribution of light amongst its various features, and the temperature of the radiating body. It was in this connection that the black-body research became of interest to Planck, for if a black-body cavity [a closed body] containing energy waves is isolated from its environment then a stationary state must set in, one which cannot be further changed without effects from the environment (and which cannot, therefore, be reversed, for that would require a change to start the reversal off). However, energy waves governed by Maxwell’s equations would not of themselves reach an equilibrium, and it is only through the introduction of a ‘resonator’ i.e. something (an imaginary physical entity) which resonates, absorbing energy from the waves around it, and emitting energy [in a transformed state] back into its environment, that the possibility of the equilibrium could be theoretically demonstrated. Planck needs the idea of the resonator in order to enable the application of equations from mechanics to the continuous medium of air.

Incidentally, but decisively, it fell to Planck to prepare a colleague’s work on ‘gas theory’ for posthumous publication, and the fact that gases were conceived as having an atomic (molecular) structure and could, therefore, be understood in terms of (determinist) mechanics, offered resources for Planck’s thinking about the black-body problem, especially in drawing the statistical work of Ludwig Boltzmann to his attention.

The heart of Kuhn’s argument is that it was Boltzmann’s statistical work that led Planck into formulating his quantum idea, but which also misled him as to what he was actually doing. Though Boltzmann’s statistical ideas (which brought out the essentially probabilistic nature of the phenomenon) enabled Planck to persist in his illusion that a reconciliation within the terms of classical physics could be found, Boltzmann himself expressed his statistical ideas in a classical and determinist way, thus obscuring from Planck the extent to which, using those statistical methods, he was operating inconsistently with his own other assumptions and (later) results.

Boltzmann (working out a formula for calculating the movement of molecules in a gas) computed in a way incongruous with his actual problem, calculating as if working from a non-statistical mechanics, in which the position of each molecule was initially known, and where the subsequent distribution could then be uniquely calculated. However, the initial distribution of molecules was not a real classical initial distribution, but a ‘coarse grained one’ (BB, 45). There were an infinite number of different ways in which the initial distribution of the molecules in a gas could be specified, and each of these would lead to a different outcome in calculating any later stage of the distribution. Boltzmann’s equations do not give actual values for particular molecules, but only average, or most probable, values. Boltzmann came to realise this, at least to some extent, but did not recast his way of putting things, stating them as if they gave fully classical, rather than purely probabilistic results. Boltzmann had thus conflated two levels of operation, and so simplified calculation considerably, calculating the positions of molecules by treating them as being located in ‘cells’ [i.e. volumes which can contain a large number of molecules], thus evading the need to specify the position of each individual molecule:

‘only by moving subconsciously between these two ultimately independent conditions was Boltzmann able preserve for so long his predominantly deterministic way of discussing [his theorem]’ (57).

Thereby, he also misled Planck, and it was not (or so Kuhn insists) until after 1906 that Planck came to realise that under quite usual physical conditions the distribution of molecules within cells affected the results he wanted to calculate – but, of course, having used Boltzmann’s method, the need to make calculations about the distribution within cells had been bypassed. Because of the way they conflated average distributions with actual ones, both Boltzmann and Planck understood Boltzmann’s formulations as specifying actual, rather than most probable, distributions for molecules and therefore as tracing actual, rather than possible interactions between them [thus not seeing that the calculations were essentially statistical, not determinist at all].

By 1897, Planck was coming to realise that the electro-magnetic field equations he had been developing on the basis of Boltzmann’s example, would not give him the non-statistical proof of irreversibility without suitable initial conditions being specified [meaning that he would be going back on the requirements he had set for a solution to the problem]. In attempting to work out his equations for energy waves in a black-body cavity, Planck had found that he the mathematics he was using would not allow him to work out the equilibrium (that could only be disturbed by an external influence) for the black-body considered as an empty volume. To get a solution, Planck hypothesised ‘resonators’, imaginary devices which would receive and emit energy, for this would allow him to work out the solution he sought. However, in 1898 he found himself forced to go back on his requirement of no special assumptions, introducing a notion of ‘natural radiation’ which achieved the effect of ruling out configurations of microstates (for resonators in a black body cavity) which would otherwise, like the operations of Maxwell’s demons, allow for the reversibility of the tendency toward increasing entropy.

Having adopted a formulation - an entropy function - which would allow the barring of some statistically possible micro-distributions as physically impossible, Planck thought he faced only one outstanding difficulty for the full solution of his problem. He needed to prove that his solution was a unique one, that there were not a multitude, even an infinity of other, equally valid computations which would yield different results. Until 1899 he was convinced that the function was unique but lacked strong proof of this. Planck’s problem changed, under pressure of increasingly refined experimental results, from that of proving the irreversibility (as described above) toward that of articulating the radiation law that he had initially formulated with those results produced by actual experimentation, not just the thought-experimental kind. He could comparatively easily adjust his formula, but, in doing so, made it ad hoc , leaving himself bereft of any strong derivation of the formula’s results from theory [when it was, of course, the whole point to provide a thoroughly principled, not an ad hoc, derivation].

Planck’s introduction of resonators into the black-body space had come under criticism and Planck himself now came to see that it presented him with a problem. He acknowledged that his procedure would only work for cases of more than one resonator. If the requirement that the atomic constituents were independent of each other was to be fully satisfied, then his proof should work for the single case [i.e. that the constituents were independent would mean that the fact that there were or were not other atomic elements would not affect the behaviour of one of them]. That his proof did not work for the single case, then, meant that the resonators in the multiple cases could not be considered independent, but this was inconsistent with the second of the two constraints he had set out for his work, that he would make no ‘special assumptions’ about the elements involved, and if that requirement was to be stuck to, then it should not matter whether there was one or more atomic element involved.,

Rethinking his position, Planck needed to consider how the total energy available to the resonators in the black-body was distributed amongst them. We now come to the point where, if anywhere, Planck introduced the idea of the quantum. His way of working out how the total energy (E) was to be distributed amongst the resonators resorted to Boltzmann’s statistical methods. In order to apply this method, whose details need not concern us here, one must subdivide the energy continuum into units of finite size, but the size of the energy elements into which the continuum must be subdivided cannot be arbitrarily set as though they were picking out just any level on a continuum of possible frequencies. These needed to be fixed proportionately to the frequency of the energy waves. Through the identification of ‘h’, a constant, later known as Planck’s constant, and frequency (v), Planck contrived the energy element hv, which element could be divided into total energy, E, to give the energy elements to be distributed over the resonators. It is here, if anywhere, that Planck came closest to breaking with classical physics. He found that his calculations of energy levels would take only integral values. These could not be distributed at all and any points across a continuum, but could only be allocated to certain discrete levels. Kuhn maintains that Planck has been misunderstood as carrying out his work in the same way as Lorenz. Working rather later, Lorenz did indeed use an unequivocally quantized conception- i.e. one which says that the energy levels themselves are discontinuous,but the whole point for Kuhn is that this conception is not present in Planck’s work and had only been read back into it. The fact that Planck’s underlying concept was not the same as Lorenz’s later one had been obscured by Planck’s adoption of a shortcut to avoid having to work out the distribution over resonators for all frequency levels, not just for one, this being a very cumbersome exercise. Thus Planck, as well as his readers, remained unaware that the actual problem he had solved was not the same as the one he was trying to, not that of distributing total energy over a number of resonators at a single frequency, but rather of distributing the energy over a totality of resonators vibrating at different frequencies. Neither Planck’s contemporaries, nor his subsequent readers have, therefore, been previously able properly to clarify Planck’s conceptual reasoning at this juncture.

That the energy levels are discontinuous seems to be the quantum idea itself: why, then, does Kuhn deny that it is?

The core element of Kuhn’s case is that the claim that the results of e=hv were restricted to integrals did not represent the post-classical quantum. Kuhn certainly cannot avoid certain passages in Planck which could be read as if the energy elements really are quantized. There are passages in Planck, Kuhn admits, where it seems that Planck does indeed literally use the modern quantum idea However, Kuhn tells us in a most unusual manoeuvre, ‘fortunately for the consistency of Planck’s thought these passages need not be read literally’ (128). Against the background of Planck’s general and persistently classical-in-nature way of thought, and in light of Planck’s lectures of 1906, there are grounds for insisting ‘that they should not be’. Kuhn’s way of understanding Planck is the first to render his (Planck’s) own intellectual development … continuous, consistent.

Kuhn holds: Planck was not really giving up on the conception of the energy spectrum as a continuum in favour of it as a series of discrete states, but was only attempting to simplify his statistical computations by describing that continuum in discrete terms (130). For Planck the relationship e=hv might entail the subdivision of energy levels in integral terms, but it remained a means of subdividing a continuum. At the same time, however, it also manifested a truth about the world. The facts of nature were such that only these energy levels were possible, that was sure enough; but this could not be, for Planck, the final position. There remained a need to understand how a continuous nature could yield such discontinuous results, and it was Planck’s hope that this would be resolved by a better understanding of the microscopic energy emission process, and thus, through the newly developing electron theory [which would give physical reasons why the values were discrete even though the phenomena were not].

Planck’s hopes could not have been fulfilled by electron theory, Kuhn claims, but Planck could maintain the illusion that there could be a classical solution to the radiation problem, because this hope was sustained by the errors in his own reasoning, about the distribution of the resonators across the cell divisions in the volume of the black-body’s cavity, that allowed for only some of the locations within the boundaries of a cell to be available to his resonators.

There is much more in BB than this re-examination of the logic of Planck’s own work, as Kuhn seeks to show both how the modern idea of the quantum originated after 1901 ( when Planck had abandoned work on black-body radiation for the time being, at least) and to show, too, that Planck had some difficulty in ingesting that idea when it was developed.

It was two physicists, Albert Einstein and Paul Ehrenfest, working independently of each other, the latter critically re-working Planck’s black-body material, who really brought in pretty much the idea of the quantum, as we know it. Einstein provided a basis in physics for Planck’s results:

arriving at the requirement through his own independent line of inquiry, initiated and pursued without reference to Planck’s black-body work, Einstein saw that that Planck’s theory, ‘properly understood’, required his (Einstein’s) own light-particle hypothesis to explain radiation in the higher frequencies. A key moment in Einstein’s thought was that high frequency radiations may behave like a collection of particles, with Einstein’s formula for the energy of these particles turning out to be the same as that for Planck’s energy elements. This provided the basis for Einstein’s reinterpretation of Planck’s theory, which, he concluded had not been compatible with classical theories, and required a break with this, though

Einstein famously remarked that the fact that beer is sold in bottles does not mean that beer exists only in bottle sized quantities. This is pointing out that Planck’s equation allows only discrete quantities of energy, but that this does not, of itself, imply that energy exists in discrete quantities.

However, though Einstein and Ehrenfest had delivered the quantum concept, it was not so obvious to physicists that it was instantly taken up. The two figures were too junior, and even though Einstein was rapidly becoming an influential figure, his prestige was not yet such as to convince many physicists of the merits of his light-particle hypothesis, and the association with this of the quantum idea actually discouraged also the acceptance of the latter:

One such was H. A. Lorenz, who came to see that the idea of a elementary quantum of energy might serve to make sense of Planck’s formula, but Planck’s theory, as it stood, seemed to require that his resonators absorb and emit energy in an entirely continuous way. He questioned Planck on this point, and drew from the latter his ‘first known concession of the need to restrict resonator energy’ (194). Not only was Lorenz already a considerable figure, with acknowledged expertise in the relevant field, but his version of the arguments avoided certain difficulties which afflicted those of Ehrenfest and Einstein. By conclusively eliminating the previously proposed mechanisms for redistributing frequencies - namely, moving resonators and colliding molecules - he made electron theory seem to be the only basis for deriving Planck’s law.

But even having accepted the need to restrict resonator energy levels, Planck was still reluctant to admit the necessity for any more than a minimal break with classical physics, though by 1910 he had ‘at last’ become

From 1907 and increasingly after 1910, the quantum idea began to take off, and the number of physicists working on it, and the number of areas they were working in both expanded, whilst the interest in black-body researches themselves declined. It was, Kuhn avers,

Planck reluctantly came to terms with post-classical ideas to some extent, attempting to incorporate the new developments with respect to the quantum into his own thought through the production of a second theory of radiation. Here, again, Kuhn’s account is revisionist. Planck’s contemporaries and other historians have seen, in this later work, a retrograde conservatism by comparison with his earlier, turn of the century, revolutionary radicalism, Kuhn sees rather the personal radicalism of a conservatively inclined individual. Planck is only (after 1910) attempting to take the steps that he had previously sought to avoid, but that had now been taken by others and had imposed themselves upon him, and had given him ‘a new perception of his achievement in the area he had made his own, the electromagnetic theory of black-body radiation’ (311).

Though forced to admit discontinuity, Planck still did not find easy the idea that energy did not comprise a continuum. First, he sought to incorporate the discontinuity by proposing a threshold level for absorption of radiation, but revised that into the view that the discontinuities were in emission rather than absorption. Scientists seeking to understand the nature of the quantum were often influenced by Planck’s theory, at least until Nils Bohr’s work on spectra showed that ‘an identical process at work in absorption and in emission’ (252) and thus precipitated the second theory’s gradual disappearance.

Though taking away Planck’s status as founder of quantum physics, Kuhn nonetheless deems Planck’s two ultimately unsuccessful theories of radiation to have been consequential, playing an important role in its creation, by giving others the confidence to proceed in the new direction and to go beyond Planck’s own ideas themselves. It was, therefore, a collaborative effort, an extended, not an instant, revolution (as usual). Planck’s own theories had not

but that still meant that Planck had been a primary contributor to the development of a theory that (ironically) ‘he never came quite to believe.’ (254)

Though the terminology of SSR is absent from BB, it should be clear that all the ideas are present, and that it, together with CR, provides clear substantiation of the arguments of SSR. If what we say is the case, why did Kuhn avoid this vocabulary? For two main reasons, we think: to avoid the kinds of misunderstandings that he had so much encountered of words such as ‘paradigm’, and, more generally, to keep himself out of a straitjacket. But Kuhn wasn’t happy with the general presumption that BB had nothing to do with or even contradicted SSR. Within five years of publishing the book, Kuhn had to write a paper, republished in the second edition of the book, to point out the connections with SSR and to explain himself. He does not want to jettison the ideas of SSR , though neither does he want them to become a set of rigid preconceptions, to be imposed on the historical data:

Planck’s ‘conservatism’ was not some reactionary posture, but, as Kuhn’s whole book seeks to show us, a deeply reasoned and entirely reasonable response to an intriguing and at the time, purely technical, challenge, one which, so far as he could see, had to be dealt with by being disposed of rather than accepted on its own (apparent) terms. Maxwell’s demon and, subsequently, the experimental results on cavity radiation, with the variation in the release of high frequency light provided classic, and to Planck, nagging puzzles.

His motivation is very plainly, at least in Kuhn’s account of it: puzzle solving. Planck was trying to produce a satisfactory solution to these unexpected anomalies, trying to satisfy his own requirement of avoiding special hypotheses; and of forming the solution out of ‘conservation’ laws (??), showing that essentially reversible equations could nonetheless be used to yield a proof of irreversibility, attempting to adapt techniques developed in the theory of gases to the case of thermodynamics, working on the problem theoretically, but responding to experimental evidence, and to the objections of critics, trying determinedly, and over several years, and by different means to reach this solution. Planck was a normal scientist - a beautifully ambiguous sentence, true in both its meanings, after reading Kuhn. I.e. Planck was a normal scientist, one like any other, just a brighter one who could be said to have helped the community ‘sleepwalk’ into a revolution, but he was attempting to practice normal science too, assuming that the problem posed by Maxwell’s demon must have a solution within the terms of the prevailing paradigms. Kuhn thus shows how the actual concrete work of normal science is not something starkly contrastive with revolutionary science, but something that can merge into it. The ‘critics’ of Kuhn’s supposed ‘dichotomy’ between normal and extraordinary science should read his corpus better before taking themselves to have refuted Kuhn.

So: Like Copernicus, Planck was judged by Kuhn to have been to a greater extent than previously realized a failure – he had not solved the problem that he had intended to solve, had not succeeded in giving a proof of the irreversibility of the law of entropy in terms of conservation laws, and had, indeed, only been satisfied with his achievements on the basis of a misconception about what he had actually done. Again like Copernicus, the revolution which Planck has/had been credited with, and one which had been named on the basis of the term that he had introduced – the quantum revolution – was largely not his achievement at all, but that of those who came after him. The use of the same term, ‘quantum’ had fatefully misled both contemporary scientists and subsequent historians into supposing that it signified the same idea.

Bohr’s Atom:

Also worthy of mention as a kind of ‘supplement’ to the black-body book, is the account, written with John Heilbron (1969), of the development between 1911 and 1916 of Nils Bohr’s conception of atomic structure. Like the black-body study this is a relentlessly technical reconstruction of the way in which Bohr eventually worked out his conception. Like the black-body study, it means to be revisionist, though rather more mildly so, meant to draw attention principally to a neglected connection between Bohr’s work and that of another physicist, J. W. Nicholson. However, its broader purpose is to fill out the story of how Bohr developed his ideas, and some of this is quite speculative, reconstructing what Bohr must have thought and reasoned at times when there is no record of what he was doing. The study is worth mentioning because this is a period of crisis in physics, with the quantum revolution taking place. Bohr differs from Copernicus and Planck in that he is looking to make fundamental change, is convinced by the state that things have reached in his discipline that the laws of mechanics which might be thought capable of governing the behaviour of atoms will not be able to do so. They will break down in this area, and a quantum view will be needed. Of course, it is precisely in revolutionary periods that scientists can meaningfully aspire to fundamental novelty, and may be found ‘casting about’ for radical solutions. However, even so, Heilbron and Kuhn insist that the answer to why Bohr’s work followed the precise course it did is not to be found in his ‘general conviction of the need for quantum theory which Bohr drew from his thesis research, but rather in certain specific problems with which he busied himself until the end of his year in England. They helped direct his reading and uniquely prepared him to recognize the special potential of the nuclear atom’ (212). Thus, the body of the study is the determination of the technical problems in physics that Bohr grappled with, and of the exigencies that drew his attention to them or that contributed to his thinking about them – such exigencies as his ability or inability to get on with particular scientists, his choice of laboratory to work in , and the fact that he came across physics papers that made an important difference to him. In other words, the story is mainly about how Bohr’s inclination toward quantum theory was given technical bite, - though it did not, in his case as in the others, mean that his achievement was a solution to the problems that he had initially been trying to solve - and much of the work that described is – though it was to issue in a revolutionary results – again, detailed puzzle solving. The case exhibits the difference – in the details, crucially -- between Planck’s basically classical conception of the quantum and Bohr’s fully quantized one:

‘As Bohr develops the limiting case, it is apparent that classical and quantum computations coincide only in their results; the models and the mechanisms of radiation remain distinct. Planck’s oscillator, in contrast, could with relative ease be viewed as itself behaving classically in the low frequency limit’ (276)

Conclusion :Implications:

Kuhn’s historical studies reiterate central theses from SSR :

First, that the comparative relations between two rival paradigms, at the time they are in vigorous competition, may be, as far as those involved are concerned, anything but clear cut. Setting aside presuppositions about what has happened since these two great revolutions, one can come to see that the now-outmoded doctrines were much less obviously mistaken than many now take them to be, and that the line between the adherents of the old and the new paradigm is not so easy to draw as, in retrospect, it seems: both Copernicus and Planck have been misunderstood as revolutionary heroes when, in fact, their motivation was to shore up, not cut down, the paradigm in place. Both thus support the idea that the search for fundamental novelty is not what is always, or even usually, involved in scientific innovation.

Further, notice the fact that Kuhn claims that the victory of Copernicanism was not only no knock out result, but more a victory through attrition, he also suggests that the Ptolemaic tradition could have been effectively shored up against the Copernican challenge, but that eventually there was no will to do this, that the attrition had worn down, rather than decisively refuted¸ the opposition.

One sometimes hears grumbles that Kuhn didn’t really free himself of the hero-worship of Whig-history (the worship of past heroes, and of ourselves as the telos of those heroes), because he spent almost all his time talking about scientific revolutions, not giving us accounts, as many in Science Studies now do, of the nitty-gritty of normal science. But these grumbles are misplaced and misleading. Both CR and BB may be studies of scientific revolutions, but they are, in fact, mostly studies of normal science. There will be more discussion about normal science below, but these two studies should militate against the idea that ‘revolutionary science’ is something that is done with a different motivation that ‘normal science’, for with both Copernicus and Planck their ‘revolutionary’ contributions resulted from what were unquestionably exercises in puzzle-solving, of the kind, one might even add, that surely only appeals to someone with a ‘geekish’ nature. It should explode, too, any idea that normal science puzzles are intrinsically trite, or that there is any easily discernible relation between the apparent and actual significance of any given problem.

Part II

Introducing Part 2.

We divide the critical issues arising from Kuhn's work under three broad headings. First, there are those issues associated with the concepts of normal and revolutionary science. These questions emerge naturally from our discussions in Part 1 but deserve further detailed consideration here. We believe that the concept of 'normal science' is easily misunderstood and that properly understood it is that which makes Kuhn's contribution to philosophy of science revolutionary.
For Kuhn virtually all of science is normal science, and normal science is a paradigm of rationality. On our account, it is 'normal science' not 'revolutionary science' that ‘wears the trousers’, and if it is thought to be the other way around this distorts the understanding of both what Kuhn has to say and of the natural science he is talking about. It also gives a wrong impression of what Kuhn might mean for other intellectual domains than the natural sciences.

Having given our account of what normal science means and implies, and having shown how, on this count, Kuhn is importantly different from Popper in the general direction and aims of his thought, we then review the dispute between them and show that the substantive differences between them need not be quite so divisive as Popper makes them out to be.

In Part B we try to deal with what is, for many, the sticking point with Kuhn. This is his idea of incommensurability. Though the idea is clearly essential to Kuhn's history of science and his idea of discontinuity through scientific revolutions, it seems to many to bee the fatal philosophical flaw in Kuhn. It seems to lead pretty directly to these undesireable consequences:

that nature has no role in determining the nature of scientific thought
therefore to relativist or idealist implications and
thereby, incidentally, to Kuhn's engaging in a performative contradiction i.e. telling us we cannot understand previous science by showing us how to understand previous science.
Partly by means of (often) favourable comparisons with Wittgenstein and Winch, we try to make better sense of what Kuhn is trying to say about incommensurability (sometimes better sense than we think Kuhn makes).
A lot of the section on incommensurability will focus on the idea of translation because this is how Kuhn and many of his distinguished critics have cast the problem. Can there be translation between different scientific paradigmatic theories? Does Kuhn say not?
Here, as on other occasions before, it is wise to pause for a moment and ask, what exactly is the question? Does Kuhn say that 'there can be no translation?' or does he say 'there can be no point for point, word for word translation?' or what? The difference between these two questions might not be instantly apparent, but be assured the difference is very important, and matters crucially in understanding what Kuhn is getting at. He does among other things deny that there can be word-for-word, point-for-point translation - but then, that is merely reiterating his argument that there is discontinuity between successive paradigms.
Does incommensurability mean that people separated by history or culture live in different realities - different 'worlds' as they are usually referred to. In other words, is Kuhn, whatever he might say, convicted of relativism, the view that there is no external standard against which different views can be objectively compared, and that one way of looking at things is just as good as any other? Is Kuhn a relativist? He has been accused of being,

Semantic relativism in the first instance presents this obstacle to understanding earlier science: we can't understand it! We can never know what previous scientists meant or were talking about - if what they said can't be translated into our words, then (since ours are the only words we can understand) we just can't understand them. The real interest of that in the Kuhn case, for the critics, is that it opens Kuhn to a charge of devastating contradiction: he denies we can understand prior science, and writes long books about prior science. Whorf and Sapir did fall into this kind of contradiction but does Kuhn? Or does he offer precisely a way out of such impasses?

Relativism about truth presupposes that we can understand others, but that we cannot criticise their conceptions. Their conceptions are self-contained, closed against us, and cannot be criticised in our terms. Therefore we cannot say that their scheme is worse than t ours, or that our scheme is better. It seems we must say that one is just as good as the other. But if they are very different (and that is, of course, the interest, that people have had very varied conceptions) then how can they both be equally good - surely one must be true and the other false (or both false)? Kuhn's historical studies seem to invite us to think that this applies to every paradigm, that it can't be compared either with nature or with other paradigms, and is, therefore, the judge in its own case and will, naturally, find in its own favour.
But this is just what drives people crazy. Realists say [imagine one, purple in the face, pounding the table top, entirely out of patience] : 'But Nature is out there, and it is not just up to us to say what it is really like, to be judges in our own case.' We will suggest that there is -- for Kuhn! -- a certain sense in which this 'Realist' intuition can be held onto, provided only that one abandons the whole effort to counterpose Metaphysical Realism as a doctrine to Relativism or Idealism. The point is not to try to be - to try to doctrinally identify Kuhn as - a Relativist (or Realist), but to see the pointlessness of all such doctrines in the philosophy of science. Small 'r' realism, a practical attitude, is then simply the natural presupposition of any science.

SECTION A: PHILOSOPHY OF NATURAL SCIENCE

We return to the topic of normal science, and to the dispute between Kuhn and two of the other epochal figures in philosophy of science in the 1960’s: Karl Popper and Paul Feyerabend. The bone of contention was the normative implication of Kuhn’s idea of normal science. Both Popper and Feyerabend saw that implication as being conservative. Thus, there are two questions that must be addressed in this chapter: does Kuhn’s philosophy of science lack a normative aspect altogether? And if it possesses a normative aspect, is this conservative in nature? Answering these two questions will hinge on a further question: does either Popper or Feyerabend fully grasp the nature of Kuhn’s concept of normal science and its subversive consequences for their own philosophies of science?

Philosophy of science commonly conceives of itself as a normative venture that will prescribe how scientists should proceed in science. For a long time, philosophy of science would identify a scientific method, but it was just this idea that the philosophers of science that we will be interested in here, were out to reject. Karl Popper had become, by the 1950’s, the dominant figure in philosophy of science, and had gathered a school around him. Popper rejected the idea that the identification of a general scientific method was of any interest to the philosophy of science: how people came up with their ideas had nothing to do with whether they were any good or not. Paul Feyerabend and Thomas Kuhn both attempted, in their different ways, to instigate a revolution against the Popperians, though both agreed with Popper that the philosophy of science was not about the identification of any scientific method. These two had very similar views on this: the scientific method was an historical fiction; no such thing was to be identified in the activities of actual scientists throughout history. What then might be the normative implications of philosophy of science?.

Let us say that a key to understanding their disagreement is that both Popper and Feyerabend wanted to give philosophy of science a role which was extrinsic to science itself. Both were driven by anti-authoritarian motives. Popper was particularly incensed by the threat that totalitarian politics represented to freedom generally, and to the growth of science in particular. Thus, Popper insisted – in terms of a liberal politics - on the urgency of maintaining a free society, one with institutions that allowed the possibility of criticism, for it was that which he identified as the very essence of science. Reflecting generational differences, Feyerabend was less troubled by the menace of totalitarian regimes than by the post-Atomic arrogance of scientific institutions. Rather than needing defence against authoritarians, the sciences themselves were becoming the most authoritarian threat. Thus, the need was to encourage scientists to be less authoritarian in their science (and therefore outside it as well). Feyerabend took an anarchist stance . Both understood Kuhn to portray science as [rightly] authoritarian]. It is not so surprising, then, that both accused Kuhn of conservatism.

Popper’s central and founding problem was the so-called ‘demarcation problem’, the need to distinguish metaphysics from science [where there was a danger – as with Marxists and Freudians – of the two becoming confused]. The difference, tied to the essentially critical nature of science, was that scientific hypotheses are constructed so that they allow the possibility of refutation. Metaphysics does not, in the way science does, make predictions which are sufficiently determinate to be compared against the facts, and for discrepancies between the two to be identified. Thus, Popper’s recommendation is that people should move out of the irresolvable disputes of metaphysics and into the resolvable problems of science by casting their thought in a form that allows the possibility of refutation. Popper wants to change the whole philosophy of science around. It had been pre-occupied with the question as to how scientific ideas can be confirmed. But, says Popper, they cannot. The only conclusive judgements which can be made on hypotheses are negative ones, that they have been disproved. No matter how much evidence is adduced in support of a genuine scientific hypothesis, this can never conclusively confirm the truth of the hypothesis. A view of the nature of science is proposed: it is an essentially critical enterprise, exclusively devoted to making efforts to disprove theories. That scientists should put forward theories that have the potential for refutation is not perhaps something that can count as a recommendation. On Popper’s own terms, it is the fact that they are doing this which makes what they do scientific (and not metaphysical). Feyerabend, rather, thinks that science is not so much critical as authoritarian. It is increasingly dogmatic, both within itself and progressively throughout the society. It will brook no alternative to its point of view, and regularly exceeds its competence in asserting itself against practices (such as alternative medicines, astrology and the like) that it deems inferior. He sees this view reflected in Kuhn, but feels that the authoritarianism is approved of by Kuhn.

Popper rejects the classical idea of scientific method, but is, of course, a methodologist prepared to prescribe.

Feyerabend is different: he sees a need to reduce authoritarianism in science itself. A central element in that authoritarianism is the insistence upon a single, unified frame of thought that recognises no valid alternatives [this sounds very much like a paradigm, does it not]. For Feyerabend, this is just a prejudice, and one which needs breaking down. Scientists should not all assent in one dogmatic scheme, but should resist this hegemony by creating alternative scientific schemes, by realising plurality within any scientific field.

It may seem odd that Kuhn’s confrontations with Popper and Feyerabend centred on normal science. One might have expected that the concept of scientific revolution and its implications would be the more provocative. Those who would find in normal science a holdover of the old paradigm in the philosophy of science, a less-exciting aspect of Kuhn’s thought, may be entirely mistaken.

‘Normal science’: on the surface an unexciting, even a dreary, term. Why does Thomas Kuhn, seemingly the philosopher of scientific revolution, dwell on this more boring-sounding, mundane topic? Surely scientific revolutions are the ‘meat’ of Kuhn’s account, normal science is merely their adjunct? And by the sound of it, normal science is more compatible with traditional versions of scientific change? How can this revolutionary in the philosophy of science allow, apparently, that science may progress normally, cumulatively, outside of revolutionary interruptions? But if one looks, for instance, at the document which above all records the clash between Kuhn and his critics, the volume Criticism and the Growth of Knowledge (Lakatos and Musgrave, 1970), which comprises the key papers given when Kuhn met face to face with Watkins, Toulmin, Popper, Lakatos, Feyerabend and others in July 1965, one finds a quite different picture. As is obvious even in the titles of some of the papers given on that occasion. - Karl Popper’s ‘Normal science and its dangers’ and even more starkly, J.W.N.Watkins: ‘Against ‘Normal Science’’. Furthermore, Feyerabend, often (and often rightly) pictured as an intellectual ally of Kuhn’s, had very similar -- and equally drastic --complaints on that occasion:

I was quite unable to agree with the theory of science that [Kuhn] himself proposed; and I was even less prepared to accept the general ideology which I thought formed the background of his thinking. This ideology, so it seemed to me, could only give comfort to the most narrowminded and the most conceited kind of specialism. It would tend to inhibit the advancement of knowledge.... More than one social scientist has pointed out to me that now at last he had learned how to turn his field into a 'science' -- by which of course he meant that he had learned how to improve it. The recipe, according to these people, is to restrict criticism, to reduce the number of comprehensive theories to one, and to create a normal science that has this one theory as its paradigm...

Both Popper and Feyerabend saw Kuhn’s work as unwelcome because it carried methodological implications they saw as dangerous for the practice of science. It was the idea of ‘normal science’ that carried the dangerous implication of conservatism. Popper thought that the idea of normal science encouraged the idea that scientists could and should be cautious, whilst Feyerabend’s fear was that Kuhn encouraged scientists to be obedient to one paradigm, thus reinforcing science’s authoritarianism.

Here is Feyerabend being quite direct on the matter, in a letter to Kuhn which sounds unmistakeable notes of warning, and of negativity:

You thereby take your readers in... I do not object to your [having the] belief that once a paradigm has been found a scientist should not waste his time looking for alternatives but try working it out... What I do object to most emphatically is the way you present this belief of yours; you present it not as a demand, but as something that is an obvious consequence of historical facts. Or rather, you do not even talk about this belief, you let it as it were emerge from history as if history could tell you anything about the way you should run science...

And here is a more indirect but nevertheless sigificantly anti-Kuhnian remark, also from the early 60s:

It is very important nowadays to defend...a normative interpretation of scientific method...even if actual scientific practice should proceed along completely different lines. It is important because many contemporary philosophers of science seem to see their task in a very different light. For them actual scientific practice is the material from which they start, and a methodology is considered reasonable only to the extent to which it mirrors such practice.

For 'actual', one can (we think) read 'normal' without disturbing the sense.

However, the key question is not whether Kuhn does offer this kind of threat, but whether his ‘critics’ have understood what normal science is, and whether, indeed, they have thought through the extent to which in practice one must, willy-nilly, agree with Kuhn.

What has upset Paul Feyerabend so much, prompting such a colourful attack on his ‘ally’; and what has incensed the orthodox Popperians ? A partial answer is provided by Barry Barnes, who indeed centres his book, T.S.Kuhn and Social Science, around the importance for sociology of Kuhn’s account of training and of the nature of normal science:

It was [his] account of scientific revolutions, with its explicit Relativistic implications, which ensured that Kuhn's work became widely known. Normal science was not so arresting a phenomenon, and some commentators, noting Kuhn's references to its 'cumulative' character, even managed to interpret it as nothing more than 'rational enquiry' in the traditional sense. The consequent image of revolutions as impassable crevasses ripping across the path of rational scientific progress was vivid and exciting, and aroused great interest. This was, however, an image sustained entirely by an outmoded and untenable stereotype of the growth of knowledge; and when it is set aside the value of Kuhn's concept becomes more open to question, and several weaknesses become evident in the manner of its formulation. .

Why does normal science arouse the ire of the Popperians and of Feyerabend most; and how it is that 'normal science' can be reasonably asserted by an influential social theorist like Barry Barnes to be Kuhn's fundamental theoretical contribution?

Normal science is, as we read Kuhn, very nearly all that scientists actually do. It is a process of extending and filling out the realm of the known; it does not look for fundamental novelties. None the less it is far from being the kind of heavily routinized and intellectually empty drudgery that some commentators have assumed. The tasks of normal science vary enormously, and even the most mundane of them can be immensely challenging. And it is, normally, entirely conducted within the ambit of a single paradigm.

Kuhn writes of five foci for factual (experimental) scientific investigation. These are:

1) The further investigation of 'that class of facts that the paradigm has shown to be particularly revealing of things.'

Tycho Brahe achieved vast (and well-deserved) fame as a great astronomer on the basis of his detailed and systematic observations of those features of the solar system and the stars suggested crucial by Copernicus. Tycho made no great discovery or successful theoretical innovation, but 'the precision, reliability, and scope of the methods [he] developed for the redetermination of a previously known sort of fact' made his reputation. Kuhn thinks that a significant proportion of normal science consists of this kind of activity.

2) The attempt to demonstrate the agreement of the paradigm with the world, at the few places where one might claim that they can be directly compared.

An example of explicitly anti-Popperian idea (Popper would exclaim that scientists ought not to be trying to confirm a paradigm’s effectiveness) is the creation of special telescopes designed to demonstrate the presence of the annual parallax of the stars predicted by Copernicus.

3) The determination of the value of natural constants.

For instance, the working out of Avogadro’s number, or of the universal gravitational constant predicted by Newton, or of the speed of light.

4) The determination of quantitative laws.

For instance, the determination of Boyle’s Law, or of Joule’s; and sometimes of their subsidiary versions in various more specific or anomalous circumstances.

Kuhn writes of these: ‘Perhaps it is not apparent that a paradigm is prerequisite to the discovery of laws like these. We often hear that they are found by examining measurements undertaken for their own sake and without theoretical commitment. But history offers no support for so excessively Baconian a method. Boyle’s experiments were not conceivable (and if conceived would have received a different interpretation or none at all) until air was recognized as an elastic fluid to which all the elaborate concepts of hydrostatics could be applied...’. And so on.

5) ‘Alternative ways of applying [a] paradigm to new areas of interest’.

These are the only aspects of normal science -- of the vast vast majority of science as it is actually, and not unwisely, practiced, according to Kuhn -- that remotely resemble the 'paradigm' one may have previously had in mind of science as exploration, as discovery, as groundbreaking, etc.

Then there are the theoretical problems of normal science, which fall in to very nearly the same classes as the experimental and observational. It’s not surprising that Kuhn should (quite reasonably) suggest this kind of symmetry -- because part of his ubiquitous point is that there tends throughout the sciences to be far more of an integration of the experimental and the theoretical than abstract theoreticist or empiricist models of science would have us believe. For Kuhn, the experimental can only intelligibly be planned or marshalled in the service of theories -- and theories will not get off the ground without being instantiated in exemplars, in equipment, etc. Though you can of course also, and very importantly, have thought-experiments -- which Kuhn, interestingly and again fittingly, thinks never have a purely 'conceptual' import, but always involve "learning about the world as well as about the concept."

Kuhn sums up by saying:

These...classes of problems -- determination of significant fact, matching of facts with theory, and articulation of theory -- exhaust, I think, the literature of normal science, both empirical and theoretical. They do not, of course, quite exhaust the entire literature of science. There are also extraordinary problems... [but these] emerge only on special occasions prepared by the advance of normal research. Inevitably, therefore, the overwhelming majority of the problems undertaken by even the very best scientists usually fall into one of the...categories outlined above.

Thus Kuhn thinks of normal science as puzzle-solving; rather than as like the creation or discovery of an entirely new puzzle. Almost all science, almost all the time, is not mediocre simply because it is like the ingenious figuring out of how things fit together in a vast and extremely complex puzzle. The places for almost all the pieces have as it were been prepared ahead of time. That doesn't make the puzzling out of how and where they fit together any less difficult or admirable.

First of all, the issue is not whether this kind of characterisation makes science interesting from the point of view of the philosopher, and whether philosophers (or indeed Kuhn) find this idea of normal science unappealing, unexciting and dull. What matters in Kuhn’s account -- and this is a vital 'sociological' point -- is whether scientists find these kinds of things interesting enough to fill up their careers, if not their entire waking lives? Kuhn’s suggestion is that scientists do find these things interesting and satisfying to do, and give each other prestige and honorifics on the basis of them – it is of course not only mould-breaking paradigm shifts that achieve high scientific recognition. Further, the substantiation of Kuhn’s claim would involve testing out his claim that there is relatively little else to be found within the scientific literature except for these kinds of attainments. When one thinks of the relatively few examples that serve the historians and philosophers of science to illustrate their arguments, and then reflects upon the endless rows of scientific periodicals that fill the science sections and periodical stores of the libraries, one can see what a tiny proportion of the work done is memorable in the popular sense. The great mass of it will be forgotten, even in its own discipline, but that is [as Robert Merton tried to point out to ancestor worshipping sociologists some time ago] one of the big differences between the natural and the social sciences; the natural sciences move on. However, the fact that scientific work is not publicly notable outside its [quite small] field Kuhn came to think it was about 100 people who typically worked in the shadow of an [exemplar type] paradigm, and that it is subsequently abandoned or absorbed anonymously into new paradigms does not mean that it must therefore be worthless - it is the essential stepping stone to further scientific work.

It is only very rarely, in revolutions, that the entire puzzle can be overturned and replaced by another. And of course, one wouldn't normally expect the pieces of the old puzzle to fit into the new one.

That there is seemingly astonishingly little empirical (sociological) evidence or data offered anywhere in the corpus of Kuhn’s work, to support his picture of the nature of (normal) science of the sort that shows just what proportion of scientists are doing what sorts of things clearly indicates that Kuhn’s interest was not in providing empirical generalities. There are of course the historical case studies, but even if our argument in Part 1 is correct, one could still object that Kuhn has not given us explicit accounts of humdrum (non-famous) normal scientific endeavours. Kuhn clearly had more of a grasp than almost any other enquirers into the philosophy of scientific change (into the theory of scientific methodology), of the actualities of the pursuit of science; but it is surprising in an academic treatment of the matter that we have mostly simply to take this on trust from him. Moreover, it is yet more surprising that this fact has elicited so very little comment down the years, given that Kuhn's influence on the social sciences (for instance) has been so great. Why do sociologists for example not demand of Kuhn at least as high a standard as they would demand from any piece of work submitted to one of their own mundane professional journals? (Part of the answer may lie in the disguisedly philosophical nature of ‘social sciences’ suggested above).

Even Barnes, while noting in passing (without complaint or suggestion for follow-up) the complete lack of empirical support offered by Kuhn for his suggestive account of the nature of scientific training, doesn't ever bother to mention that Kuhn's entire account of the practice of normal science -- his "fundamental" contribution -- is largely unevidenced.

Let us mention just a couple of examples (a few of the many possible), taken from Kuhn's discussions of normal science, of what we are talking about:

A part of normal [scientific] theoretical work, though only a small part, consists simply in the use of existing theory to predict information of intrinsic value. The manufacture of astronomical ephemerides, the computation of lens characteristics, and the production of radio propagation curves are examples of problems of this sort. Scientists, however, generally regard them as hack work to be relegated to engineers or technicians.

Is Kuhn in danger here of falling victim to the 'great scientist syndrome' which as a matter of general policy he attempts to resist? In order to answer this question, it would be useful to be shown the evidence that scientists DO generally regard these things as ‘hack work’. Kuhn offers none, here or elsewhere.

Kuhn again:

The scientific enterprise as a whole does from time to time prove useful, open up new territory, display order, and test long-accepted belief. Nevertheless, the individual engaged on a normal research problem is almost never doing any one of these things. Once engaged, his motivation is of a rather different sort. What then challenges him is the conviction that, if only he is skillful enough, he will succeed in solving a problem that no one before has solved or solved so well. Many of the greatest scientific minds have devoted all of their professional attention to demanding puzzles of this sort.

Here we have a truly central claim of Kuhn's. But where is the ‘evidence’, the ‘data’, for it? Where is the sociology/anthropology? For sure, Kuhn indirectly supports his claim a little bit elsewhere through his historical remarks about the science of (e.g.) Roentgen; but precious little. And to offer no empirical support at all in the first instance for a vital contention such as that normally scientists are almost never displaying order or testing long-accepted beliefs -- is this not a remarkable proceedure?

Is it not especially remarkable, given that Kuhn early in his book claims explicitly (and in line with his own ground-breaking suggestions as to the true nature of scientific pedagogy) that he will introduce his readers to "examples [paradigms?] of normal science or of paradigms in operation" prior to much later giving a 'more abstract discussion' of them?

To make sure we are not being unfair to him: Kuhn at least makes a start at rectifying the omission here, if such it is, in the Postscript to the 2nd edition of SSR. And, as will be explained below, we should not perhaps expect TOO much from Kuhn on this score. He is not a sociologist, and has in the final analysis little interest in the actual nature of professional (thought-)communities, etc. etc.. His interest, one might say, is rather in the use of reasonable sociological guesses and suggestions to provoke one to drop dubious philosophical claims and over-generalisations.

In sum: There may be good reason to believe Kuhn's very general claim(s) in the passage quoted above; but it is troubling to have to rely on his say-so. A good question, we think, to ask oneself when presented with a bold set of unevidenced abstractions such as those quoted above, is always this: What would it take to make belief in what Kuhn is saying here reasonable? Supplementarily: What data would be helpful; what studies would it be nice to know that Kuhn himself conducted, or at least read; to support his claims (if they are meant to constitute more than intriguing provocatory alternatives to the complete abstractions offered in the accounts of scientific theory-verification and falsification which Kuhn was rebelling against?)? What would it take to 'confirm' Kuhn's philosophy of science here?

And so, now: Do we take any of the above as a reflecting negatively on Kuhn, or at least of the claim to find in Kuhnian 'normal science' the centrepiece of his revolution in the philosophy of science? As a matter of fact: not at all.

Rather, we take it as a strong indication that one of our central claims is true: that Kuhn is above all a philosopher of science -- that it is in his philosophical claims and provocations and suggestions that his real interest is to be found. For sure, his 'own' (home) discipline was history of science -- and within it he made extremely valuable contributions. In a sense, in their detail, they are of narrow interest (they will never be widely-read, even if we wish that they would be). As we have already seen, they have deep import in providing Kuhn with examples through which to exemplify and dramatise the progress of philosophical revolutions -- but that is perhaps their only real philosophical relevance. And some might even argue that they do not exhibit the degree of radicalism one may find oneself hearing in Kuhn’s philosophical claims about either normal or revolutionary science. For instance, Copernicus emerges from Kuhn’s book The Copernican Revolution a figure almost entirely bereft of revolutionary ambitions, and as someone who worked almost entirely within the Ptolemaic paradigm.

We take our evaluation of Kuhn’s essential identity to be confirmed by the kind of remarks which he made not infrequently toward the end of his life, such as the following striking reflective comments:

The new approach that has so fundamentally altered the received image of science was historical in nature, but none of those who produced it was in the first instance a historian. Rather they were philosophers, mostly professionals, plus a few amateurs, the latter usually trained in science. Though most of my career has been devoted to history of science, I began as a theoretical physicist with a strong avocational interest in philosophy and almost none in history. Philosophical goals prompted my move to history; it's to philosophy that I've gone back in the last ten or fifteen years; and it's as a philosopher that I speak this afternoon…

Given what I...call the historical perspective, one can [in fact] reach many of the central conclusions we drew with scarcely a glance at the historical record itself... ...[I]t is taking us [a long time] to realize that, with that perspective achieved, many of the most central conclusions we drew from the historical record can be derived instead from first principles. Approaching them in that way reduces their apparent contingency, making them harder to dismiss as a product of muckraking investigation by those hostile to science...

What is striking is first the degree of self-identification as a philosopher (of someone who began life as a physicist and then trained as a historian of science) conceits; and second the surprising and indeed trumpeted willingness, which we have been discussing, and which is here openly proclaimed, to dispense with the density of actual historical examples in favour of the abstraction of ‘first principles’. To say it again, Kuhn is a philosopher above all, and it is as such above all that he deserves evaluation.

Popper and Feyerabend want to prescribe for science, but they want to prescribe an attitude for individual scientists, rather than a method. Both want to prescribe to scientists that they be adventurous, though each in their different ways. Popper wants scientists to be adventurously speculative in their constructive moments, and relentlessly critical otherwise. Feyerabend wants to stop scientists being taken in by the idea that they have got the sole truth on things, and wants them to be anti-authoritarian in their scientific practice. It is thus in the idea of science as normal science that Popper and Feyerabend disagree with Kuhn, whom they interpret as prescribing a different attitude, that scientists should be obediently conventional, going along with the crowd. Both, however, can only make that criticism by exaggerating Kuhn’s arguments about authoritarianism in the natural sciences.

Popper and Feyerabend think that the institution of science is in need of help from the philosopher [an idea perpetuated in the work of people like Fuller and other participants in the science studies movement], and both were primarily concerned with the place of science in a free society This is not a concern Kuhn exhibits in his historical and philosophical work at all, and his concern is much more preoccupied with descriptive issues than with prescriptive ones. This is not to say that his work is utterly devoid of ‘prescriptive potential’, only that this would not be either very specific or advise anything original, in many ways ut would devise nothing other than continuing to do science: indignant at Feyerabend’s accusation that he is ambiguous between description and prescription, Kuhn replies that they are to be read as ‘both at once’:

‘If I have a theory about how and why science works, it must necessarily have implications for the way in which scientists should behave if their enterprise is to flourish. The structure of my argument is simple and, I think, unexceptionable: scientists behave in the following ways; those modes of behaviour have (here theory enters) the following essential functions; in the absence of an alternate mode that would serve similar functions, scientists should behave essentially as they do if their concern is to improve scientific knowledge.’

It is, we think, misleading to read Kuhn as recommending normal science. His most fundamental and contentious claim -- though if it is heard right and if Kuhn convinces, it will come to sound an utterly anodyne 'claim' -- in that respect is that normal science is what science is. Meaning that: there would be no science at all if there was not nearly only normal science; that revolutionary science cannot happen at all without a vast background of normal science; and that even in revolutionary times, most of science (and most of its upshots) are anyway partially like normal science and mostly unlike (say) philosophy. The practice of normal science is deeply entrenched in the practice of the natural sciences, and is perpetuated by the organisation of the natural sciences. If normal science is what science is, then what value is there in recommending that scientists should do this? For it would clearly be absurd, normally, for them to do anything else.

But this shows that Popper at least has misunderstood what normal science is, that he imagines that it is intended to highlight only one element in science, that ‘puzzle solving’ picks out one kind of scientific activity, rather than advancing a characterisation of (virtually) all kinds of scientific activity:

But the ‘normal scientist’ was never was exemplified for Kuhn by scientific inadequates, but in fact by leading figures: Popper is hardly entitled to feel sorry for Copernicus and Planck, or to condemn them as badly schooled.

If we concede anything to Popper’s and Feyerabend’s criticisms we run the risk of confirming the view of Kuhn is indeed a conservative [which he may, for all we know, really be when it comes to the matters that bother Popper and Feyerabend about the wider society] . However, we are saying his philosophy of science is not usefully described as conservative,; though it is hard to be heard clearly, it at all, when one is saying something that does not fit on a conventional spectrum. It is matter-of-course in contemporary social sciences and humanities to categorise thinkers in terms of optimism and pessimism [which is much the same as conservative/radical] about the possibility of generating improving social change. Kuhn, in these terms, would look like a conservative, since, if you read into him the kind of prescriptions Popper and Feyerabend want to extrapolate from the concept of normal science, then he will appear to be discouraging people from thinking about the possibility of bringing about fundamental change in the nature of science. Are we guilty of projecting a conservative Kuhn; or is Kuhn actually guilty of the conservatism we 'attribute' to him? Neither!

Let us say that we see no reason to attribute to Kuhn any conclusion about the possibility or otherwise of improving democratic control over science, or indeed about intensifying the corporate control of business over its work. Concerns with the place of science in society motivate disputes over these matters, and it is just not a question which arises within Kuhn’s project , and no evidentially unsupported inferences about these matters should be made . The description of science as normal science seems to us a depiction which would not be altered by either the democratisation or the commercialisation of science. 'Puzzle solving' could be accommodated within very different forms of organisation, as it has been over the centuries during which the natural science establishment has built up to its present position; the fact that scientists were once self-funding scholars, are now tenured employees, and might increasingly become corporately sponsored researchers does not figure in Kuhn’s sketch; perhaps because it was irrelevant to it?

The real mistake, though, is to think that engagement in normal science is a manifestation of an individual’s attitude, one of mindless compliance with prescriptions, as though scientists are being merely obedient with respect to prevailing requirements of scientific activity whereas they could as easily disregard them. But this is not the picture which is anywhere implicit in Kuhn. The idea of the scientist as only the conventional follower of an orthodoxy makes it sound as if the only thing inhibiting scientists from breaking with the orthodoxy is their timidity, their unwillingness to think for themselves – a pretty insulting view really. It makes it sound as if nothing could be easier than to think of an alternative way of doing things in any area of science, that nothing could be easier to come up with ways of really putting an existing theory on the rack [Popper] or of generating very different but equivalently impressive alternatives that could match with an existing paradigm [Feyerabend, and perhaps Pickering (1984)]. But this shows absolutely no sign of appreciating the extent to which Kuhn emphasises how very hard it is to do anything [important] in science, and indeed, how little control any individual scientist has over the possibility of inducing fundamental novelty. The contrast between the normal and the revolutionary scientist is not, for Kuhn, as it is for Popper and Feyerabend, a characterological one, nor is it any difference in professional competence.

So, we need to make it quite plain that the idea that most scientists are not seeking fundamental change does not mean that they are somehow inherently conservative, intimidated by their training and professional experience from ever possibly thinking that their discipline might be usefully changed. We assume that what Kuhn does says does not conflict in any respect with the idea that every individual scientist might like to think of themselves as being eventually ranked with Newton, Darwin, and Einstein, absolutely eager to make a complete breakthrough if only they could, that they might be permanently on the lookout for an opportunity to make their name in a really big way. It is not to be assumed that it is their personal conservatism that stops scientists from searching for fundamental novelty. Kuhn’s point surely is that if scientists do dedicate themselves to changing fundamentals , if they were to decide that that was what they are going to do, then they would usually be making only an empty gesture, adopting an undertaking that would make no material difference to their scientific work. It would be like one of us deciding that life in modern society is pretty unadventurous, and that we had therefore better have an adventure, deciding to dedicate ourselves to seeking hidden treasure. This would be an entirely idle gesture without a somewhat more concrete idea of what treasures there might actually be find, and where to start looking for them.

To keep the argument concise, we’ll try to round it out with two further points:

1. That fundamental work is dependent on timeliness. And
2. That the best way to make a fundamental contribution is to pursue normal science.

The latter is crucial and is the (achieved) burden, if read carefully, of chapters 5 to 9 of SSR (and of the historical studies). We have already discussed these in Part I of the book. Let us here recapitulate, and expand on the morals:

If there really was a Holy Grail, we might set out on a quest for it; but there is no opportunity to do this, because we are not convinced there ever was any such thing, and have absolutely no idea where to start looking for it if it did exist. And, in the same way, the situation in a mature science is that opportunities to make fundamental changes are relatively rare, and require a combination of [often fortuitious] circumstances – it is -- of course -- not plainly obvious where there might be room for a fundamental contribution, what sort of thing might make such a contribution, and so on, so it is not even as if a scientist can identify the appropriate circumstances; Planck thought he was preserving the integrity of classical physics, not coining an idea that could eventually shake it – he just did not see the possibility of treating the discontinuity as in the phenomena.

‘Did not see’ might be ‘could not see’; recognising that you might reject the ‘continuum assumption’, the assumption that matter was continuous, that particles were embedded in the ether [that you might seriously propose that this could be done in the context of 19c classical physics] could be a virtual impossibility. Not because scientists have a kind of sentimental attachment to classical physics, or are hidebound as a result of their career investment in that approach (though some of them might be). But just because it would be by no means easy to see how that idea could really cash out, or how it could be as much as a serious idea. What would it mean to talk about 'quantum discontinuity' in 1899? It is clearly hard for people even now, after a century of quantum physics, to get their head around the idea that nature is discontinuous and statistical, and one might therefore get a (correct) sense that Planck would have real difficulties in even thinking that thought.

Now for point (2): we’ve been saying that a point which Popper and Feyerabend both miss, is that the distinction between normal and revolutionary science considered as actual practice is not a sharp differentiation . For example, it is most important not to imagine that the distinction is supposed to be one which is reflected in the general attitudes of individual scientists, as if some were ‘insurrectionist’ and others were ‘conservative’ characters, some agitating for change, and others fighting to prevent it – there are times, assuredly, in which scientists might be in these positions, but it is not because one crowd are generally willing to knuckle under to orthodoxy and the others are not. As Kuhn tried to make plain, the scientific meat of a revolution is the estimation of the robustness and prospects of the paradigms, and there is normally , taken from a properly historical, retrospective point of view, relatively little to choose between the two sides. Those who are reluctant to change may be no less sincere than those who will eventually win the accolade of history as the progressive forces, and it may be that those who resist change can give, argumentatively, pretty much as good as they get, have good arguments against their critics, might indeed see big flaws in the would-be rising paradigm. Remember, too, that absolutely nobody is proposing that they should go right back to the beginning, throwing out everything achieved under the old paradigm altogether; the revolutionaries are proposing to go on from the paradigm in place i.e. to address problems arising in and from that paradigm, as well as to incorporate parts of it in their new paradigm. Of course, popularises of science don't tend to tell us much about the many times where the resisters have been quite right, and the would-be new paradigm turned out to be useless or even quackery.

The difference between revolutionary and normal science is a difference in the state of the science rather than in the inclinations of individuals. There is some difference between the activity of scientists in normal and revolutionary science [they are, in the latter case, somewhat at a loss perhaps, and are casting about for ideas, and are spending time on propaganda, arguing fundamentals in ways that they might not otherwise have been] – however, this does not cash out as a difference between someone doing normal science and someone doing something quite otherwise, a kind of ‘revolutionary science’ imagined on the 'model' of (say) 'communist science' or 'new age science'. The revolutionary struggle is somewhat more like a propaganda war in which the two sides try to promote their respective causes and run each other out of town, but the scientific work which goes on within those periods and in the respective camps is not really much different from the normal kind, in respect of puzzle solving etc – the revolutionary scientist is not, as seen in Kuhn’s main case studies, someone who is out to make a revolution at all, who is looking for a way to turn the paradigm upside down, and who is mostly arguing philosophy or methodology, but someone who is trying to sort out a problem within the paradigm, and has run out of ways of solving the problem within the paradigm, and so is trying out new ways of solving the problem.

The ‘advice’ that the best way to achieve fundamental novelty is to do normal science isn’t really advice at all, it is again more a matter of saying ‘there isn’t anything else to do than normal science’. Thus it is quite unclear how scientists might do otherwise than ‘normal science’, what kind of activities Popper and Feyerabend have in mind in addition to those which Kuhn identifies. And this is one crucial dimension in which the real substance of Popper’s and Feyerabend’s difference with Kuhn is quite obscure. Insofar as there could be substantial disagreement amongst them it would seem to come down to an empirical question, though not an easy one to answer without a lot of research. Is Kuhn’s list of activities that scientists engage in, as given above, incomplete? Are there activities scientists engage in that are not on it, and if there are, how many of them are there? Second, if there are such activities, are they the sort of activities that are definitely not ‘normal science‘ i.e. do not involve working on and within a paradigm, which do not constitute a puzzle solving practice? Finally, if there are such activities, and they are not puzzle solving, then how significant are they as a proportion of things scientists actually do – are they a big proportion or, relative to the range of things Kuhn picks out, comparatively infrequent or even inconsequential?

Kuhn’s most important objection to Popper is with respect to the role of criticism, where he accuses Popper of having an entirely unrealistic picture of what actual science is like. In the land of Popper’s continuous revolution, science would not be like science-as-we-find-it-all. At best, it would be like the pre-paradigmatic situation prior to the emergence of natural sciences, when everybody was disputing fundamentals. Even worse, Popper’s idea of criticism would make science more like the philosophy seminar rather than even a pre-scientific stage. Certainly, taking Popper at face value, this would seem an entirely appropriate objection. However, it may be that the charitable treatment of Popper would be that he does not believe anything of that sort, that he does not and cannot in reality hold a picture of science as an endless and unrelenting round of critical argumentation. It can be argued that, in fact both Popper and Feyerabend’s arguments presuppose Kuhn’s picture of normal science [but neglect to notice that they do so.]

Kuhn’s objection is that Popper’s view of the importance of criticism to science is very much exaggerated, and that it is [as anyone can see just as a matter of fact that working scientists do not constantly spend their time striving after revolutionary reputations, attempting to shoot theories down the instant they are put up]. But is that really the way Popper thinks? One might suggest that each side is exaggerating the extent of their possible disagreement with the other because they have been drawn toward discussing the critical inclination of scientists at the level of individual motivation. Both sides, we suggest, are well aware that criticism is first and foremost an institutionalised feature of science, and that there is – in many ways – no real difference between individuals being critical, on the one hand, and going about their routine puzzle solving work on the other.

Criticism is not only manifested by the slanging matches which might be occur during revolutions, but is, or ought to be, most crucially apparent in ‘routine’ scientific work. Popper does not really, any more than Kuhn , need to suppose that scientists are in endless, perpetual and fundamental dispute with one another. Plainly they are not. But that does not mean, either, that they are not engaged in something worth calling criticism.

Perhaps some of the seeming divergence between them might then be explained thus:

Thesis: that Kuhn’s focus is fairly heavily upon scientists involved in investigations into phenomena (‘finding out’, as Hacking puts it), whilst Popper is ostensibly preoccupied with an image of scientists as testers of theories.

Argument: Kuhn’s conception of normal science makes it the paragon of directly cumulative scientific work, and it contributes to the progress of our knowledge by the depth and intensity of its inquiry into nature

A main part of the work of normal science is, then, the investigation of particular phenomena, with the normal scientist applying rather than contriving fundamental theory, relying upon the accepted paradigm to deliver a result, rather than striving to expose the theory at its most vulnerable points. Kuhn argues that though there is no testing of the fundamental theory against the results of the scientist’s investigations, there is testing of the individual scientist’s work against the standards of the prevailing theory. Normal science is puzzle solving because the paradigm generates puzzles, which should be soluble in its terms by the competent investigator. But it is, of course, a routine aspect of scientific work that it is routinely presented to and criticised by one’s colleagues - and, of course, it is an aspect of scientists’ puzzle solving efforts that these are often themselves essays in criticism of prior puzzle solving efforts - the ‘puzzle solving’ motivation includes the urge to exceed the ingenuity of other solvers.

Thesis: That both are tending to lapse into treating ‘criticism’ as a matter of individual motivational , as involving the difference between ‘critical’ and ‘conforming’ individuals rather than as an institutionalised feature of science.

Argument: The implication of the preceding argument is that ‘criticism’ is an institutionalised feature of the natural sciences, one which is embedded in the now utterly taken-for-granted forms of scientific activity, in the presentation, publication and circulation of scientific work, a level of intense scrutiny by one’s colleagues that does not obtain in any other area of life. The extent to which Kuhn presents scientific training as ‘dogmatic’ [simply cut note (though I personally would still rather keep it)109?]is not to suggest that it has the objective of producing compliant and dogmatic individuals, but of producing competent practitioners, up to speed with current work, and capable of forging new directions of work for themselves, of significantly extending the reach of the paradigm, if nothing more than that. The natural sciences are not motivated to rehash past controversies, and it is the business of scientific training to acquaint beginners with the received body of work. ‘Critical ability’ does not represent an addition skill acquired in addition to learning how to do the maths, design experiments, apply the theory and so on.

Thesis: That Popper leaves out of his story, in a way that Kuhn does not, the amount of work required to develop a paradigm to the point at which telling criticism is possible.

Argument: Kuhn, recall, stresses that a paradigm , on its first appearance is very much underdeveloped, and that its value is in important part in its fertility as a source of further work that will flesh it out, and capitalise on the possibilities it offers for raising levels of precision . Normal science provides the paradigm with its content, and does not fit a simple contrast between seeking either for refutation or for confirmation. Spelling out and giving application to the paradigm is not so much a matter of seeking supportive evidence for it (let alone conclusive confirmation of it) but could as much be thought of as mining its potential. The spelling out of the paradigm will, of course, contribute to the potential for refutation, by both improving the precision of its claims, and by explicating its most unlikely implications, and generating anomalies – thus exposing it to stronger risks that the results will not turn out as expected.

Though it is true that the notion of ‘normal science’ will subsume those individuals whom Popper would despise, the ones who adopt a cautious, bandwagon-riding approach, it hardly includes only those, nor intimates that they are more than a minority. It is clear that those who are practicing normal science are often stretching both themselves and the boundaries of their science. It is not only those who create scientific revolutions who deliver notable scientific achievements . The alternative simply is not between the great revolutionary scientists and hack workers, and the overwhelming majority of scientists do - or so Kuhn thinks - stand somewhere between these two extremes.

Finally there is the issue of ‘anomalies’ or of potential falsifiers.

Popper’s notion of the ‘verisimilitude’ of theories can be seen as very much akin to Kuhn’s idea of notable scientific achievements, at least in this respect: both recognise that there will be pros and cons for any scientific theory. Each assumes that though a given framework fits nature, it does so only to a certain degree and that, somehow, inevitably, subsequent science will reveal respects in which it does not do so. However, as Kuhn argues, and Popper effectively assents see Lakatos’ discussion of ‘sophisticated falsificationism’ (Lakatos, 1981, 31-47) and Popper’s late statement on falsification (1982, xix-xxxv) moves to ‘sophisticated’ falsificationism – this is among other things an increasingly major concession to Kuhn)), scientists do not give up a theory just because it is (in at least certain respects) ‘falsified’. Scientists give up one theory only in order to take on another. The scientific revolutionary has to match and surpass the achievements of the prior paradigm, and it is only under some (never precisely specifiable in advance) conditions that the potential of some anomaly to the prevailing paradigm to provide the basis for an alternative conception that matches and surpasses it will be discerned and developed. There may be conservatism amongst some scientists, and there may be an unwillingness because of vested interests in the status quo to entertain suggestions that the prevailing paradigm is fundamentally flawed, but this does not explain why anomalies only occasionally become the basis for the refutation and replacement of the paradigm with which they will not fit.

In sum, then, with respect to the issue of the critical nature of science, if the two thinkers are read charitably, and not treated as expounding exaggerated and extreme positions, one holding that science is unRealistically critical and the other that it is unRealistically dogmatic and authoritarian, there need be little disagreement of substance between Popper and Kuhn. Popper cannot help presuming what Kuhn emphasises, that revolutionary science turns over a paradigm by putting another in its place. Kuhn highlights what Popper at least downplays, namely, the difficulty in coming up with any serious scientific conjecture, i.e. something that could viably act as a new paradigm.

The thing that Feyerabend neglects about normal science as Kuhn portrays it, and which renders his prescription for paradigm proliferation vacuous, is the categorical nature of scientist’s procedures under paradigms. They do not treat the paradigm as a provisional installation, as a point of view which can be opted for or declined according to one’s preferences. The paradigm is not a ‘point of view’ on phenomena, which is to be offered in a spirit of interpretation, toward which alternatives might be entertained. The paradigm’s policies are treated as definitive of matters of fact, and their outputs categorically stated. Nor is this to serve Feyerabend’s precise point, which is that scientists should take a more distanced attitude toward their creations, express them in tentative terms, an inclination that would be acceptable if it was legitimate to cultivate alternative paradigms. However, Feyerabend’s are proposals as to how science should be [drastically] changed to legitimise the proliferation of paradigms, and involve, as such, the concession that such proliferation currently has no real place in science, and that, therefore, Kuhn’s ‘normal science’ does depict what science is actually like.

But isn’t this why Feyerabend’s proposal is necessary? Well, to think that it could be at all plausible from Kuhn’s point of view really is to overlook what Kuhn has laid out with respect to normal science and the pursuit of paradigms: the creation of paradigms is not a for-its-own-sake affair, and actual paradigms emerge from the scientific round and are only retrospectively identified as such, and it would be a very fundamental change in science to value paradigms as ends, and to value therefore a plurality of them. The very identity of something as a scientific discipline is tied up with unity-around-the-paradigm, so it is quite unclear as to how different paradigms could actually exist, how they would retain any sense of being related to each other? The conditions for the formation of a new paradigm are tied in very specific ways to their predecessor, a fact which Kuhn formulated with his emphasis on the technical bite that they must have. That one can formulate one paradigm with sufficient technical bite to challenge is rare enough, that one should generate a plurality of them… As Feyerabend envisages them, the plurality of scientific ideas would lack just that feature, the technical bite, that, in Kuhn’s account, marks out a paradigm. Further, paradigms are not produced de novo, they are in important part constituted out of the prior paradigm, and thus a new paradigm cannot accede autonomy to alternatives, for it will want not merely to conceive things in its own terms, but, as part of that, to re-conceive what the prior paradigm’s achievements. What, then, would be the value to working scientists to attempt to develop a new paradigm just to ensure that there was a plurality available: how great an effort would it be to engender a new paradigm significantly, if not entirely, different from that already in place?- If it was merely to be an optional alternative to the other, then the effort would have to be just as successful as that already in place, and therefore just as problematic to achieve as the initial paradigm was. Further, what is the point of developing an alternative paradigm that is just as good as the one in place? If you are going to the trouble to develop a brand new paradigm, why not produce one that is better than the alternatives? What is the point of having a [presumably mostly a notational equivalent] mere alternative to a paradigm, why not contrive a replacement for it?

We do not offer this as an ideological defence of normal science, but as a suggestion that Feyerabend has not really thought through what he is proposing, that he certainly has not seen either the extent to which he depends upon the idea of normal science to promote his critique, but also the extent to which, in trying to articulate it, he has failed to address the features that Kuhn identifies as essential to it. In consequence, he has no answer to the question: how would one leverage change away from the normal science which currently comprises the natural sciences toward the kind of thing that [Feyeraebend thinks] he would prefer to see.

Perhaps a further important element in Kuhn’s difference from Popper and Feyerabend is the extent to which Kuhn treats science as primarily an investigative activity, whilst Popper and Feyerabend really treat it as a predominantly theoretical one. Though Kuhn never puts the point in so many words, he sees that the value of the examples are in their fertility as an inspiration to researches into specific kinds of knowledge. It would be wrong to think that what scientists were doing was ‘exploring their paradigm’ rather than investigating particular kinds of phenomena: but finding out about particular kinds of phenomena is exactly the same thing as exploring the paradigm. Normal science involves, then, for example, finding out about the chemical reactions involving proteins, the nature of regularly repeated enrgy emissions from stellar bodies, the effects of chemicals on the brain, the conditions under which metals fatigue, and so on and on. The interest in ‘normal science’ can lie at least partially, if not entirely for some, in finding out more about the nature of a particular phenomenon.

Kuhn is trying to tease one away from an almost ubiquitous and deep-set intellectualism in one’s thinking about science. Kuhn's account of 'normal science' can , controversially, be seen as a novel model of what it is for a collectivity of persons to be engaged in rational inquiry. Of course, many forms of rational inquiry are not science -- but arguably, normal science can be read as a model for rational inquiry in general. A model emphasising that much must be taken for granted for anything to be disagreed upon, that a focus on advancing research requires a disciplined exploration of an agreed agenda, etc. . This would be Kuhn as philosopher par excellence -- for this would be a mode of argument going well beyond sociology or history. But it would still be philosophy in the sense of being a (non-intellectualist) approach to scientific activity.

Consider again -- try to SEE -- Kuhn AS (a) revolutionary in the philosophy of science. The concept of normal science is not a conservative conception: it is very threatening, it is radical, and it was largely hitherto unrecognised as vital, foundational, for the study of science, for studies of science which do not take the finished discovery or theory as the only relevant standpoint from which to tell a tale of scientific change, and which do not focus on the rare unexpected innovation made by an isolated or eccentric or heroic man as the be all and end all of such change. It is threatening, because it says that little if any of science is like the Popperians in particular said it was. And because even scientific revolutions in their socio-historical concretion emerge out of the same processes, not literally out of odd isolated eccentrics with bold and brave new ideas. This thought is in a sense stronger than Kuhn's important and well-known claim that "Anomaly appears only against the background provided by the paradigm... . By ensuring that the paradigm will not be too easily surrendered, resistance guarantees that scientists will no be lightly distracted and that the anomalies that lead to paradigm change will penetrate existing knowledge to the core... . // So long as the tools a paradigm supplies continue to prove capable of solving the problems it defines, science moves fastest and penetrates most deeply through confident employment of those tools." The distinction between normal and extraordinary science, so severely criticized by Toulmin and others, is in a way of less import once one has understood that the actual practice of science need not be that different in order for its results to be extraordinary . To anticipate, we want to claim that the point of talk of incommensurability can be largely separated from the distinction between ordinary and extraordinary science, at least insofar as that distinction is thought of as a matter of the kind of practice engaged in at the time, rather than as a matter of conceptual transformations fully visible only to the sensitive historian. And what one sees, when one thinks through the normal vs. revolutionary distinction properly and with care, is that the kind of thing that is going on in science (not particularly in its individual practitioners) at these different 'moments' is such that:

1. Revolutionary science, which in its day-to-day substance in mostly normal science anyway, could not emerge except from normal science; and
2. Unless one understands that, conceptually, there are the normal and the revolutionary moments in science's development, in the 'structure' of science, then one will fail to be understanding science at all. That is, accounts of science which really left no room for the kind of stability of problems and data found normally, and for the kind of conceptual innovation found occasionally, would not really be accounts of science at all. They might successfully account for some bit of scientific activity; but that would dissatisfy their producers. They mean to be accounting for science -- once they understand Kuhn's approach and criticisms adequately, they will (or should) give up even their partial account, for it does not achieve what they wanted to achieve in the first place.

In a certain sense, one might go so far as to say that the real criticism directed at Kuhn by Popper et al was that Kuhn is not sufficiently the philosopher of scientific revolution. Popper basically says to Kuhn: The problem with you is your notion of normal science, or at least your notion that normal science is basically O.K. . I could stomach your talk of 'scientific revolutions', if only you were prepared to admit that (little) scientific revolutions are happening all the time, or at least ought to be.

Popper plays not Roosevelt but rather Trotsky, to Kuhn's (as imagined by Popper) Stalin. Popper preaches not, as one might expect, no revolution and instead enlightened liberal efforts at rational change -- no, one might say he preaches permanent, ‘global’ revolution. He looks for a culture in which scientists are continually prepared to radicalise their enterprise from the ground up, in which there are no shibboleths, only the ever-present prospect of drastic change and the jettisoning of basic assumptions.

Popper's primary accusation -- that people are, for Kuhn, stuck in a framework, that he is an irrationalist in thinking that free unframed thought is impossible -- is of course the very opposite of the accusation that others make most central -- that Kuhn is an irrationalist in thinking that drastic change is too easy, in preaching the gospel of scientific revolution. (It is perhaps worth noting right here that Kuhn emphasizes the internality (i.e. resulting principally from factors internal to the science in question), even 'necessity', of scientific revolutions. And after all, even gestalt switches are not unconstrained. Quite the contrary: one can see a duck or a rabbit, but little or nothing else. As intimated above, Popper has a quite inadequate idea of what being a revolutionary would involve. It is not a matter of just saying, "Let's be revolutionary!" It is a matter of being willing, if push really comes to shove (as it rarely does), to countenance more fundamental change/revolution than Popper is willing to countenance.)

One might risk describing Kuhn as providing the basis for an anti-Foundationalist epistemology , with at its centre a reconceptualisation of the nature of rational inquiry focussed around the nature of normal science. Perhaps seeing Kuhn as doing this makes him look less extreme than either those who accuse Kuhn of an 'anything goes' mentality or those who accuse him of being a 'frameworkist' would have it...

Kuhn’s revolution in the philosophy of science is, we would suggest therefore, rather widely misunderstood by those not closely familiar with it, and perhaps unaware of its threat, force, or promise. Barry Barnes is arguably right in this, at LEAST so far as 'the social sciences' are concerned: Kuhn’s most radical successful contribution to the philosophy of science is probably not his particular rendition of ‘scientific revolution’, nor exactly his (much-misunderstood) notion of ‘paradigm-shift’ -- it is in his role specifically as the philosopher of normal science that Kuhn’s most authentically revolutionary contribution is to be found! It was in his insistence, that is, on the mechanisms through which science is and has to be normally NON-revolutionary, that Kuhn struck a blow to the heart of the Popperian enterprise, and depicted a 'new' vast realm of science, one which conformed to the standard (post-)Positivist image of science only at the huge cost of rendering the latter more or less trivial. Trivial, as we have emphasized, because Kuhn explained how the cumulativeness of normal science was relative to a paradigm (a disciplinary matrix) whereas for Logical Empiricists and their successors (including now many recent/contemporary philosophers who take themselves to be Realists, and oppose the Anti-Realism of the Carnap etc. crew), the cumulativeness of knowledge was absolute .

In sum: 'Fans' (e.g. Barnes) and 'foes' (e.g. Popper) of Kuhn alike , (albeit often only dimly and foggily) appreciate that, once one gets beyond the banalities of the loosest talk of 'new paradigms' consequent upon catastrophic/dramatic-sounding scientific revolutions, Kuhn's suggestive philosophy of science is what most people are interested in. And that philosophy of science is founded perhaps less on concrete historical accounts of ruptures (and still less on actually established sociological investigations) than on a novel and abstract account of the normal, skillful, mundane proceedures of problem-solving, puzzle-solving (communities of) scientists. The latter may sound unexciting; but, as we have stressed, its consequences are arguably just as revolutionary as all the talk of ‘scientific revolutions’. Kuhn's account of normal science 'parallels' his account of scientific revolutions: he introduces, through the two put together, truly an account of science ... for the first time ever.

We hold, then, that a fatal flaw in most criticisms of Kuhn's rendition of scientific change is that Kuhn's critics try to criticise one of the 'aspects' or 'moments' of science as described by Kuhn, while surreptitiously drawing, at the same time or elsewhere, on that very moment. Thus, as already mentioned, Popper attacks the legitimation of normal science as science. But he also requires the kind of stability there is in ordinary (normal) science, in order for there to be enough agreement for falsification to actually work -- to work stably in a community. Furthermore, Popper fails ultimately to account even for the genuinely revolutionary moments in science, because he fails to make room for the kind of significant conceptual change (see SSR p.98, e.g.)... for which the ground is prepared only by the existence of normal science (see e.g. pp.88-95 of SSR).

Carnap and other logical empiricists ((post-)Positivists) seem to understand the existence and importance of normal science -- but, not only does their narrow reading of it fail to leave any space for revolutions, but they don't even really leave sufficient space for normal science. They don't leave space, that is, for exploring the paradigm, for puzzles. (see e.g. SSR pp.98-101).

Feyerabend is a kind of limiting case. He seems to overcome the different limitations of vision of Carnap and of Popper alike -- but at the cost of obviously yielding an activity that will bear scant resemblance to anything we could now call science, and will instead look more like (say) Modern Art. Just because Feyerabend really has no time for normal science. In him alone does one really find almost an ideal type of someone picking just one of Kuhn's two aspects and focussing all his praise on that one -- all his ire on the other. And we have wondered in fact whether even Feyerabend would be prepared to countenance the real abolition of normal science.

Mostly, the important thing to see is how virtually all would be methodologies of science, even arguably the Feyerabendian 'anti-methodology', actually presuppose Kuhn's picture of science! This is why Kuhn says, in his subtle way, the extraordinarily strong critical things he says of the received view in the philosophy of science. Namely that, if we take them at their word, rather than seeing how they collapse into his view, the Positivists and all their successors and inheritors (this includes the Falsificationists, the Logical Empiricists, and arguably also Feyerabend (as an anarchised post-Popperian) and all who retain any 'formalism' in their methodology and epistemology, any notion of the scientific method as expressible in philosophical/logical formulae) fail to give us a genuine view of science at all. This is the meaning of Kuhn's formulations on (e.g.) p.80 and pp.98-102 of SSR. Taken at face-value, even late Carnap, and sophisticated Popper, and Kuhn's 'friend' Feyerabend ... fail to generate accounts of science at all.

One of the reasons why Kuhn’s ideas were so influential on the social sciences and humanities was because these were already much interested in and influenced by the philosophy of science. Kuhn’s book must have seemed like yet another, and welcome, contribution to the efforts that would-be social scientists had long been making, namely, to turn themselves into proper scientists, under the guidance of the philosophy of science. Thus, there was abundant enthusiasm in some circles for Popper’s advice: sociologists and their like should become scientists by ensuring that they developed proper theories, ones that could be refuted by evidence. Kuhn’s message must have seemed reassuring in this way: it strongly reinforced the idea that the social sciences could really be sciences -- in a manner easier to achieve even than adhering to the Popperian form. Certainly, Steve Fuller is intensely critical of Kuhn on the grounds that many people have taken Kuhn’s account of the natural sciences as a model to adopt and follow in the human sciences and social studies. That cannot be, however, a basis on which to criticise Kuhn, for it was certainly not his advice that these people were misguidedly following.

Consider, then, the situation that social scientists have long found themselves in. They can recognise this situation in Kuhn’s description of the early stages of the natural sciences. The early natural sciences have no paradigms, they have schools, ones which are endlessly debating fundamentals, with each inquirer trying to make a completely fresh start, and to rebuild the whole discipline anew and from scratch. But this is just what contemporary social sciences are like. Kuhn’s study shows how the natural sciences have been transformed, how someone – a Newton, a Galileo perhaps – has come along and succeeded in entirely reshaping their area of inquiry, turning it into a unified discipline. There must, then, be hope for the social sciences: their present condition is just like that of many scientific pursuits before they developed unity-around-a-paradigm. Therefore, there is nothing to stop – and seemingly every reason to expect – that social studies can and will turn into paradigm-ruled pursuits. Is it though, just a matter of sitting around and waiting for one’s Newton or Galileo to turn up, or is it a matter of making a more deliberate effort to implement the promise that can be found in Kuhn? In other words, has Kuhn shown us how to turn the social ‘sciences’ into the social sciences?

Let us begin by setting our briefly what we argue for in this section. Our argument, in simple, is this: that the social sciences make the mistake of supposing that the application of the philosophy/methodology of science in their own area is a key to scientific progress. It is the old and seemingly endlessly attractive idea of modelling one’s efforts on those of (other more successful) sciences. But, Kuhn asks, is the success of the natural sciences because natural scientists know more about truth than anyone else, or just because they know more about plants, or animals, or soil, or stars or whatever their interest might be than others.

’ It may, for example, be significant that economists argue less about whether their field is a science than do practitioners of some other fields of social science. Is that because economists know what science is? Or is it rather economics about which they agree?’ (SSR, 160-1)

How much do economists or sociologists -- or physicists or geologists -- really know about science? How much does anyone really know about science in either the sense of knowing how science is actually done and actually works, or in the sense of knowing what it is about the things that scientists do that make them scientific? What social ‘scientists’ think they know about science is merely the philosophy of science. The implication of what Kuhn says is therefore that, really, social scientists typically know nothing or next to nothing about the actual natural sciences.

So, social scientists are going about things in entirely the wrong way insofar as they are guided by the idea of attempting to turn what they do into sciences. This kind of argument is very strongly put by Kuhn with respect to the social sciences [so called] in his argument about the futility of the methodological imperative to quantify

(cf. The functions of measurement in physical science, ET,179-221, esp. p.221).. The fact that the most successful [not by any means all, we add] of the natural sciences are highly quantitative has convinced many that the very essence of science is measurement. This conviction has certainly been influential on the social sciences, and the imperative of measurement – Go forth and quantify! – disfigures (especially) American sociology even today. Kuhn argues that the attempt to build a science through quantification is entirely futile, and that the history of science shows this. The history of science shows that quantification often arises out of a rich and detailed qualitative knowledge -- or at least, aesthetically/practically productive and impressive conceptualisation (think of Copernicus, for instance) -- of the phenomena in question. Creating methods of measurement independently of one’s understanding of the phenomena one is attempting to investigate just is an unproductive exercise. One requires above all an exemplary scientific achievement. Not simply a quantificational form to one's hodge-podges or hand-wavings.

Kuhn’s own approach is really telling the social scientists that one cannot move from a pre-paradigmatic state to a paradigmatic one by design, that none of the paradigm-based pursuits have emerged in this way. Thus we can perhaps polemically summarise Kuhn’s implication in this way: that the attempt to make [say] sociology scientific by modelling it on the natural sciences is just about the most unscientific way of proceeding imaginable. Effectively, the attempt to set out the ground plan of the discipline, and to build upon that is precisely to perpetuate the condition of ‘the schools’, and is to attempt – imagining that one is following the way of the natural sciences – to do what no natural science has, to our knowledge, ever done. [Of course, we don’t mean that one natural science can’t borrow ideas and examples from other natural sciences, and in that sense, follow the example of another science, for they do, of course, routinely do that. We’re talking rather, about the attempt to build a science from scratch: one has a title for the discipline – sociology, say - and one then tries to figure out in advance what that science will consist in] . There is a standard yet, we think, wrong image of Kuhn which , in outline, is as follows:

The way to scientificity is simply the establishment of the dominance of a paradigm (disciplinary matrix) in one's subject. One needs to professionalize one's discipline around the central focus of the doctrines of one of its schools, and that's all.

The pro-Kuhn camp takes the message of this to be 'We just need a paradigm -- if we enforce agreement on a paradigm, then we can be a proper science. There's nothing more to being a proper science than that.' The anti-Kuhn camp takes the message to be 'Kuhn legitimates relativism and mob rule, because any group of people can 'get' a paradigm in that sense -- so the genuine sciences will not be able to distinguish themselves from pseudo-sciences if Kuhn's ideas are accepted'. Kuhn is saying that it will be in their own good time that disciplines acquire a paradigm, if ever they do. They cannot be frog marched into a paradigmatic state.

We are not trying to put into Kuhn’s mouth the argument that the social sciences cannot become bona fide virtually-indistinguishable-from-the-natural-sciences science. The line of thought we have just intimated carries no implications either way about how things will turn out , but certainly does suggest that, however they do turn out, there is nothing predestined about the development of a paradigm (or lack of same). Kuhn’s whole approach gives us no reason to assume anything other than that the emergence from pre-paradigmatic status is, so far as anyone can judge, a wholly contingent matter.

Mary Midgeley provides a useful example. Now, someone who had read Kuhn, and who as a consequence of such reading had come up with the popular thought that what one had to do was indeed to try to get the methods of one's own school to triumph as 'the scientific method' in psychiatry, would then presumably wage an essentially political campaign to demonstrate and enforce this, replete with accounts of how the beliefs of their school alone could enable psychiatry to understand itself and refine its methods and get lots of government money and be respectable among the medical community, etc. etc. The question is, would this be likely to be a productive thing to do? Would it be likely to hasten the advent of a truly scientific psychiatry?

Midgeley addresses these thoughts by means of querying in particular whether Materialist schools of psychiatric thought are pursuing their efforts to scientifise their discipline in a way that ultimately makes much sense:

[T]he reduction of mind to body is now seen as a major factor in determining diagnoses and methods of treatment. As two concerned practitioners in this field have put it,

"Despite the ambiguity and complexity of psychiatry, it is striking that many students begin its study with the appearance of having solved its greatest mysteries. They declare themselves champions of the mind or defenders of the brain . . . ...The unfortunate result is that many of them become partisans -- and needless casualties -- in denominational conflicts that have gone on for generations and that they scarcely understand." (Emphasis in original.)

As the authors point out, this metaphysical issue cannot be ignored. ...It is

"more than a question of taste whether we think about schizophrenia as a clinical syndrome . . . as a set of maladaptive behaviours, a cluster of bad habits that must be unlearned, or as an 'alternative life style', the understandable response of a sensitive person to an insane family or culture.

Each of these proposals makes different assumptions about the phenomenal world and its disorders, and each has different consequences for psychiatric practice and research . . . The result of ignoring the fundamental differences between perspectives is not to diminish sectarianism but, in the end, to encourage it."

‘ It seems reasonable to suggest that they would best be seen as viewpoints belonging to investigators encamped round the mountain of mental trouble. Yet the temptation to choose one and to take sides is extremely strong for a profession that feels the 'scientific' imperative compelling it to choose only one approach.

Thus Midgeley is claiming that the idea that there ought to be one of the existing schools triumphing in order to commence a glorious new age of normal science within a discipline which as yet lacks it is part of the problem, not part of the solution. The effort to make one's discipline scientific may well encourage sectarianism, rather than diminishing it, and to no productive end.

An approach to this question via the Feyerabendian critique of Kuhn

:Are Feyerabend's criticisms valid?

Bearing in mind our earlier discussion of 'paradigms' and 'normal science', let us focus in on one of Kuhn's rare direct remarks on the social sciences in this context:

In parts of biology -- the study of heredity, for example -- the first universally received paradigms are [really quite] recent; and it remains an open question what parts of social science have yet acquired such paradigms at all. History suggests that the road to a firm research consensus is extraordinarily arduous. (SSR 15)

The use of the word 'yet' might imply a teleological vision. And likewise the phrase that Kuhn uses elsewhere, 'pre-paradigmatic'. But just because certain disciplines have become ... disciplines, have become sciences, surely cannot imply that all will. For example, here is one possibility:

that the social sciences will eventually come to appear to most of us as astrology appears to most of us now -- as a pathetic attempt to ape science, failing due to its failure to have a genuine tradition of research, a genuine actionable set of problems and puzzles.

But the immediate point is this. We hope it will not be taken as a vacuity if we remark that Kuhn describes for us the structure of normal science and of scientific revolutions -- in those disciplines which do in fact fit the description. In disciplines which 'find themselves' with paradigms. In disciplines where the expression 'pre-paradigmatic' is not necessarily misleading ... because the discipline did as a matter of fact come to have a paradigm, come to be unified around an exemplar(s), etc. Kuhn lays down no advice or prognostication for disciplines without a paradigm. There is nowhere in Kuhn -- not in the quote given above, nor anywhere else -- a claim that one can confidently predict that in a discipline with schools, the eventual victory of one school can be confidently predicted. We do not mean simply: the victory of one particular named school. No, we mean the victory of any school, ever. Kuhn's claim concerning the emergence of paradigms is purely a retrospective claim. He is talking about the structure of the emergence of those disciplines that have become sciences. Not providing a manual for the creation of new sciences. He is, at least by implication and omission, pretty clear that that there can never be a guarantee that a discipline without a paradigm will acquire one, and thus no sense in which it can be obvious and perspicuous that (e.g.) the social sciences are well-conceptualized as on the road to normal science.

For the victory of a school, the construction of certain types of institutions is perhaps necessary. And certainly afterward. But this does not imply that it is a good idea to construct such institutions at any particular time. Nor that the construction of same will ever be enough. One needs to have sets of agreed-upon exemplars, common methods / ways of acting, and an absence of ongoing foundational disputes. There are strict limits to the extent to which any of these can be imposed upon others in the discipline unwilling to be imposed upon. One can try to suppress foundational disputes -- for example, through hegemony in a professional association or in educational institutes in a discipline -- but this is liable to be to some extent self-defeating, especially in any climate valuing academic freedom, etc.

Let us sum up. The attempt to force a victory of one school, the forced establishment of some dominant exemplars, and thus the imposition of a disciplinary matrix for the first time will normally result, not in a surer road to science, but in a surer continuation of the reign of 'schools'! Kuhn ought neither to be praised nor buried for having apparently given 'pre-paradigmatic' sciences a road or a menu toward normal science. Because, appearances to the contrary, he simply did not do so. Careful reading indicates that he did not even attempt to provide such a road or recipe.

For Kuhn aims to record primarily not what scientists say they do, nor what others say they do, nor what they think they should do, nor what others think they should do, but what they actually do. Thus it is off-target for Feyerabend to refer to Kuhn as having the 'belief' that scientists 'should not waste...time looking for alternatives' to a working paradigm; and for him to claim that Kuhn is saying that history can tell you the way science should be run science rather drastically misses Kuhn's point.

Feyerabend and Kuhn Again

But let us note also two positive moments of Feyerabend on Kuhn:

(i) Feyerabend, much more than the orthodox Popperians, found Kuhn’s concrete accounts of scientific revolutions impressive and highly suggestive -- suggestive of the extent to which such events are 'non-rational’, and even also have an aspect worth calling something like ‘incommensurability’ to them;

and

(ii) Rather more surprisingly, there can also be found in Feyerabend, if one searches it out, a different strand -- namely, a limited but real defence or explication of Kuhn’s normal science. In particular, Feyerabend helps us to account for something which can be elusive, something which was perhaps still partly missing in the previous section, and which Barnes does not supply in the slightest: that is, why Kuhn’s remarks on normal science are couched so thoroughly at the level of generality that they are, why they are not in fact concretely exemplified prior to (or at least after) the generalisations, why therefore it can rightly look as though what Kuhn is supplying us with is at ‘most’ the outline of a ‘philosophical sociology’. Here is Feyerabend, providing us with the materials to fill in that gap, to complete perhaps our account of (Kuhn on) normal science:

[In the analysis of science] historical research and not rationalist declarations must now determine the nature of the entities used, their relations and their employment in the face of problems and...a general theory of science must make room for these specific parameters. It must leave specific questions unanswered and it must refrain from premature and research-independent attempts to make concepts ‘precise’. Kuhn’s account perfectly agrees with these desiderata. His paradigms are ‘obscure and opaque’ not because he has failed in his analysis but because the articulation changes from case to case. The relation between theories and paradigms remains unresolved because each research tradition resolves it in its own way, in accordance with the cosmological, normative, empirical elements it contains.

Thus there can be a general account of normal and/or extraordinary science only at a very high level of abstraction and generality. Feyerabend makes clear that Kuhn’s paradigm concept is (thus) not pitched at an unacceptably high such level -- it could not be pitched otherwise, if it is to be pitched at all (if one is to do more than only tell specific historical stories -- and if one were only doing the latter, one would have entirely given up the philosophy of science ). If one attempts to make it more methodologically detailed and concrete, one is back (as Feyerabend sees it) to the fantasies of late-Popperianism and Lakatosianism, or to outright Positivism. If one wants a philosophy of science at all, at least for the purposes of uprooting other (wrong-headed) philosophies of science, one will inevitably then produce something more like a philosophical sociology than like a concrete first order sociology.

–

This highly-useful sympathetic (as opposed to warning/highly-negative) Feyerabendian interpretation of Kuhn even on normal science is to be found actually at a handful of important points in Feyerabend’s work; e.g. compare the following:

Understanding a period of science [according to Kuhn] is similar to understanding a stylistic period in the history of the arts. There is an obvious unity, but it cannot be summarized in a few simple rules and the rules that guide it must be found by detailed historical studies (the philosophical background is explained by Wittgenstein...). The general notion of such a unity, or ‘paradigm’ will therefore be poor and it will state a problem rather than finding a solution: the problem of filling an elastic but ill defined framework with an ever-changing historical content. It will also be imprecise. Unlike the sections of a theoretical tradition which all share basic concepts the sections of historical traditions are connected only by vague similarities. Philosophers interested in general accounts and yet demanding precision and lack of ambiguity...are therefore on the wrong track; there are no general and precise statements about paradigms.

What of the use that social scientists have themselves made of the concept of ‘normal science’? This is a question we will deal with in the concluding chapter of this book. But we need to turn without delay to the related -- but methodologically prior -- question which we have dramatised here as: Do you need a paradigm to catch a paradigm?

For there is one point further to the above arguments worth making here, in this chapter, and right away. What were folks expecting when they expected that Kuhn’s ‘Structure’ should show them a way forward for the human sciences, for their own social discipline, along the sure road of science? These people, these sociologists and political scientists and psychologists and anthropological linguists, and perhaps also literary and art critics and historians and students of religion, were presumably expecting that Kuhn was pointing them toward something beyond his own practice. But if they had looked at that practice rather harder for rather longer, they might not have been so expectant that it would provide them with something radically new, with the outline of how to get hold of a paradigm for their use.

For one is struck, if one notes the listing of disciplines just made, that Kuhn himself borrows something from each of them. That is, one could well bear in mind his use of metaphors from religious studies and politics, his analogies to art history, his use of methods from textual criticism, his borrowings from gestalt psychology and from Sapir-Whorf, not to mention his straight history (and sociology). So: Kuhn’s own practice draws far more on the practices of the human sciences and the humanities than does that of any other major philosopher of science. Kuhn is to some considerable extent himself a human scientist. As intimated above, Kuhn’s own approach can be modelled on that of a natural scientist (and thus his account of scientific revolutions self-applied) only at considerable cost, or with considerable care. Kuhn is doing philosophy, and is doing it after the fashion of interpretive human science far more than most philosophers of science (some of whom attempt to draw more on Logic, or ‘Cognitive Science’, or to build their own ‘(philosophical) theories’ of science, for example).

He attempts to ‘capture’ how science works through employing the concept of ‘paradigm’, etc. . And one hopes that what Kuhn is finding is not wholly of his own invention. In other words, one hopes that ‘paradigms’ are actually already there in the social practices of the communities etc. which Kuhn is talking about. In other words, Kuhn encourages one to look at the sciences and to see if one finds paradigms there. Paradigms are already objects of Kuhn’s philosophical sociology. Exemplars and disciplinary matrices are both constitutive of the order of scientists’ practices in a normal science situation. And again, they pre-exist Kuhn’s description of them, they are not just artefacts of Kuhn’s writing (unless Kuhn is quite wrong -- in which case no-one would need worry about his lessons for the social sciences).

Now, what is it that human scientists more generally do? Is it not something very similar? For example, a sociologist looking at any set of practices, be they what they may, or an anthropologist looking at an ‘alien’ society; are they not in search of the beliefs, methods of acting, tacitly agreed norms etc. among the people they are looking at? Are they not in the business...of describing these?

We are suggesting the following: that, rather than taking inspiration from the content of Kuhn’s descriptive history of the natural sciences, rather than looking for a paradigm to guide and enforce limitations on their own practice qua social scientists (an enterprise liable to be useless or even counter-productive as argued earlier in this section), social scientists could profitably look instead to Kuhn’s version of their practice as he himself employs it. Social scientists could usefully think through the sense in which their own practice is already the searching out and describing of paradigms and their ilk. Do they need a separate paradigm of their own to do that properly? Might it not rather hinder their task? Take our sociologist, looking (say) at some set of religious practices and beliefs. Isn’t Peter Winch right in saying that "...the sociologist of religion will be confronted with an answer to the question: Do these two acts belong to the same kind of activity?; and this answer is given according to criteria which are not taken from sociology, but from religion itself." (ISS, p.87). Why? Because:

The concepts and criteria according to which the sociologist judges that, in two situations, the same thing has happened, or the same action performed, must be understood in relation to the rules governing sociological investigation. But here we run against a difficulty: for whereas in the case of the natural scientist we have only to deal with one set of rules, namely those governing the scientist’s investigation itself here what the sociologist is studying, as well as his study of it, is a human activity and is therefore carried on according to rules. And it is these rules, rather than those which govern the sociologist’s investigation, which specify what is to count as doing the same kind of thing’ in relation to that kind of activity.(ISS, p.87)

Similarly: the appropriate criteria for deciding whether two people are engaged in the same kind of activity -- are both testing a particular hypothesis or not, say -- belong to that activity -- say, the specific science in question -- itself. At times of paradigm-shift, there may suddenly be divergent decisions among scientists on such issues, such decisions.

Let us sum up the above. Kuhn’s ‘fans’ say: Social science needs a paradigm (that doesn’t exist yet). We say: Social science is about, among other things, finding paradigms that exist already, in social settings. (And what one surely needs to do in relation to such paradigms is to describe them, to be responsive to them as they already exist, not to impose an alien theory onto them.)Students of society should not think of the practice of finding paradigms and exploring their nature descriptively as radically new. Kuhn did what they have already been doing, to a considerable extent (and vice versa, now). And what they do looks very different from what natural scientists do -- for the latter, unlike the former, do not have as their business anything like the description of paradigms. If they ‘explore’ paradigms, it is in the utterly different sense indicated in earlier chapters -- through theorisation, experimentation, etc. And the point we have made is that one has no particular reason to think that the human sciences will profit from aping such methods. For they need essentially to explore something like paradigms which already exist, rather than creating a new one. They need to effect a description of a set of human practices, a set of practices which do not necessarily need to have a paradigm or a set of categories or such like imposed upon them in order to become interpretable, for they already embody such a set of categories. They may even be argued to be correctly describable in principle in a sense unavailable to natural scientific inquiries, because there is no such thing as describing the non-human-world in a way that the latter prefers. Whereas perhaps the human world truly can be ‘cut at its joints’ (!) -- by a description that respects it and (simply) gets it right, gets it in terms accurately reflecting participants’ self-understandings and ordered activities. Paradigms and their ilk already exist -- in social action (e.g. of scientists).

The ‘Kuhnian’ apologists for social science may, in their desperation for respectability, be overlooking this possibility, the possibility that careful description of social action, of paradigms etc., may as Mary Midgeley among others suggests, already be possible (‘even’ in disciplines -- the social studies etc. -- without a paradigm), provided one doesn’t get sidetracked into fighting for dominance of a would-be social science. And let us be quite clear about this: the wish of Kuhn’s cruder fans or appliers to ape natural science by means of ‘getting’ a paradigm, finding their own Newton, is deeply ironic. These people, who think that Kuhn has proven a kind of Relativism to be true, are still -- at the very same time -- wanting to have the kudos of being recognized as scientists, by means of having a paradigm to unify them and the paraphenalia of professionalism to maintain and enforce the unification. But this shows that they are still vulnerable to the attractions of Positivism or of ‘Scientific Realism’. If they really had the confidence of their Relativist convictions, they wouldn’t care about how the natural sciences conducted themselves, they wouldn’t try to ape science as described by Kuhn or whoever -- they would boldly strike out in their own direction, they would rest content with self-generated criteria for how, if at all, to distinguish between good and bad ways of structuring their discipline, good and bad work within their discipline. It is in fact a sign of deep disciplinary insecurity that one calls upon a philosopher of science to supposedly legitimate one’s own discipline as being ‘just as good’ as the natural sciences. It makes no difference, whether one hopes to do that by pulling one’s own discipline up to their level or pulling their discipline down to one’s own level. . .

The alternative of course is for ‘the social sciences’ to regard themselves as truly sui generis, as not needing to look to methodological aspects of the sciences with paradigms in order to validate themselves. This can only be done if more or less one accepts the current state of one’s own discipline, ducks out of endless methodological debate (except insofar as it is necessary to puncture the aspirations of those, for example, who have been criticized above) and gets on with doing what good work can be effectively done within that discipline. For example, perhaps: in sociology, good ethnographies and descriptions of very diverse social practices. Including (but only as one case among many) of scientific practices.

The community of practitioners has to actually be impressed by - has to actually pretty much universally recognize - a scientific achievement, and take it for a paradigm. If that doesn’t happen, then too bad -- you don’t have a science.

Kuhn does not well very much on borderline cases of (mature) sciences. One extrapolates to these cases at one’s peril -- our interpretation of the true (and small, if you like) impact of Kuhn on the philosophy of the social sciences is far less perilous a way to go. And we have been clear that Kuhn was not in the business of laying down norms for how to get paradigms, nor saying that ‘getting’ a paradigm is always possible.

The clinching piece of evidence for our interpretation, with which we end this chapter, is from Kuhn’s longest, if still fairly brief, consideration of an example from the social sciences in SSR. We have already mentioned the moment, let us now dwell upon it:

Why should the [scientific] enterprise...move steadily ahead in ways that, say, art, political theory or philosophy does not? Why is progress a perquisite reserved almost exclusively for the activities that we call science?

Notice immediately that part of the question is entirely semantic. To a very great extent the term ‘science’ is reserved for fields that do progress in obvious ways. Nowhere does this show more clearly than in the recurrent debates about whether one or another of the contemporary social sciences is really a science. ...Men argue that psychology, for example, is a science because it possesses such and such characteristics. Others counter that those characteristics are either unnecessary or not sufficient to make a field a science. Often great energy is invested, great passion aroused, and the outsider is at a loss to know why. Can very much depend upon a definition of ‘science’? Can a definition tell a man whether he is a scientist or not? If so, why do not natural scientists or artists worry about the definition of the term? Inevitably one suspects that the issue is more fundamental. Probably questions like the following are really being asked: Why does my field fail to move ahead in the way that, say, physics does? What changes in technique or method or ideology would enable it to do so? These are not, however, questions that could respond to an agreement n definition. Furthermore, if precedent from the natural sciences serves, they will cease to be a source of concern not when a definition is found, but when the groups that now doubt their own status achieve consensus about their past and present achievements. It may, for example, be significant that economists argue less about whether their field is a science than do practitioners of some other fields of social science. Is that because economists know what science is? Or is it rather economics about which they agree?

Here is the crucial difference between naturally acquiring something like a paradigm, and merely striving deliberately to get the trappings of one. Kuhn’s ‘followers’ and his ‘antagonists’ alike confuse the latter with the former.

Can we get Kuhn off the charge of ‘semantic relativism’? (Do we need to?)

Kuhn has been attacked not only by the leading philosophers of science, but also by the leading American philosophers of his time, and the most important of these – such as W.V.O. Quine, Donald Davidson and Hilary Putnam - have accused him of a semantic relativism that is self-defeating, involving a fundamental, and almost elementary mistake. Does Kuhn say that there are irreducible discrepancies in meanings between different scientific theories, between different cultures, between languages, so that systems of meaning are reciprocally closed? Put in the way the issue actually came to be discussed: is it possible to translate without loss between one 'system of meaning' and another? In defending Kuhn against these critics we do not suggest that it is all down to their misconceptions of what Kuhn says, for the determination of what Kuhn means by what he says on the issue at stake here – incommensurability – is not easy. Nonetheless, we will deny that Kuhn’s argument has the fatal flaw that these critics allege.

Kuhn says that pre- and post-revolutionary scientists ‘live in different worlds’ (SSR 121) and, unlike Feyerabend and Imre Lakatos, insists that they can only live in one world. The scientist is always ‘in the grip’ of one paradigm, that which is dominant at the time. The scientist, therefore, cannot understand what came before the revolution? But if the scientist cannot understand more than one paradigm, then how can the historian or philosopher hope to? But Kuhn, as either historian or philosopher, then seems in this impossible situation: he tells us that we cannot understand previous science, and yet writes case studies to explain previous science to us.

Donald Davidson’s attack on ‘conceptual relativism’ in ‘On the very idea of a conceptual scheme’ is heavily sarcastic about Kuhn in this respect: Kuhn wants us to imagine radically different – incommensurable – conceptual schemes in science and is also aware that we can only ever be in one of those. How then can Kuhn possibly understand those different to his own, let alone understand them in a way which enables him to explain them to the rest of us? So it is a mystery as to how, if two things in the same field are incommensurable we can understand both well enough to see that that is what they are. Surely, if incommensurability is a strictly semantic matter, then we cannot think of both paradigms, hold them in mind, and then ‘notice’ the incommensurability. If they are incommensurable, then that’s that: any paradigm other than our own must be effectively unrecogniseable to us. (It would seem a result, then, that we cannot even assert the thesis of incommensurability itself.)

Literally, incommensurability means the impossibility or unavailability of a common system of measure. The idea originally comes from mathematics, from the shock which the Pythagoreans long ago got from realising that there must be numbers which are not expressible as fractions, which are not ‘rational’. This in fact follows almost directly from a thorough understanding of Pythagoras’s law concerning right triangles. If one has a right isosceles triangle, and if each of the shorter sides are one unit in length, then the hypotenuse, by Pythagoras’s law, must be the square root of two units in length. So there is an object in the real world which can be shown to be the square root of two units in length. But it can easily be mathematically shown that the square root of two is not a ‘rational’ number; for if we suppose it to be a ‘rational’ number, then a contradiction follows.

Therefore there are objects the length of one of whose sides is in an important sense not comparable to the lengths of the others. The latter can be expressed as fractions, the former simply cannot. There is in other words no common system of measure, in a certain important and quite intuitive sense, to (e.g.) the sides of some right triangles. The ‘irrational’ numbers are ‘incommensurable’ with the ‘rational’ numbers.

[[[Fig. here]]]

Fig. 1

(A ruler, however minute its divisions, could not measure side c absolutely accurately if it could measure sides a and b absolutely accurately. The measurements in question can be done successfully in ordinal terms, and indeed to any arbitrarily-required degree of accuracy; but there is always the possibility of demanding that the measurements be done more accurately, at which point the ‘incommensurability’ will again be evident.)

This idea is taken up by Kuhn and Feyerabend and applied to science, where it would appear that there may be measuring schemata -- schemata to ‘measure the world’ with -- which are not intertranslatable without loss of data or meaning. However, one should note that there is a sense in which the mathematician can nevertheless describe the ‘incommensurable’ numbers perfectly well -- otherwise one couldn’t understand the incommensurability just described in (we hope) an accessible way! And there are ways in which the numbers -- the lengths -- in question can be perfectly effectively compared: e.g. We can say that the square root of two is greater than 1.4, less than 1.5, etc. etc. . Similarly, Kuhn & co. must be able to describe to us the incommensurability they are concerned with, on pain of there being no idea that they are putting forward here. The question will be whether this necessity of their being able to express the incommensurability means that it cannot cut very deep at all. E.g. Must any lack of intertranslatability perhaps be absolutely marginal/minute, as seemingly it is in the maths case?

Slightly metaphorically -- and this is of the essence of incommensurability according to Kuhn (Feyerabend argued at times for a similar version) -- the idea he seemingly wants is that there may be ways of doing science, weltanschaungen, paradigms, which are logically discontinuous: they don’t simply contradict each other, since they are different in ways which deny them the resources respectively to make statements which flatly confront each other. If they could do that they would be commensurable, but they can’t. And it is at the least an open question whether the mathematical analogy alone will get Kuhn all the way to this.

One of Kuhn’s key examples of incommensurability, as we have already noted, is the transition from Newtonian to Einsteinian physics. One cannot fault Kuhn for bravery here. He takes on his opponents on one of their strongest turfs. For it is a virtually a verity, and a widely-accepted one, that Newtonian mechanics is true as a special limiting case of Einsteinian Relativity (SSR 97-98). Popularizing scientists and philosophers alike have thus found in this famous case a prototypical example of the traditional image of scientific progress: the prior view remains true, but only within a restricted domain of application, while scientific knowledge grows seamlessly to cover novel cases efficaciously, cases for which the prior view was false or inapplicable.

Here is the heart of Kuhn’s account of how, even though it appears that Newton’s Laws can be derived from Einstein’s relativistic dynamics, this appearance is actually delusive:

"[T]he physical referents of [the] Einsteinian concepts are by no means identical with those of the Newtonian concepts that bear the same name. (Newtonian mass is conserved; Einsteinian is convertible with energy. Only at low relative velocities may the two be measured in the same way, and even then they must not be conceived to be the same.) Unless we change the definitions of the variables...the statements we have derived [from Einsteinian Relativity, in an attempt to show Newtonian mechanics to be a special case of the latter] are not Newtonian. If we do change [the definitions], we cannot properly be said to have derived Newton’s Laws, at least not in any sense of ‘derive’ now generally recognized. [The] argument [of those who would derive Newton from Einstein] has, of course, explained why Newton’s Laws ever seemed to work. In doing so it has justified, say, an automobile driver in acting as though he lives in a Newtonian universe. An argument of the same type is used to justify teaching earth-centred astronomy to surveyors. But the argument has still not done what it purported to do. It has not, that is, shown Newton’s Laws to be a limiting case of Einstein’s. For in the passage to the limit it is not only the forms of the laws that have changed. Simultaneously we have had to alter the fundamental structural elements of which the universe to which they apply is composed."

The last point is crucial. Kuhn argues that Newton and Einstein take the universe to be populated by different fundamental entities. There is no way, he is saying, for one to inter-translate between the two without obliterating this vital fact. If one reads (e.g.) the word ‘mass’ differently from how it was read under the Newtonian paradigm, one cannot literally be claiming to derive Newton’s laws. In scientific revolutions, the furniture of the universe changes. And there is no neutral further language in which to describe this furniture (SSR 114-5, 125-7). There is only, normally, the language of the victors, which tends either to make its predecessor look stupid and bizarre qua scientist, or to make it look like it was always really trying to be its successor. Thus Newton is made to look ‘proto-Einsteinian’, usually. Alternatively, he could be treated as for example Aristotle sometimes is -- as a great philosopher, but as someone whose physics (whose dynamics, especially) is just ‘crazy’, and hardly worth calling ‘science’ at all.

To put it another way: insofar as Einstein superseded Newton, this could actually only be so in tandem with the belief that Newton was wrong -- Einstein didn’t show that Newton was a special case of his own, new, view. (Of course, we must be very careful, if we say this; we must bear in mind that for Kuhn there is never simple refutation, never a crucial experiment that one must be convinced by; the observations of Mercury during the eclipse which are sometimes taken as a crucial experiment that proved Einstein’s theory correct depend on so many further assumptions etc., and were in any case only achieved well after Einstein’s theory had largely won the day -- on no ‘evidence’ at all, one might say. One might then say that for Kuhn there is only refutation as such when there’s no contest any more, i.e. in a context of pure justification alone. The refutation is only clear when one theory has been decisively accepted at the cost of another -- but by that time, the other is hardly understood at all; and, if understood at all, probably only by means of the efforts of historians and philosophers of science. One makes the predecessor looks a stupid, or bizarre and crazy in their views such as to be not really a scientist at all, or (often best of all) rather like oneself. All three can be Whiggish strategies, but the third is the most effective if it can be pulled off, for then it becomes impossible to read the predecessor as themselves. They read rather as if they’ve been trying to be you all along, as if they’ve read you, but ill-understood you.)

Can’t one still say that "There just isn’t mass like Newton said there was; his classification system was wrong; mass a la Newton doesn’t refer"? We can respond to the question briefly (and effectively) as follows: No. One can’t unmisleadingly say that, because classification systems in themselves are not true or false. Only things that are said using classification systems can be true or false; but then there has to be some ‘system’ within which their truth or falsity is assessed. So: we can if we wish say of Newtonian statements about mass that they are in some instances false because they fail to connect up with reality at all: But then we’ll be already tending to misread them; we’ll already be reading them from the perspective of the Einsteinian paradigm or some such.

We can’t simply say " ‘mass’ a la Newton doesn’t refer", except as an elliptical way of already making the same Einsteinian critique of Newton. (‘Reference’, for Kuhn, does not make a magical connection between words and world, but refers (!) to what a Relativist would call a purely ‘intra-paradigm’ phenomeon.). To say (e.g.) " ‘mass’ a la Newton doesn’t refer" is only to show that we have already accepted Einstein’s system. That system is / must be authoritative for us, now, qua physicists or scientifically-informed laypersons.

Much as the Einsteinian could truly and non-question-beggingly say, "We just don’t use the term ‘mass’ in the way that Newtonians did; we have good reason to believe that the theories one gets out of using it that way will be less good than those we can get out of talking a la Einstein instead." It’s not exactly that one can’t use the term ‘mass’ in the old way (except in certain restricted and simplifying/pedagogical contexts), it’s that we just don’t. We don’t take that usage seriously. Except if we are interested in understanding the history of the discipline. And again, what natural scientist qua natural scientist should have to be much interested in doing that?

Understanding as translation.

Let us go deeper into the question of understanding science, understanding past scientific ideas. As we have said, argument about incommensurability gets turned into argument about translation - because the two hugely influential philosophers, Quine and Davidson both think that understanding is pretty much the same as translation. Clearly, in one respect this is true but it is surely a mistake to tie understanding and translation [ or ‘interpretation’ as Davidson calls it] entirely together as Quine/Davidson do, attempting to understand the first in terms of the second .

The idea that understanding and translation are wedded might seem persuasive, for surely to understand someone else’s ideas is a matter of being able to put them into words that we ourselves can understand? Thus, if someone speaks to us in a foreign tongue, we cannot understand what they say, for we cannot understand their words. To understand them we must put their words into our English ones. ‘Translation’, however, does not apply, in the thought of someone like Quine, only to transactions between a foreign and our native tongue, but also to cases that are within ostensibly the same language. We have to assume that the words of the other speaker are used with the same meaning that our words have, that they do translate into our own meanings.

Kuhn is thus being drawn into one of the central disagreements in modern American philosophy, reflected in the following quotation from Hacking, over whether there can be any unique, determinate, translation between one language and another:

"There are three philosophical fantasies that we could label ‘too much’, ‘too little’, and ‘just right’. The just-righters...claim there is just one right system of translation between any pair of languages... Philosophical debates currently [1975; and still to quite a large extent in 2001] focus on the claim that there is too much free play between languages to determine any uniquely best system of translation. The most famous exponent of this is Quine, who calls it the indeterminacy of translation. Imagine that we observed all there is to observe about speakers of an alien language. We know every occasion on which any sentence was, is, or will be uttered, and we know all the observable precedents and consequences of each such occasion. We even know how speakers of that language are disposed to talk in situations they never in fact experience. In short, we know infinitely more than any radical translator [an anthropologist encountering a quite alien language] ever could know. Even if we knew all that, there are, claims Quine, indefinitely many mutually incompatible systems of translation that would square with the data.

Quine urges that there is too much possibility for translation. The opposed doctrine maintains that there is too little. Two human languages could be so disparate that no system of translation is possible. This is in the spirit of Feyerabend’s doctrine of incommensurability.’ [Why Does Language Matter to Philosophy, 151-2).

Hence, the problem of incommensurability tended to be conceived by both the critics and by Kuhn himself to be one of the possibility of translation. Kuhn is willing to say that his doctrine of incommensurability does signify the impossibility of thoroughgoing translation between two different scientific schemes. Cast in those terms, and understood in the context of the continuing debate over translation, Kuhn seems to confront the following difficulty: in denying that there can be translation between two schemes, either

[a] he is wrong in that there can, there must be translation between such schemes, and his whole (philosophical) project collapses [since it is, for Kuhn to maintain his ‘incommensurability thesis’, essential to make the case that there is no such possibility], or

[b] he is right, there is no translation between them, in which case, his whole (historical) project collapses [since he, no more than anyone else, can translate a defunct paradigm into our contemporary one, and hence cannot possibly explain their world view to us].

Davidson insists (supported by specific philosophical reasons than need not matter to us here) that we should not call something a language that we could not translate into other languages. Therefore, the idea of separate ‘conceptual schemes’ between which there would be no translation does not hold up. If conceptual schemes are things between which we cannot translate, this means there can be no such things as distinct conceptual schemes. Thus Davidson believes that Kuhn clearly should abandon incommensurability [a], but that, given that Kuhn plainly does not want to do this, that he (Kuhn) ends up in position [b], without the ability to say the specific things about episodes in the history of science which apparently prompted his serious turn to philosophy in the first place.

We believe that Davidson however does not allow Kuhn any philosophical space, that he unduly restricts the room for manouevre that there is on this issue – that, in effect, he is much too quick, and as a result begs the question against Kuhn.

Let us begin our concrete response to Davidson with what might seem a relatively small point: Davidson too readily generalises Kuhn’s argument to ‘language’ from its designed application specifically to the case of scientific scheme. Davidson may be right about the context of conceptual-scheme talk vis-a-vis natural language, but this is really irrelevant to Kuhn’s argument. Like Davidson, and unlike Sapir-Whorf, we think that English and French (and even Hopi) are not usefully regarded as constituting or directly yielding different conceptual schemes. But does that imply that theoretical systems of science etc. are not reasonably called conceptual schemes? No; philosophical work would need to be done to make the implication go through. As we discussed in Chapter 32 above, Kuhn, in his account of the Copernican revolution identified some functions for conceptual schemes, such as those of saving on memory, facilitating the working out of implications and so on. Kuhn would not have needed to e.g. identify the Ptolemaic system as a conceptual scheme, nor to make arguments about the functions of such schemes if he had regarded conceptual schemes as identical with natural languages. Part of Kuhn’s specific point about ‘scientific’ conceptual schemes, which he later came to emphasise strongly is that their constituent terms are inter-defined. Thus, Davidson’s denial that different languages house different conceptual schemes does not directly contradict Kuhn’s insistence that the Ptolemaic astronomical system was developed into a conceptual scheme.

Further, we have mentioned (000) the ambiguity in Kuhn’s initial formulation of incommensurability as something that might be understood as either thoroughly globalised or highly localised. Kuhn later unequivocally disambiguates his meaning: incommensurability is a local thing, even in the context of a scientific theory, something which affects only those areas of a science in which there are inter-defined terms. Thus, the impossibilities of translation between conceptual schemes of the kind Kuhn has in mind are partial only.

What’s more, Kuhn never said that it was impossible for scientists to understand their predecessors. Kuhn said (documenting his claim with historical research) it was possible for them to do so, and that they did do this, even that there were conditions (incommensurability being one) favouring both likelihood of misunderstanding between rivals in a revolutionary period and of retrospective misinterpretation of prior work. This is, for Kuhn, an unsurprising fact, a consequence of his argument that it is impossible to translate entirely between two conceptual schemes. One cannot express, in the terms of one theory, everything that can be expressed in the terms of the other. But this does not make understanding both paradigms impossible, only very tricky, requiring (imaginative and historical) effort, work.

Kuhn does not, therefore, accept that understanding and ‘translation’ are wedded in the way that Quine and (especially) Davidson think they are.

In understanding how Kuhn can insist both that translation is impossible, and that understanding of ‘different conceptual schemes’ is possible, we need to look again, and more suspiciously, at the idea of translation. Quine’s and Davidson’s idea of what translation is should not be thought of as being the same as that which is involved in translating French speech into English as we ordinarily go about this. We have words in English such as ‘totem’ which are words that could not be translated into English. That is, there was no single word in English which meant what ‘totem’ meant in the languages that explorers encountered, so, of course, we have added the word to English. We could not, then, translate ‘totem’ into English, in the sense that we could not identify one word which would (did) match the word. Of course, we could get English speakers to understand the word ‘totem’ easily enough, by doing a lot of explaining [in English] about the people who used the term, how it fitted into what they do and, thus, what they meant by it.

Kuhn himself, of course has been busy ‘translating’ historical science, sometimes written in now-defunct tongues, into English; but, of course, his ‘translating’ is not a matter of matching word for word the texts which express those ideas, but of giving us elaborate explanations of their meanings, which draw upon much more than narrow linguistic understandings.

Are we now ourselves disagreeing with Kuhn and saying that he is wrong: translation is possible, he does it himself? Worse, are we impaling Kuhn on a deadly (and more or less Davidsonian) contradiction: he denies that it is possible to translate at the same time as he is doing exactly that? In fact, we are drawing attention to the fact that the claim that translation is impossible depends essentially upon what one understands by ‘translation.’ Here is Kuhn:

"I [suggest] that the problems of translating a scientific text, whether into a foreign tongue or into a later version of the language in which it was written, are far more like those of translating literature than has generally been supposed. In both cases the translator repeatedly encounters sentences that can be rendered in several alternative ways, none of which captures them completely."

What Kuhn is denying is that the kind of translation that Quine and Davidson ostensibly seek is available between two ‘conceptual schemes’. In principle, a translation would give, for each sentence in one language, a sentence in the other language that would match it in meaning, and one could do this for all the sentences in the two languages. But what if the sentences were incredibly long? What if the ‘sentence’ needed to translate a sentence from a scientific text was actually the length of a monograph, having to go into all the historical conditions and sensibilities etc. involved in the old conceptual scheme, so as to avoid missing its real ‘meaning’?

Now Kuhn’s objection has become clearer: it is that between two different scientific systems it may [sometimes] be impossible to find for certain terms in the one system any terms in the other that match them in meaning. It may just be that one system has, and the other recognisably lacks, a term (as with the totem example). It is obvious that modern physics has no term which corresponds to ‘phlogiston’. But: Any term or even any longer phrase which one might hope to get to correspond with phlogiston characterises the world in a way which cross-categorises with modern Physics’s way – the two cannot be rendered compatible. Sometimes, it may be that it looks as if there is an appropriate term, as if the two systems share the term in question. This may be a delusion, and even though one can produce a sentence in system one which matches word for word a sentence one can construct in system two, it still may be impossible to claim these two sentences as translations for each other! Why? We can give a first approximation to an answer in the following fashion: Because some of the words differ in (one thing one can mean by) ‘meaning’, as with the example we (following Kuhn) have used: ‘mass’ in Newton’s scheme does not mean the same as ‘mass’ in Einstein’s. So, the word-for-word resemblance between matched sentences of the two schemes would be superficial only. Translation is meant to match two sentences that mean the same, and assertions in Newton’s scheme about mass just don’t mean the same as they do in Einstein’s: in the sense that the two matched sentences would lack the same ‘feel’, the same detailed set of interconnections. The only way one could get that feel or atmosphere, that same set of detailed interconnections, would be through a large-scale exercise in history, philosophy and imagination – i.e. through the kind of thing that Kuhn pursues in greatest depth in his case studies. And it would be odd indeed to say that the translation of (say) ‘The Earth is at the centre of the Universe’ is to be found simply in the totality of the argument of The Copernican Revolution. Better to say, not just that there is no point for point translation between some Ptolemaic and ‘Copernican’ statements, but that there is an important sense in which they cannot be inter-translated at all. Would one call something a translation into Russian of "A bird half wakened in the lunar noon; Sang halfway through its little inborn tune", if it was the length of a book, in order to capture all the possible allusions of the lines in English etc. etc.?

The impossibility of translation in the word-for-word, sentence-for-sentence sense follows from the nature of scientific systems, or conceptual schemes as Kuhn sometimes terms them. These schemes have internal interdependencies, and some of the vocabulary may be interdependent. Kuhn’s point applies to cases in which terms are interdefined. If that is so, if a term’s meaning (its use, broadly considered) hinges upon its relation to certain other terms, then to pluck the term from that context is to divest it of its meaning. One cannot just transplant that word to another system: attempting to do so will simply result in changing its meaning because one will be relating it to a different set of interdefining terms. Thus, where two scientific systems are closely related as rivals paradigms there will be points at which no translation of particular sentences between them will be possible because the key terms cannot be isolated from the respective vocabularies of the two schemes.

Let us recapitulate what has been shown above. The failure of 'point-by-point' translation is important, but not the conclusion of Kuhn’s argument. The point which Kuhn brings out particularly in his consideration of attempts to translate between phlogistonic and 'modern' chemistry is this: that not even long 'paraphrases' or complicated multiple uses of symbols can be usefully said to 'capture', to translate, phlogistonic chemistry:

"We have not only to say that phlogiston sometimes referred to hydrogen and sometimes to absorption of oxygen, but we have to convey the whole ontology of phlogiston in order to make plausible why it was taken to be a single natural kind."

The work of attuning oneself to a different sensibility is the work of interpretation. It may in some cases, even if carried through to the maximum feasible degree, not result in what Kuhn wants to call a translation, in, we might, say, the full sense of that word. Because sometimes, Kuhn thinks, there is no such thing as a translation available between two modes of thought. They are not missing a common currency in the sense of some extractable sense, or 'sameness of extension'; but these only apply in an intra-paradigmatic sense. There can be different modes of thought, styles of reasoning, 'grammars', whose difference can be 'detected' by the intelligent work of history, and by an 'aesthetic' sense.

Equally important to Kuhn’s rebuttal of the accusations on translation is his assumption that understanding comes before translation. It is perhaps appealing to think of being unable to understand something said in a foreign language, and then being able to understand it because it is translated. It is important to understand, now, that it is a distinct peculiarity of Quine’s to think that the same point applies to our own language too, that when someone speaks to us in words that seem exactly like our own English words, nonetheless we are involved in translating them into what we imagine are our own equivalents. Quine may have philosophical arguments to justify treating understanding that way, but we are not trying to resolve the dispute between him and Kuhn, but to point out that the two are at cross purposes.

Kuhn treats the native and alien tongues case as different, in accord with our more usual idea that we translate between two different tongues, not within the same one. Then the apparently persuasive link between understanding and translation collapses. We did not learn to understand our native tongue through translation. When we acquired our mother tongue we had no other tongue to translate it into. Thus, we learned our native tongue directly, we learned to understand it from scratch. Thus, understanding proceeds independently of translation in this case. In the case of translation between two tongues, think of it from the point of view of the translator, rather than from that of ourselves as people who understand what someone said in another language because someone puts it into our own for us. Someone who translates has to be able to understand both languages before they can translate. Someone who understands French cannot translate passages in French for us if they have no English. Thus, it is only someone who understands both languages who can establish that one language has a word ‘totem’ for which the other has no equivalent.

The historian of science is like the anthropological visitor to a remote tribe, having to start to learn their language from them, even from scratch. A bilingual understands both languages, but that does not prevent there being parts of one language which cannot be translated into the other [the word ‘television’ might present such a problem for a language other than ours; much more serious difficulties, difficulties which cannot even in principle be solved merely by the addition of a new word into the other language, are presented by literary language.].

Let us summarize Kuhn's conception, especially as laid out in his later works, of his views on incommensurability, as expressed through the concept of translation:

Interpretation, a fundamentally hermeneutic concept, is suggested by Kuhn to be fundamental to understanding another language (or whatever) when one does not already understand that language. [Thus, importantly, Quinean 'radical translation' is better read as a kind of interpretation, according to Kuhn.]

Bi-Lingualism results, if one manages fully to acquire the new language.

Translation, is possible only when one can move between the two languages in a manner which enables one to 'capture' in the one language what is happening in the other. Slightly less vaguely, one must be able to follow and render the network of significances and associations that matter to meaning, in a 'full' sense of that word, before one can be said to be able to translate.

It is worth mentioning Peter Winch’s (1964) arguments about some problems in understanding an alien society, which involve very similar concerns and responses to Kuhn’s, but also make explicit something that is only implicit in Kuhn.

Kuhn had compared the historian of science’s difficulties to those of an anthropologist who must come to terms with another society with very different ways than the anthropologist’s own.

Winch, treating these kinds of difficulties as in a way representative of general problems in the social sciences focussed on a specific case, that of understanding a tribal society that engages in magical practices of the sort that can seem quite incomprehensible and bizarre to us. How can people possibly believe that the things that they do can work? Winch’s effort, in their case, is very much the same as Kuhn’s with Copernicus and Planck: to show that this question poses a false problem, that if their way of thinking is properly identified, if its terms are fully elaborated, then we will come to see that the fact they can and do engage in those practices is no more problematic for them than it is for us to be fully immersed in our own practices. The problem, Winch is arguing, arises not from the nature of the alien belief system itself, but from our assumption that our way of thinking is not only the correct one, but that it is utterly obviously so. Unless something prevented those people from doing so, they would naturally see the world the way we do – Winch, like Kuhn, wants to remind us that our way of viewing the world is by no means ‘the natural one’ [for there is no such thing as what one tends to want from that expression], and the impression that it is the natural and obvious one results from our familiarity with and immersion in it, not from our understanding of how we came by it in the first place or of the ways in which it resembles or differs from other ways that people have also found persuasive.

What does Winch make explicit that Kuhn does not? As we have presented the argument over translation there seems to have been an attempt [by Davidson] to force a choice between two extreme positions. Either we deal with different conceptual schemes, which are utterly closed to each other, so that the inhabitant of one cannot possibly understand another or it is impossible for there to be serious divergence between two systems because they must be fully translated one into the other. We have established that Kuhn does not fall into either of those positions, and that there is room for him (and Winch) to take up in between them (or, if you prefer, orthogonally to them). This, of course, is by virtue of Kuhn’s holding, as he actually does¸that two scientific schemes are neither wholly closed against each other nor fully translateable one into the other. Winch’s point is that attempting to understand an alien system is not just a process of ‘translation’ but is one of learning, a matter of changing ourselves and adding to our own conceptions - we do not understand an alien society by absorbing what it does to what we do, but come to accurately appreciate the difference between our ways and theirs, recognising that we have been apt to treat such cases in the past with condescension, rather than understanding. Thus Winch makes readily apparent – makes explicit -- an intermediate ‘position’/possibility between ordinary understanding on the one hand and sheer nonsense / nothingness on the other: namely, what it is to understand something worth calling different … something which can be understood only by an effort of imagination or analogy, something which resists one’s categories. Something, for example, like a genuinely new philosophical idea. This ‘intermediate position’, providing one sees it, shows that and how Davidson begged the question in "On the very idea of a conceptual scheme"; and how one can say the kind of thing that Kuhn and Winch want to say, without committing oneself to a self-refuting ‘semantic relativism’.

We’ve denied that Kuhn [and Winch] are ‘semantic relativists’. Are we/they out of the woods? Not yet. There is a worse suspicion : that Kuhn, and Winch, are relativists about truth.

The relativism seems to follow from incommensurability. Here is what incommensurability means: insofar as there is incommensurability between different scientific paradigms, then so far is one unable to translate [in the strict sense] what can be said in the words of one into what can be said in the words of the other. If you can say ‘p’ in the language of scheme 1, you can’t say ‘p’ in scheme 2. In that case, of course, you can’t say ‘not-p’ in scheme 2 either. In other words, you can’t get schemes 1 and 2 lined up so that they flatly contradict each other, so that one says ‘p’ and the other says ‘not p.’ Hence, you can’t decide between them both by comparing them with the actual situation [whether or not p], since to describe the situation as p or not-p is to use the meanings of one scheme, when the legitimacy of using those meanings to describe the facts is just what is contested.

Does incommensurability not then automatically imply relativism about truth? If there is no scheme-independent way of telling whether ‘p’ is true, then that means that it is only in terms of scheme 1 that it is possible to say that ‘p’ is true then if it is true in p it cannot be said to be false. But doesn’t that mean that what any scheme says is true is true just by virtue of the scheme’s saying it is true? And wouldn’t that mean that what every scheme says is true is true because the scheme itself says it? And isn’t that just relativism: every scheme is as justified as every other.

But didn’t we, in our explaining of ‘incommensurability’, say, in the original mathematical example, that that we can’t compare in terms of a common measure at all doesn’t mean that we can’t compare (at all). Didn’t we also say that Kuhn does insist that scientific change involves comparison of paradigms, and what is a scientific revolution but a judgement that one paradigm is better than another.

Someone determined to extrapolate a relativist implication from incommensurability will not necessarily go away at this point. All very well, they may say, but the comparison is only between one paradigm and the other, but a comparison between one paradigm and another can have no purchase: there is no role for nature in this comparison. But isn’t the polarity of contrasting paradigms with each other, on the one hand, and contrasting paradigms with nature, on the other, just the polarity that Kuhn explicitly rejects: in real, historically existent science, comparison with nature is made by way of paradigms. And those comparisons, as carried out by science, are decisive [though they may not be simple, uncomplicated and patently conclusive]. What else are the Kuhnian case studies except an attempt to help the reader understand why that simplistic picture of two theories proposing p and its direct contradiction not-p each being compared against the independently established fact of whether or not p just does not occur.

So Kuhn is not a relativist? Well,

in his "Reflections on my critics", Kuhn does accept that there is a minimal sense in which he is willing hereabouts to be regarded as a ‘relativist’:

"[There are] contexts in which I am wary about applying the label ‘truth’... . Members of a given scientific community will generally agree which consequences of a shared theory sustain the test of experiment and are therefore true, which are false as theory is currently applied, and which are as yet untested. Dealing with the comparison of theories designed to cover the same range of natural phenomena, I am more cautious. If they are historical theories...I can join with Sir Karl [Popper] in saying that each was believed in its time to be true but was later abandoned as false. In addition, I can say that the later theory was the better of the two as a tool for the practice of normal science... Being able to go that far, I do not myself feel that I am a relativist. Nevertheless, there is another step, or kind of step, which many philosophers of science wish to take and which I refuse. They wish, that is, to compare theories as representations of nature, as statements about ‘what is really out there’. Granting that neither theory of a historical pair is true, they nonetheless seek a sense in which the latter is a better approximation to the truth. I believe nothing of that sort can be found."

‘Partial communication’ is about speaking at cross-purposes, speaking from bases which are not fully reconcilable with one another (and across which there is no point and no available means of making serious ‘verisimilist’ calculations). That is what – and ‘all’ -- that Kuhn is really saying, here.

Sometimes the accusation against Kuhn (and likewise Winch, and Wittgenstein) surfaces in an apparently different form – not ‘relativism’, but ‘idea-ism/idealism’. It is worth our treating it separately for a little while here – because considering the allegation of ‘(linguistic) idealism’ allows for perspicuous rebuttal of one of the main underlying worries that Kuhn’s ‘opponents’ have: They fear that he is subject to a sort of mad credulousness. That he is committed to saying that things exist in the world if we think they do.

We are dealing with allegations which ascribe to both Kuhn and Winch doctrines which they do not themselves embrace and which they would and should disavow, but denying that they fall for an error does not ensure that they don’t implicitly fall into it anyway. ‘Linguistic idealism’ is an extrapolation from their explicit arguments, but it is, unfortunately, a projection which involves placing a particular and inappropriate spin on their actual arguments. It is perhaps easy to see why the extrapolation seems plausible, even inevitable. The argument is that, according to their views (allegedly), the very concept of ‘correspondence with reality’ varies between cultures. Each is therefore as well justified as any other, each in its own terms is valid – and there are no common or neutral terms in which they can be compared. But doesn’t this mean precisely, the argument against Kuhn and Winch continues, that the culture decides what is real, that it dictates what is true and false? How can it be otherwise if it is only in the terms of one or another system that we can say what is the case, and it is only in the terms of that system that we can decide whether what we say is the case is the case? Therefore, if that system says it is the case, then, logically, whatever it says is the case. Thus, if the witchcraft system says that someone is bewitched then (for them) they really are. We may say that there are no witches, with [by the same logic] the consequence that, in our system, there are no witches. It does not follow from this that therefore there are no witches at all – e.g. maybe there are – really are – witches ‘for them’ (but not ‘for us’). Thus, it is the language of the culture, which dictates what can conclusively be said to be true or false which decides what reality is like: if the culture says that witches are real, then the culture is correct, and therefore witches exist. For a Realist, of course, this is to get things upside down. It is how things are with the world that decides whether what we say is true or false, so it is whether or not there really are witches [and there aren’t any] which dictates that when they say there are witches they are wrong.

Of course, in reality Kuhn is not arguing that the pre-Copernicans were correct about the immobility of the sun, nor is Winch arguing that there really are witches in Africa, though not in the UK, but this suggests why they are accused of linguistic idealism: they seem to be taking the view that reality is determined by our ideas expressed in language.

There is a major misunderstanding on the part of Kuhn’s and Winch’s critics.

One of them, Bernard Williams, attempts to lay out the ‘linguistic idealism’ position as a clear series of logical steps. Unfortunately, he commits a major logical slip in doing so, but, fortunately, because he attempts the logical presentation, this makes the error apparent, and makes the absurdity of the alleged position transparent

1. ‘S’ has the meaning we give it.
2. A necessary condition of our giving ‘S’ a meaning is Q.

Ergo

3. Unless Q, ‘S’ would not have a meaning
4. If ‘S’ did not have a meaning, ‘S’ would not be true.

Ergo

5. Unless Q, ‘S’ would not be true.

Consider (iv) : If ‘S’ did not have a meaning, ‘S’ would not be true.

Consider the way in which ‘true’ is introduced into the argument. It is not as if the conditions for the truth of S were amongst the conditions Q. The formulation ‘S’ would not be true’ makes it sound as if ‘S’ is true, and as though, therefore, its truth depends upon the initial clause of (iv): ‘if ‘S’ did not have a meaning…' This also gives the impression that (v) presents a challenge to the truth value of ‘S’. What is the alternative to ‘S’ being true? That it is false. Thus, the conclusion which (v) seems to convey is that it is the set of prior conditions, Q, which determine whether ‘S’ is or is not true.

Line (iv) is, in fact, an attempt to defy, rather than develop, the logic of the ‘incommensurabilist’ argument, which is quite plainly that the condition ‘Q’ are not conditions for the truth of ‘S’ but conditions only for its meaning. The implication of the claim that a necessary condition of ‘S’ having a meaning is a condition of ‘S’ saying something that ist capable of bivalence, treated as a hallmark of an empirical proposition, one that is capable of being either true or false. The condition, Q, is a condition for ‘S’ being an empirical assertion, not of ‘S’s being a correct empirical assertion. One could accommodate this point by reformulating (iv) as:

‘If ‘S’ was not an intelligible empirical statement, then ‘S’ would not be the sort of thing that could be found to be either true or false.’

But this is really, then, only a repetition of what is said in (ii) and (iii): it does not progress the argument, and, of course, it remains non-committal as to whether ‘S’ is true or false.

But Q was only introduced as a condition for ‘S’ to have a meaning. ‘S'’s having a meaning is a precondition of ‘S’ saying the kind of thing that could be true – that would be true if the evidence showed that what ‘S’ asserted was indeed the case. If ‘S’ is an empirical assertion, capable of being found either true or false, then of course the meaning of S does not establish its truth: empirical inquiry is required to determine whether it is indeed true. Whether Wes is more or less than six feet tall gets settled by measurement, not by the mere assertion of ‘Wes is under six feet tall’. Q is a precondition for ‘S’ meaning what it does, and, again, of course, whether S is or is not true does depends upon its meaning what it does, but only because that tells us what kinds of facts would be relevant to determining its truth. However this does not mean that in any usual sense of the expression, Q includes the condition for S being true. Q is not amongst the things that we can cite in support of ‘S’, but only a basis upon which we and other can know what we are saying when we declare ‘S’.

This understood, (iv) and (v) are seen as repetitions of each other, variant expressions of the claim:

,If ‘S’ did not have a meaning, we couldn’t even say ‘S’, i.e. couldn’t say that it was true or false’..

Once more on (iv), which now shows the depth of the confusion involved: for ‘S’ changes its identity in the course of this assertion. ‘If ‘S’ expresses the claim ‘Wes is under six feet tall’, then ‘S’ does have a meaning. It means that Wes is under six feet tall. That ‘S’ depends upon condition(s) Q to have this meaning does not detract from the fact that ‘S’ does mean: Wes is under six feet tall. Under other conditions than those that obtain, under conditions which comprise the absence of Q, then there is no ‘S’. Under condition(s) non-Q, either the words ‘Wes is under six feet tall’ are meaningless, or they mean something other than what they mean under condition(s) Q. In either case, a string of sounds or even a statement which does not mean that Wes is under six feet tall just is not ‘S’.

Much more concisely: the arguments of (I) to (iii) are for Q as an identity condition for ‘S’. (iv) and (v) either reiterate (I) – (iii), and are superfluous, or they distort the meaning of (I) – (iii).

Williams’ exposition then makes it sound as if among the conditions Q are those which not only make it possible meaningfully to assert ‘S’ but also those which decide whether ‘S’ is true . We can see from ‘Wes is under six feet tall’ that it is Wes’s height which is the state of affairs which determines whether this ‘S’ is true, for this is involved in our understanding of the sentence ‘Wes is under six feet tall.’ The conditions Q certainly dictate that the thing to do is to measure Wes’s height in feet to determine how tall he is, but we cannot determine from that fact about Q alone whether Wes is more or less than six feet tall! Nor can we even presume from the occurrence, abstracted from any context, of the sentence ‘Wes is under six feet tall’ anything about the world. The string ‘Wes is under six feet tall’ might be an hypothesis, something to be ascertained by inspecting the state of affairs referred to, calling for measurement. On the other hand, ‘Wes is under six feet tall’ might also be a description of the state of affairs – if it is a report back on the (proper, competent and accurate) measurement of Wes then it does describe the state of affairs, provides the evidence that confirms the hypothesis. The meaning of ‘Wes is under six feet tall’ depends upon the way it is advanced, whether it is an hypothesis as to what measurement will show, or a citation of what the results of measurement were, or a guess, or (etc.). The importance of this difference will be obscured if we keep thinking of things as being either ‘inside’ or ‘outside of’ language (or of sentences (let alone parts of sentences) meaning independently of their context(s) of use). Making measurements and reporting their results is not really adequately described as a linguistic event or an occurrence ‘within language.’

In short: the linguistic idealism which Williams presents is a straw position. It is not a position which could be put forward without basic and deep error. Kuhn and Winch make no such error – their view, as usual, is much more ‘modest’ than foes (and friends alike) suspect. They spent much of their careers after their early ‘successes’ trying to explain this to people. We hope that our readers at least are in a mood to listen, and read, and see – and not presume that Kuhn (or Winch) is committed to something ‘exciting’ and absurd.

Far from arguing that we have to accept that the convictions of the pre-Copernicans or those of believers in magic are true, Kuhn is in fact arguing that we cannot possibly make their way of thinking our own.

There is a sense in which we sometimes use the word ‘understand’ to mean something like ‘potentially be seriously able to say, myself’. Kuhn does not think the historian of science does or could aspire for what they are describing (i.e. old science) to come meaningfully out of their own mouths – Kuhn is not preaching the Ptolemaic system!

The kind of understanding that Kuhn and Winch seek to provide us with is one which allows us better to appreciate the very-other’s point of view, but which leaves us a very long way short of accepting their point of view, further perhaps than before we read Kuhn and Winch. This aspect of their philosophy, this respect in which they are the true ‘anti-relativists’, is utterly missed by most commentators, pro or anti. Kuhn and Winch aspire to present 'the Other'’s point of view to us in such a way that we can understand how that point of view could be compelling to them, how, in those same circumstances and under those conditions we ourselves would have thought [and been utterly and unquestionably comfortable in doing so] in exactly those same ways – and how, in the circumstances in which we actually are, those other/older ideas are complete non-starters. Putting aside all that we now know from post-Copernican astronomy, and imagining ourselves gazing into the skies, reading the astronomical tables, immersed in Aristotelian physics, and so on, can we not see how the idea that the earth was a fixed and central point, would have seemed wholly convincing, not least supported by the stark obviousness of what our own eyes could see. But, of course, this is an almost infinitely long way from suggesting that it could be convincing again, that we could seriously put aside our post-Copernican culture and unquestioningly embrace the Ptolemaic conception. The conditions ‘Q’ that enabled the Ptolemaic system to have the sense that it did have, for its constituent assertions to be put forward as serious, even confirmed hypotheses, have been comprehensively eroded. We can recite the lines from the Ptolemaic system, but we cannot, ourselves, deliver those lines as stating a series of serious hypotheses that anyone should attempt to test, let alone as a series of assertions. Here is a limit to the extent to which expressions from ‘alien’ schemes can enter into, can be translated into, our ‘own language’. They can only enter as things that we can say in, so to speak, quotation marks: we are only repeating, without endorsing, the things that they – the witchcraft believers, the pre-Copernican astronomers – say. There is no affirming these remarks as expressions of our own thought.

In sum: Everyday language-users or (especially) scientists, ‘live’ in one paradigm at a time (within any one given field): a contemporary physicist for example cannot seriously make assertions in ‘Newtonese’ – ‘Newtonese’ is, according to Kuhn, more dead than it is according to a 'point-of-view' relativist, or than it is according to a cumulativist about scientific-knowledge (e.g. a Logical Empiricist).

So for example an Einsteinian scientist who makes a good [by Kuhnian standards] study of Newtonian physics, who has understood them fully in Newtonian terms, will then be able to say with fluency only ‘What a Newtonian would say in this case or that’: our modern physicist would not be able to say these things on his or her own behalf, in the voice of ‘What I would actually say here is…’ This is what Kuhn calls ‘irreversibility’ in the development of science. The point of the whole exercise is, of course, to be accurate about what could and should come out of the Newtonian’s mouth, and the nature of the difference between that and what does come out of the Einsteinian’s. Kuhn is completely NOT saying, ‘From a certain point of view, the old paradigm is still true.’ He expressly holds, as we have made clear, that Newton can be rendered a special case of Einstein (and thus kept true) only at the cost of misunderstanding Newton’s theory. There is a real clash between paradigms for Kuhn, in a way which Relativist readings of him typically ignore or finesse, at the cost of their completely missing Kuhn’s point.

But the clash is not the clash of P and not-P, either. For us as Wittgensteinians, rather than followers of Quine or Davidson as such, it helps to point out the large extent to which what Kuhn is really talking about is ways in which changes in paradigms engage in and constitute the reconfiguration of what Wittgenstein sometimes termed 'grammar'. For us, language is not something that floats free, but something which is thoroughgoingly interwoven with activities. ‘Conceptual change’ is integral to change in ways of organising activities: What words can mean depends upon their connection to, and part in, our activities. When Wittgenstein says that to describe a language is to describe a way of life, he does not, as Sapir-Whorf would have it, mean that the ordinary meaningful use of some particular language is in the end incomprehensible to someone thinking or speaking in the ‘different ontology’ of another language. That way, clearly, lies self-refutation. What does Wittgenstein mean, then? Let’s bring it right down to basics: Take the word ‘king’. The word ‘king’, in the English language, is the name of a Chess piece and also the title of a monarch -- and it is clear that republicans can use and understand the word ‘king’ in the latter sense, in a perfectly ordinary everyday way, just as well as monarchists.

The disappearance of an activity does not deprive us completely of the use of the language it is interwoven with -- Latin teachers would have been living some big lies, otherwise; and though the inhabitants of a republic cannot themselves swear allegiance to a monarch, it is not impossible for them to understand what it is to do this. Is sum, Kuhn, like Wittgenstein, is on about activities – linguistic activities intertwined with non-linguistic activities in various ways.

By this point, we hope to have satisfied and convinced some readers. But we suspect that many readers will still be feeling certain nagging doubts about what it all means. (Perhaps especially if they know Kuhn’s precisifications of incommensurability in TRSS etc., which can seem complex and daunting.) Kuhn is still not necessarily that easy to read, even after our ‘help’. Are there are further useful analogies at hand, to communicate the general character of what Kuhn is up to in SSR and TRSS vis a vis ‘incommensurability’?

Well, for example, philosophers read each other’s books, but often they just don’t get what the other is saying. The characteristic form of inter-subjective philosophical puzzlement is perhaps not to know one’s way about in someone else’s discourse; for its components to seem perfectly familiar, but for the upshot to be uncanniness, or a wild oscillation between the feeling of incomprehension or of unbridgeable difference, the sudden dawning of mutual understanding, and then a rift opening up unexpectedly again. Philosophical disputes are quite commonly [as have been those around Kuhn] more over what the parties are respectively trying to say, than about how things are.

And here, in a way, we have of course come full circle right back to Kuhn’s earliest efforts to describe what a scientific revolution is. Namely, an upheaval in the course of which the .’discipline’ of normal science -- its characteristics of having a regularity and a cumulative nature not possessed by (e.g.) philosophy or sociology -- is partially suspended, and instead a situation is temporarily found in which philosophical-type disputes are possible. Moreover, such an upheaval specifically involves such-and-such becoming a candidate for truth-or-falsity when it didn’t even make sense before, or vice versa. So perhaps what we are saying should be unsurprising after all. When Kuhn is talking about incommensurability, a really apposite analogy then may be to the situation of two persons or schools locked in ongoing philosophical misunderstanding. And again, such philosophical puzzlement, where what one side says must seem either pointless or nonsensical to the other, is virtually never resolvable through semantic clarification, through a simple mutual demonstration of meanings. (The philosopher must practice a ‘hermeneutic’ effort to understand another philosopher – and roughly this is what is called for in the philosophy of science, too.)

As we have already noted, Kuhn himself tends to use analogies to literature.Particularly useful, we think, is thinking of poetry (both the ‘understanding’ of poetry in general and the further issues arising in the translation thereof), where words are not transparent – their whole point is often to fit in particular ways with the lines that surround them in the poem, or at least to facilitate specific kinds of associations and connections which are, as it were, provided for in the language. Take for instance the opening two lines of Robert Frost’s "On a bird singing in its sleep":

A bird half wakened in the lunar noon

Sang halfway through its little inborn tune.

Isolating one of these lines from the other would make a hopeless nonsense of their poetry. And even were they so isolated, then we can still say that the non-transparency of the language here is shown line-by-line, by for instance the importance of the rhyme of ‘lun-’ with ‘noon’, the aural-semantic ‘allusion’ from the word ‘noon’ to the concept ‘moon’, and the powerful metaphor of ‘lunar noon’ itself. None of this kind of specificity is present in the words, "Pass the salt" (in almost any imaginable ordinary language context for them). In short, words in literature are typically tied together in ways analogous to the inter-connections Kuhn sees as crucial within scientific lexicons. The incommensurability of lexicons, then, is like the untranslatability (and, indeed, similarly, the unparaphrasability) of literature.-

Finally, compare Wittgenstein’s comments on religion:

‘Suppose that someone believed in the Last Judgement, and I don’t, does this mean that I believe the opposite to him, just that there won’t be such a thing? I would say: ‘Not at all, or not always.’ ...

If some said, ‘Wittgenstein, do you believe in this?’ I’d say: ‘No.’ ‘Do you contradict the man?’ I’d say: ‘No.’ ...

Would you say: ‘I believe the opposite’, or ‘There is no reason to suppose such a thing’? I’d say neither.

Suppose someone were a believer and said: ‘I believe in a Last Judgement,’ and I said: ‘Well, I’m not so sure. Possibly.’ You would say that there is an enormous gulf between us. If he said ‘There is German aeroplane overhead,’ and I said ‘Possibly. I’m not so sure,’ you’d say we were fairly near.

It isn’t a question of my being anywhere near him, but on an entirely different plane, which you could express by saying: ‘You mean something altogether different, Wittgenstein.’

The difference might not show up at all in any explanation of the meaning. ...’

The interesting thing in each of these cases – philosophy, poetry, religion – is that understanding can be really difficult, and we might sometimes even find it impossible, even though the words involved are all ones in a language that we know. Thus, it is that Wittgenstein’s difficulties in understanding what religious people might mean by claims to believe in a Last Judgement applies to a claim in which each word is a perfectly ordinary one when used outside the religious context.

‘Translations’ are of course nevertheless made; but there is a sense in which we take them to be inevitably ‘partially successful’ (cf. ‘partial communication’) -- there is something, which need not be strictly semantic, which is generally missing in even the best such translations. This is what Kuhn had in mind, we believe, when he spoke of what Quine and Davidson ignore – what gets lost in translation.

That there are real difficulties in understanding across different cultures and in translation between them does not come as a surprise to us with respect to philosophy, poetry and religion … so why should there be any difficulty in accepting that the same is true in the case of [history of] science? Unless, of course, one thinks that it is somehow demeaning to science to link it with philosophy, poetry and religion – but is that anything other than a prejudice? Just as in the humanities cases, then, perhaps, if one is to understand and depict a vanished scientific tradition, one will need to find novel and surprising and un-inevitable ways of rendering it into terms that we can do something with. Understanding past science will be more like producing good paraphrases or translations of poetry than like producing good translations of car maintenance manuals. Here is Kuhn, on p.238 of The Road Since Structure: "…the ‘difficulties in communication’ arise between members of different scientific communities, whether what separates them is the passage of time or the different training required for the practice of different specialties. For both literature and science, … the difficulties in translation arise from the same cause: the frequent failure of different languages to preserve the structural relations among words, or in the case of science, among kind terms. The associations and overtones so basic to literary expression obviously depend upon these relations. But so…do the criteria for determining the reference of scientific terms, criteria vital to the precision of scientific generalizations." (italics added)

What is an ontology?

To sum up what we have been saying here about Kuhn's view: Words cannot be compared with reality. Nor can concepts. Nor even, in any direct respect, can sets of these – ‘conceptual schemes’, or, indeed, ontologies. Basic ontologies (‘furnitures of the universe’) cannot be compared with reality, with nature. We would better say that only scientific claims can (in a way) be (i.e. through being tested ‘intra-paradigmatically’, and occasionally through being compared and contrasted with other dying or incipient paradigms).

"Isn’t an ontology itself regardable as making a claim?" No – no-one says ontologies (except, sometimes, metaphysical philosophers). Ontologies are what one works with, one’s resource, not one’s topic. Ontologies are, if you like, what makes claims possible. An ontology is at best specifiable as something like a list (e.g. ‘matter’, ‘form’…) of properties that things (using that word now in the vaguest possible sense) can have or not have or have to various degrees, etc. .

Scientific claims are precisely makeable only ‘within’ one paradigm or another, on the basis of one ontology or another. Advocates of different paradigms thus misunderstand each other, in roughly the respect in which philosophers find themselves not infrequently systematically puzzled at things which other philosophers say.

But what exactly is an ontology, now? If we repudiate on Kuhn’s behalf the untenable claim that ontologies represent or ‘correspond’ to hermetically sealed systems of meaning, what do they ‘represent’? How are they to be understood?

Outrageous as it may sound, we think that Kuhn’s point of view, what he is trying to say, can be fully appreciated only if one gives up the notion that what it is for one to understand an ontology – a ‘lexicon’ (in Kuhn’s terms), a particular scientific ‘conceptual scheme’ (in the phrase commonplace in philosophy) -- is to do anything like grasp a metaphysical system, or comprehend a set of super-facts. Instead, one should think of understanding an ontology, roughly, as ‘getting’ a style. We are not saying simply that there is an analogy between ontology and style. No; we are saying that one should try to see an ontology as a style, as (a) form; and that that is the only way one can see ontologies in the present context, without falling into philosophical illusion. There is no such thing as magisterially surveying ontologies from an external -- semantic -- point of view. There is no such thing as an external point of view to language, or indeed to our best science, which alone could provide one with a ‘position’ from which to entertain the alleged claims of ‘Metaphysical Realism’ or ‘Relativism’. Only if there were could it make any sense straightforwardly to give the true account of the history of scientific progress toward ‘cutting nature at its joints’ (‘realism’) or to describe incommensurable systems of meaning (‘relativism’). The latter is self-refuting; the former misses (or accounts purely reductively and inadequately for) the very difficulty which prompted Kuhn’s philosophy of science in the first place, the ‘strangeness’ of much past science, if one actually looks at it properly, rather than merely propagandistically.

The difference between chemistry before and after the Chemical Revolution, then, is not that the meanings of the sentences of phlogistic chemists are literally inaccessible to us. It’s not that their ontology is literally ‘cognitively closed’ to us. It’s rather that they operated with a significantly different taxonomy -- a taxonomy which is worth calling ‘significantly different’ because it is directly translatable into our’s only at the cost of a fatal (to historical understanding) loss of style, of form, of sensibility. Kuhn wants us (historians and philosophers of science) to put us more closely in tune with the connotations of the words of the old paradigm. If we ‘translate’ ignoring these, we’re not really translating at all (in the ‘full’ sense of the word…). We’re just producing a version of them in our own terms – that is the upshot of following Davidson. Being able to translate, so as to understand merely from our own unalloyed and un-nuanced and unaffected point of view what the sentences of the old scientists meant, is not enough.

What is needed is to be able to get much closer to understanding what is lost in such a ‘translation’, much as in situation of the translation of natural language, or particularly of poetry. What is lost is not best described, we think, as a semantic item, a meaning. It is rather the awareness -- the ‘presence’ -- of the systematic network of associations and connections of words with one another and with certain practices in Newtonian physics, and the ‘grammatical effects’ of that system. It is something like a feel, an atmosphere, a style (of reasoning, of writing). To think ‘mass’ or whatever a la Newton is to be able imaginatively to ‘re-create’ that atmosphere, and to re-grasp those (linguistic) effects.

Some may still find the above uncomfortably vague. An ontology -- that seems a substantial, manly thing. A thought-style, an atmosphere, a form of language -- that may seem in comparison flaccid and hand-wavy. But we hope to have provided already the materiel with which to undercut these impressions. One is under a deep illusion if one thinks that fundamental ontologies can be spoken, can be simply declaratively given, at all. They can ‘only’ be understood as, roughly, ways of speaking. Though they are not like Rortian ‘vocabularies’ – for Kuhnian ‘taxonomies’ are far more structured than that (and so, of course, our analogy to literature is only...an analogy).

These definite and ‘structured’ ways of speaking, these taxonomies, must be understood in a wholistic fashion. Kuhn’s wholistic incommensurability, especially in the later formulations, applies to sets of interdefined terms. If you change the locus of one term in relation to other terms, you change (the use of) that first term also (when they are interdefined) – it’s no longer the same term in a different theory. Hence, the translation can’t be effected on the one hand, and, on the other, insofar as the terms are different and conflicting, then of course we can’t affirm equally statements featuring each of them.

This point is terribly important; let us elaborate and exemplify it a little. Words/terms in a scientific context have an extremely specific web of connections with the other words/terms around them. Take a symbolic generalisation -- that functions as a tool, as a basis for a number of crucial exemplars (exemplary problem-solutions) -- like Newton’s ‘F=M.A’. Kuhn (and, somewhat similarly, Feyerabend too) argued that this is only the equation that it is if it stands in very specific relations to various other equations, and also to various laboratory proceedures, and so on. One might say, that it is only the equation that it is in a certain great physics text (Newton’s Principia), and in other texts which have stood in a particular historical relation to that text. It is in a way absolutely tied to its scientific context. By contrast, an ordinary language expression, like "Pass the salt", is much less context-specific. It can be used in numerous settings, and can survive many other changes in the language around it without having to suffer any significant modification in its use.

Now, in a way, lines of poetry are less context-specific still. They are endlessly re-contextualisable. Thus they might seem the absolute opposite of scientific terms.

But the analogy we have been pursuing (with literature, following Kuhn) still has force. For the web of connections a line of poetry has with the language around it actually has a very great deal of specificity, even if it is far less formalized than in the case of scientific terms. Unlike ordinary terms, words in poetry are not transparent – their whole point is often to fit in in particular ways with the lines that surround them in the poem, or at least to facilitate specific kinds of associations and connections which are, as it were, provided for in the language.

Unlike in the case of most ordinary language, literature shows clearly its ‘wholistic’ nature – a wholism shared, according to Kuhn, with scientific language and practice.

Conclusions

Let us close this chapter with one further linking remark to Wittgenstein.

We have endeavoured to rebut the almost invariably wrong/over-played attributions to Kuhn of ‘relativism’; and to present the sense in which Kuhn can intelligibly hold onto something which one could if one wished choose to call, say, ‘(minimal conceptual) relativism’. The latter is in the conceivability (and actuality) of a sense of ‘concepts’ in which it is intelligible to speak of different concepts. The most crucial passage of all on this in Wittgenstein himself runs as follows:

‘I am not saying: if such-and-such facts of nature were different people would have different concepts (in the sense of a hypothesis). But: if anyone believes that certain concepts are absolutely the correct ones, and that having different ones would mean not realizing something that we realize -- then let him imagine certain very general facts of nature to be different from what we are used to, and the formation of concepts different from the usual ones will become intelligible to him.

Compare a concept with a style of painting. For is even our style of painting arbitrary? Can we choose one at pleasure? (The Egyptian, for instance.)’ (PI, Part II, p.230; italics our’s)

Our concepts are not, Wittgenstein reminds us, ‘fixed’ by nature. ‘Our’ style of painting -- or of writing, for example of writing poetry, with the distinctive kinds of effects and ‘aspects’ that that yields -- is not as a result arbitrary -- and no more, of course, is our style of science, our scientific sensibility. One might talk here of the needs of our lives and the shapes of our concepts – one might talk, that is, of ‘form of life’. Kuhn is with Wittgenstein in seeing nature not as a standard of and for comparison, except as ‘within’ a paradigm. Only in ‘intra-paradigmatic’ thinking does nature play a precise and demarcatable role. Kuhn is concerned that we will do bad history and philosophy of science if we – absurdly -- take our concepts to be ‘absolutely the correct ones’.

In a nutshell, Kuhn is interested in real cases where the formation of concepts different from our’s has happened, has been the case.

Kuhn points to the same process as Wittgenstein, only in very concrete circumstances: in scientific revolutions. Kuhn sees scientific revolutionaries as "[imagining] certain very general facts of nature to be different from what we are used to", and thus as finding themselves needing "[to form] concepts different from the usual ones."

In conclusion, then: Perhaps the most important thing we hope to have achieved in this chapter is not just to have explained what incommensurability is, but to have got over to the reader the full ‘triviality’, moderateness, reasonableness and ‘descriptiveness’ of the concept. So long as one finds, as we find, the clear preponderance of Kuhn’s writings leaning in the direction we have indicated here, then one finds no reason to judge Kuhn guilty of extremism or self-refutation here. On the contrary, what Kuhn means by ‘incommensurability’ ought to be recognised precisely as a to-be-expected aspect of what is still we think very much worth calling ‘the growth of scientific knowledge’. The philosophers who have argued otherwise have, in the main, failed to understand the nature of Kuhn’s contribution.

Though we return to some of their concerns once more, when we take up the issue of some of the forms of words which most confused Kuhn’s philosophical and scientific critics in the first place: ‘World Changes’.

There is no getting away from incommensurability, and in this chaptersection we deal in proper detail with one of its most famous consequences, the idea of ‘world changes.’ Through that topic we deal with perhaps Kuhn’s main explicit philosophical affiliations: first, his persistent Kantianism, and then his more recently accented Darwinism.

On our first encounter with the idea of ‘world changes’ we argued that Kuhn’s formulation of it, understood in relation to his historical accounts, and understood as using the expression ‘different worlds’ in a routinely idiomatic fashion, could be construed as a harmless restatement of the case that Kuhn had already made. At the same time, however, we registered that this was not all that Kuhn wanted to do with the idea. He desired, further, to express a strictly philosophical rendition of the situation of the scientist undergoing major conceptual change – an understandable desire, but an unavoidably problematical one. He evinced some unease about the formulation(s) he was using, advanced the point throughout in a tentative way -- and gave the impression of thinking that there was rather more to the idea than he had yet managed to either identify or express. This is a moment in Kuhn’s thought that has definitely, we think, been troubled by the confusion of idiomatic and philosophical uses of the same word, namely ‘world.’ As used in expressions such as ‘the world of high fashion’ or My world and welcome to it! (by James Thurber) there is little danger of one feeling that a difficulty is in the offing: one understands clearly enough what these sayings mean. In philosophy, however, the world ‘world’ plays a very different role, and operates as (pretty much) a synonym for ‘reality’, even ‘reality as a whole.’ Therefore, some of the temptation that Kuhn may feel to adopt and persist in a locution [world changes] that he admits he finds strange may precisely be because he feels that he is, in saying them, making remarks of strong philosophical significance.

Saying that scientists divided by their paradigms live in different worlds, and that paradigm-shifts involve changes from one world to another can easily give the impression [especially if associated with all kinds of intellectual trends following from the ‘linguistic turn’ in modern thought: he alleges that ‘research in parts of philosophy, psychology, linguistics, even art history, all converge to suggest that the traditional paradigm is somehow askew’, that something philosophically bold is being asserted, that ‘reality itself’ is different before and after a scientific revolution, that ‘reality itself’ has been changed by the revolution. And Kuhn has reason, in his own terms, to think that he must be seriously putting forward a philosophically consequential position when he advances such statements. We will argue that the inclination to think that philosophical issues are at stake is encouraged by [at least] Kuhn’s commitment to his initial historical objective of doing justice to past scientists and by his strong inclinations toward a ‘two moments’ doctrine of perception/observation, or in other words, to resort to a Kantian notion of ‘phenomenal worlds’.

We will argue, however, that Kuhn’s real difficulties originate in confusions about the relations between tenses, between different kinds of descriptions, and with difficulties in articulating different - especially historical and scientific - discourses.

Kuhn was not by any means alone in thinking that something philosophically fateful was going on. His commentators and critics have been only too ready to follow him in this conclusion and ‘world changes’ has been conceived as a major issue in – if not the central and most damaging implausibility of – Kuhn’s thought.

However, Kuhn’s uncertainty about his own meaning was genuine, and he was much less quick than the commentators and critics to decide what he must mean. Kuhn remained painfully dissatisfied with his own grasp on the idea of ‘world changes’ and made repeated attempts to reconstruct it. We will, below, examine a couple of the ways – both early and later – in which Kuhn grappled – and in radically different fashion – with this matter.

To get to grips with the question of why ‘world changes’ should be a problem that Kuhn felt he needed to take up at all, let alone to struggle with, we need to mention, first, Kuhn’s Realism.

Kuhn’s most savage critics must surely include those who deem themselves advocates of ‘Realism’, and their attacks often emphasise that Kuhn’s major fault is that he affronts their Realism – as Kuhn accepts he does, though not, perhaps, in the way, or for the reasons, that they imagine. , It is said that his arguments express Idealism, not Realism, and are generally irrealist in character. Kuhn feels entitled, nonetheless, to insist that he, too, is a realist, but not of the kind that regular Realists will find themselves comfortable with.

‘Realists’ are not all philosophers of a single stripe, and ‘Realism’ can include a variety of different ideas, the different kinds being perhaps best identified on the basis of the positions they see themselves as opposing – Phenomenalism, Instrumentalism etc. One kind of Realism is adduced in response, precisely, to Idealism. The issue between those two is whether there is an external reality, one which exists independently of the human mind, with a character which is intrinsic to reality itself and distinct from [and only possibly coincident with] the categories of human thought. Realists insist that there is such a reality, accusing Idealists of holding that reality exists only in thought. Going so far, that is, as to maintain that reality is composed of those very categories: there is no difference between our minds and the reality they ostensibly attempt to apprehend. Kuhn’s few words [in SSR] about turning from the way paradigms ‘constitute science; to the way they ‘constitute reality’ might seem to license criticism of him for falling for the latter view, but, taken in relation to almost everything else he says, this cannot be right (See ‘Incommensurability 1, above). It is actually in the sense that a Realist is insistent upon a mind-independent reality, that Kuhn is a Realist.

Here is latter-day Kuhn, once again attempting to distance himself from those apt to think of themselves as his inheritors, those who say that ‘reality is a social construction.’

‘[T]he world is not invented nor constructed. The creatures to whom this responsibility is imputed, in fact, find the world already in place, its rudiments at their birth and its increasingly full actuality during their educational socialization , a socialization in which examples of the way the world is play an essential part. That world, furthermore, has been experimentally given, in part to the new inhabitants directly, and in part indirectly, by inheritance, embodying the experience of their forebears. As such, it is entirely solid: not in the least respectful of an observer’s wishes and desires; quite capable of providing decisive evidence against invented hypotheses which fail to match its behaviour, Creatures born into it must take it as they find it. They can, of course, interact with it, altering both it and themselves in the process, and the populated world thus altered is the one that will be found in place by the generation that follows…what people can effect or invent is not the world but changes in some aspects of it, the balance remaining as before.’ (TRSS, 101-2)

This is not, however, a matter of Kuhn belatedly coming to accept a point of view that his work had, up to this time, either pointedly or unwittingly undermined, but shows, rather, Kuhn insisting upon a point that his work has, throughout, presupposed. Indeed, Kuhn’s Realism is a crucial element in his particular brand of his ‘Kantianism’, a brand that tries (like Hegel and various other post-Kantians) to dispense with the noumena. .

We have earlier tried to dispel the false impression that ‘nature’ has no part to play in Kuhn’s philosophical interpretation of his historical account of change in science, insisting that the formation and change of paradigms might almost be seen as a collaboration between scientists and nature. Nature exists quite independently of our thought, and seems, on Kuhn’s view, to be necessarily elusive of any definitive set of comprehensive categories (which is plainly not the same as: entirely elusive of all our categories). On the contrary, nature is indeed captured in scientific schemes, but only partially so in each case, and by many different kinds of categories. And nature can, of course, only be captured through one or another set of categories.

As is clear in the quote just given, and in our discussion of the SSR formulation of world changes, Kuhn does not come remotely close to advising us that natural reality is constituted by and transformed with our scientific categories. What, then, does he hope to gain by adopting, and taking seriously this locution.

We mentioned Kuhn’s commitment to the initial historical objective of doing justice to past scientists, and this is a fundamental feature of his thought, albeit one to which, at moments, he can perhaps be too strongly attached . As such a fundamental feature, it can provide him with what he can see as one of the good reasons for persisting in this line of thought. In fact, doing so gives shape to the problem that Kuhn faces with respect to ‘world changes.’

As is manifest in the following quote from SSR

‘During the seventeenth century when their research was guided by one or another effluvium theory, electricians repeatedly saw chaff particles rebound from or fall off the electrified bodies that had attracted them. At least that is what seventeenth century observers said they saw, and we have no more reason to doubt their reports of perception than our own. Placed before the same apparatus, a modern observer would see electrostatic repulsion (rather than mechanical or gravitational rebounding), but historically, with one universally ignored exception, electrostatic repulsion was not seen as such until Hauksbee’s large scale apparatus had greatly magnified its effects.’ (117)

Kuhn’s root idea is that there is normally no good reason to postulate a difference at a basic level in the human qualities of different generations of scientists. Construe those qualities on the [minimal/’empiricist’] assumption that what scientists report about themselves and others is usually what they experienced. Then conclude: if scientists then as now are equally honest, careful, scrupulous and the rest, in their reports, and if they are reporting their experience, then their reports indicate/report what indeed they did experience. In that sense, no scientific observer’s report [failing the unusual, viz. dishonesty, carelessness etc.] is invalid.

But then, given the assumption that there is only one and the same natural world to be observed, one is left with this puzzle: how can the observers of one and the same world each observe different things in it? This puzzle is most memorably stated in Kuhn’s small thought experiment of putting an Aristotelian and a Galilean together to observe the motion of a string on a stone:

‘Since remote antiquity most people have seen on or another heavy body swinging back and forth on a string or chain until it finally comes to rest. To the Aristotelians, who believed that a heavy body is moved by its own nature from a higher position to a state of natural rest at a lower one, the swinging body was simply falling with difficulty. Constrained by the chain, it could achieve rest at its low point only after a tortuous motion and a considerable time. Galileo, on the other hand, looking at the swinging body, saw a pendulum, a body that almost succeeded in repeating the same motion over and over again ad infinitum. And having seen that much, Galileo observed other properties of the pendulum as well and constructed many of the most significant and original parts of his new dynamics around them …..Do we,,, need to. describe what separates Galileo from Aristotle….as a transformation of vision? Did these men really see different things when looking at the same sort of objects? Is there any legitimate sense in which we can say that they pursued their research in different worlds’ (118-120).

He does not go on to answer these in the unqualified affirmative!!!

The immediate temptation is to ask: what do they respectively observe, what is the content of their visual field? It is here that the second fairly fundamental and persistent assumption of Kuhn’s comes into play, that of the ‘two moments of observation/perception’ , or, as it is alternatively formulated, a doctrine of reality as both ‘object sided’ and ‘subject sided.’

Kuhn, in SSR and for a time afterward, thought about these matters very much in terms of visual metaphors – the idea of the gestalt switch is clearly of that kind, and his thoughts around these issues were cast in terms of the content of the observer’s visual field: what appears in it? He later came to regret both the gestalt analogy and the visual thrust, regarding this as seriously misguided. The correct way to think about these problems [as we will see] is, for Kuhn on scientific change, in linguistic terms. However, in our view, the ‘linguistic turn’ provides a means of attempting to get himself out of a problem that had arisen in part because of Kuhn’s residual attachment to an empiricist legacy, the idea that the issue turns on the contents of the visual field.

The doctrine of ‘two moments’, as we call it, draws upon what is obvious, and obviously true. The difference between the observation reports of scientists from different traditions may be put down to the differences in the traditions from which they come. In Kuhn’s terms, what scientists will report themselves as having observed, will depend upon ‘prior experience’, but this merely means [at least in a gross way], that it depends upon prior training, upon the scientific scheme they have been trained into. Thus, Kuhn’s ‘thought experiment’ can be set out: we know what the Aristotelian and Galilean respectively will report themselves as seeing – constrained fall and pendulum motion – because we know what the difference between Aristotelian and Galilean physics is. It is, we are saying, true but utterly unsurprising that the Aristotelian will report the first kind of motion, and the Galilean the second.

The difference between them, then, really derives from their respective science.

We are suggesting, then, that it is not a good idea to think of the disagreement between the two [kinds of scientist] in the way that Kuhn sometimes does, as a perceptual difference, and as one which must, therefore, reside within the visual field; but this is how Kuhn has tried to envisage the commonplace about scientific difference we have just reiterated. Setting it up this way, Kuhn is drawn into thinking that the visual field itself is a composite, that what is in the visual field is in part put there by ‘prior experience.’ However, there must also be something in the visual field which is not a product of prior experience, for prior experience must be applied to something to generate an observation. And it is, of course, to an input from nature itself, that prior experience must be applied.

Nature is present in the observations of science. Hence, vindication of our point that Realism has always been a fundamental, and from his point of view, indispensable element of Kuhn’s thought. Scientists do observe the [one and only] natural world, but they do so through the mental preparation that prior experience provides, or in the terms that their conceptual scheme supplies. Equally, this makes plain why Kuhn wants to be both a Realist and a Kantian. Our knowledge of the world [not just our scientific knowledge ] must always involve two elements: a contribution from the world, and a contribution from our minds, with the latter (so to speak) endowing structure upon the former.

Together with the insistence upon the integrity of scientific observers, then, Kuhn is propelled toward the view that there are two worlds. There is the real world out there, the world of nature, towards which scientists direct their observations. But there is also the ‘phenomenal world’ within which a scientist dwells, a world that is the object of his or her routine observation. (Though using ‘two worlds’ here, we might better – but less conveniently – say that Kuhn’s is a doctrine of one-and-a-half worlds since the real and phenomenal worlds are not completely distinct. The phenomenal world is partially made up of input from prior experience, it is also made up of a contribution from nature itself). The doctrine of two worlds promptly generates, of course, a doctrine of many worlds, for scientists differ in their prior experience, and therefore, the phenomenal reality varies, depending [grossly] upon the paradigm to which the observer owes allegiance.

These assumptions set the form in which Kuhn actually confronts the ‘world changes’ problem. World changes are clearly to be understood as changes in phenomenal worlds, the displacement of one phenomenal world by another. When paradigms change, phenomenal worlds then change with them. Scientists divided by a scientific revolution occupy different phenomenal worlds. Here is the remaining problem: how can it be that one and the same natural world can accommodate different phenomenal worlds? It is his inability to fully satisfying himself on this question that motivates Kuhn’s returns to and repeated rethinking of it.

Kuhn, like Sellars and many others in recent times, wanted to get entirely away from the empiricist notion of ‘the given’. One of the ways that Davidson’s attack on Kuhn can be seen to be dangerously uncharitable is in failing even to acknowledge this ‘moment’ in Kuhn’s thought. That said, it is undeniable that, though to get beyond ‘the given’ is what Kuhn intended to do, it is not really what he succeeded in doing. Indeed, it looks like his felt need to continue to speak of the ‘contributions’ to one’s experience and to one’s words of nature and of the mind makes it impossible for him to get beyond ‘the given’.

Slightly more concretely: Kuhn’s ‘two moments’ position is an uncomfortable one since, taken seriously, it is unstable on the question of whether or not the natural world does or does not manifest itself within our visual field?

At one level Kuhn’s Realism involves him wanting to say something like this: there are lights in the sky which are the objects of astronomical observation, and these are manifestations of natural phenomena ‘out there’ regardless of what kind of astronomical doctrine we hold. Sometimes, Kuhn speaks as if ostension can straightforwardly give us this, even across paradigms. But, what we see when we look at those lights [for we do see those regardless of our scientific allegiances] will depend upon our prior experience i.e. upon which astronomical doctrine we accept. This looks as though nature itself does appear – in the form of the lights which, assuredly, originate off the earth, however they do originate – in our visual field … but to say that the stars and planets do not appear to the naked eye, and their identity depends upon what we understand the lights to be i.e. which astronomical conception we contrive or adopt.

However, if we hold that whatever appears in the perceptual field can only appear in interpreted form, then, of course, whatever is ‘out there’ cannot actually manifest itself, cannot appear as such in the perceptual field at all but only in one or another interpreted form … and so Kuhn has this problem: how deeply down does the interpretation go? And how is one to answer this latter question? Since what can appear in the field is an inextricable fusion of nature and interpretation it is not possible to single out anything in the field which is the contribution of nature itself, however tempting it might be to appeal, as above, to the ‘lights in the sky’ example.

Kuhn appreciated, if not these specific difficulties, that there were difficulties, and his first attempt [in 1969] was to resort to a distinction between data and stimulus.

The natural world appears in our perceptual field as ‘interpreted’, as what are, thus, the data of science: hence, the lights in the sky are data, external but interpreted, data which are produced in us by nature itself, are the results of the upshot of natural effects: the causal input of nature is the ‘stimulus.’ The process of interpretation cannot, however, take place within the visual field, since what is present in the visual field can only appear there in interpreted form. Therefore, in a desperate manoeuvre, Kuhn seeks to argue that the interpretation takes place outside the visual field, and prior to the moment of visual perception. The ‘process of interpretation’ is then conceived as a causal process. It is in the interaction between the causal inputs of the external world and the causally governed responses of our nervous systems that the perceptual world is constituted. Kuhn must then be bold. The obvious objection is that if we are confronted with an entirely natural and causal transaction between an external world and the nervous system, then presumably same cause, same effect. This would undermine the ‘plurality of worlds’ thesis which Kuhn is, as we have explained, strongly tempted towards.

If the perceptual field arises from the natural interaction of the input from the world and of the nervous system, then the only way in which the two-moment thesis can be sustained is to have prior experience affect the nervous system itself: the nervous system is to be thought of as programmed by experience, and therefore can be reprogrammed by further experience; which really means, in practice, only can be either educated differently [as, in a scientific revolution, those following the new paradigm are trained differently from those brought up on the old one] or re-educated [as would happen if a scientist ‘crossed the floor’ during a scientific revolution, and came to think instead with the new paradigm]. Kuhn never did report the studies he was making on computer simulation of these processes.

Kuhn has (merely)_ moved the line between given and interpretation rather than abandoned that distinction altogether. i.e. has re-located the interaction between ‘the given’ and ‘the interpreted’ by moving it outside the visual field and into the interaction between the nervous system and the causal input of nature.

Kuhn did not persist long in the previous way of thinking about the problem. Already, in its terms, he had begun to prepare the way for what he conceived as a superior solution, namely, the adoption of a taxonomic solution.

In developing the idea of the re-education of the nervous system , Kuhn had sought to illustrate by an example of education – taking the case of a small child being given parental instruction on how to discriminate between different kinds of waterfowl on the basis of their observable characteristics. Kuhn’s assumption that the way in which [scientific] language relates to reality is through the classification of the similarities and differences that constitute phenomena in their ‘uninterpreted’ state now comes into play. Scientific language, for him, consists in classificatory schemes. Therefore, it is entirely natural to envisage parental education as involving instruction in the acquisition, through observation, of a classificatory scheme. Kuhn’s later development of the ‘linguistic turn’ is a matter, then, of dispensing with the arguments about data, stimulus and nervous system programming which have led to this kind of example and focussing directly on classificatory schemata.

Kuhn is, in elaborating this example, also showing another influence upon his thought, that of Benjamin Whorf and Edward Sapir, whose notorious Whorf-Sapir hypothesis held that the structure of language [in their minds, its grammatical structure] determines the nature of perception of reality. Whorf-Sapir deny that there is any necessary correspondence between the structure of any language and the actual structure of the reality that is perceived, and Kuhn pursues this thought with respect to classification. Waterfowl possess an array of characteristics, and there is no reason to suppose that the selection of criteria by which one may differentiate one fowl from another is the only selection that may be made: the makers of classificatory schemes may make different selections from amongst the array of similarities and differences which an assortment of objects may exhibit [thus it is the characteristics which are – logically at least – prior to the objects: the characteristics which are selected to make up the classificatory discriminata serve to identify the objects]. Thus, it is not only possible, but inevitable, that different classificatory schemes are possible for one and the same reality, and that different categorial schemes will therefore yield different objects to observe.

But do the different categorial schemata merely glomm onto fully pre-existing objects or clusters?

The key Kuhn paper addressing the issue just outlined is "Dubbing and Redubbing: The vulnerability of Rigid Designation". Kuhn’s intent and fighting spirit is clearly evident in the title here. He signals that, unlike the essentialists, he will concentrate not only on the ‘dubbing’ (naming, baptising) of kinds in the world, but on their redubbing, their re-classification – on revolutions, and their widespread nature and effects, in short. He further signals that he thinks that ‘rigid designation’ – the metaphysical idea at the heart of K/P essentialism – is vulnerable to Kuhnian objections, vulnerable to falling afoul of what Kuhn has said about serious conceptual change in science

The underlying neo-incommensurabilist ‘position’ which Kuhn wishes to defend and build upon is stated clearly at the outset of his paper. It is to be noted, once again, that it wisely, modestly and crucially focuses upon the role not of the metaphysician but of the historian:

"To understand some body of past scientific belief, the historian must acquire a lexicon that here and there differs systematically from the one current in his or her own day. Only by using that older lexicon can historians accurately render certain of the statements that are basic to the science under scrutiny. Those statements are not accessible by means of a translation that uses the current lexicon, not even if it is expanded by the addition of selected terms from its predecessor." (298)

Here is a pretty careful ‘linguistic’ (re-)formulation of what we have suggested is an absolutely central message of Kuhn’s, throughout his career. Kuhn is suggesting that incommensurability be understood primarily as the (‘partial’) "untranslatability" of taxonomies of natural kinds across revolutions. The (double) scare-quotes are necessary because, "Incommensurability…equals untranslatability, but what incommensurability bars is not quite the activity of professional translators. Rather, it is a quasi-mechanical activity governed in full by a [Quinean translation] manual" (299).

The crucial sentences, for the purposes of trying to see what Kuhn is up to in discussing incommensurability under the heading of ‘world changes’, are perhaps the following:

To possess a lexicon, a structured vocabulary, is to have access to the varied set of worlds which that lexicon can be used to describe. Different lexicons – those of different cultures or different historical periods, for example – give access to different sets of possible worlds, largely but never entirely overlapping. (300)

It is what Kuhn means to mean by such grandiose sentences as these that we shall now try to uncover.

As already suggested, the philosophical worries of Kuhn’s mainstream philosophical critics, facing Kuhn’s effort to establish the import of these changes of lexicon – radical alterations in taxonomy, in mode of classification or ‘ontology’ – might be expressed as follows: There is only one world, and the Realist (unlike the Relativist or Idealist) can have coherent things to say about our deepening knowledge of that (one) world, because we (all of us, especially via scientists) are always in touch with the world. We are in touch with it through our naming of bits of it, and our growing knowledge about the nature of what we name. It may that at different times people had radically wrong ideas about the nature of the world – they may have thought, for example, that water was a primitive element – but, through being in contact with bits of the world (e.g. with water), and through naming it, they always had some kind of ‘basis’ to their claims. We can connect with them and what they said, because there are direct (albeit long) chains of connection – linguistic and (more generally) ‘causal’ – between their use of these words and our use of them. They may have ‘meant’ something very different by their words, but the reference of their words was just the same as our reference for the same words. Reference – and in particular a causal theory thereof – will settle the problem which meaning poses. Kuhn is wrong, because he thinks that incommensurability of meaning is important and deep. It is, in fact, completely shallow and unimportant, once one understands that the real reference for natural kind terms remains continuous over time and through ‘revolutions’.

Kuhn made original and interesting replies to this kind of essentialism, making a strong case that the causal theory of reference will not solve the problems/challenges which ‘incommensurabilism’ poses.

The Kripke-Putnam essentialist story is usually run in two main versions. It speaks of the dependence of meaningful and consistent language-use on continuity of reference across SPACE, and also across TIME.

This is the famous ‘Twin-Earth’ case – Putnam alleged that the meaning of ‘water’ would be different in a place (‘Twin-Earth’) if and where what superficially appeared to be water was actually a different chemical (‘XYZ’ for short, i.e. a substance with a different ‘essence’). The heart of Kuhn’s response is this: "The terms ‘XYZ’ and ‘H20’ are drawn from modern chemical theory, and that theory is incompatible with the existence of a substance with properties very nearly the same as water but described by an elaborate chemical formula. Such a substance would, among other things, be too heavy to evaporate at normal terrestrial temperatures. Its discovery would … demonstrate the presence of fundamental errors [anomalies] in the chemical theory that gives meanings to compound names like ‘H2O and the unabbreviated form of ‘XYZ’. Only within a differently structured lexicon [to that of modern, post-phlogistic, chemistry], one shaped to describe a very different sort of world, could one, without contradiction, describe the behaviour of ‘XYZ’ at all, and in that lexicon ‘H2O’ might no longer refer to water." (310, our italics)

Is Kuhn merely fiddling here? Is he being a spoilsport, bringing in mere facts to bear on a philosopher’s charming speculations? No! He is raising a fundamental difficulty for the essentialist/referentialist view. He is saying: ‘If we try taking Putnam’s example seriously it turns out that Putnam doesn’t really offer up a tenable thought-experiment after all. Unless you are willing to fundamentally revise chemical theory, i.e.

to alter it in a radical way, to turn the paradigm – in the full sense of the words, the taxonomy of chemical theory – upside down’.

Bird counters that Kuhn is muddying the waters, that his (Kuhn’s) objection can be finessed by means of switching to a time, perhaps the mid-nineteenth century, when we could know that XYZ is not water (and that water is H20), without knowing that XYZ cannot have the surface properties of water (unless modern chemistry is more or less completely wrong). But this just seems incoherent: it seems that now there no longer is a thought-experiment. For how are we supposed to know that water is H2O if we cannot rule out that some water is XYZ, if we cannot rule out XYZ as a starter in the game? And we cannot rule out the latter unless (e.g.) we know that XYZ cannot have the surface properties of water ( unless, modern chemistry is more or less completely wrong, is in need of a fundamental taxonomic overhaul ). Unless and until one has a good scientific reason for insisting that water’s extension cannot include XYZ, one will not need to endorse Putnam’s ‘externalist’ conclusion. Kuhn’s point is: such good reason is ‘only’ in fact given by the taxonomic etc. structure of modern chemistry. The apparent discovery of XYZ would prompt not a reflection on the alleged truth of referentialist/externalist essentialism, but would rather herald a scientific revolution in chemistry.

In short, Putnam’s essentialism begs the question against Kuhn by ignoring the knock-on consequences of change in taxonomy, of change in the world-as-understood-by-science.

Putnam suggests that ‘water’ referred to the same substance (H20) in 1750 as today, and that that’s an end of the matter. Kuhn, by contrast, is interested in the structure of (any given) Chemistry, and writes as follows:

"’H2O’ picks out samples not only of water but also of ice and steam. H2O can exist in all three sates of aggregation – solid, liquid and gaseous – and it is therefore not the same as water, at least not as picked out by the term ‘water’ in 1750. The difference in items referred to is, furthermore, by no means marginal, like that due to impurities for example. Whole categories of substance are involved, and their involvement is by no means accidental. In 1750 the primary differences between the species recognised by chemists were still more or less those between what are now called the states of aggregation. Water, in particular, was an elementary body of which liquidity was an essential property.’’ (311, our italics)

Kuhn then remarks: "This is not to suggest that modern science is incapable of picking out the stuff that people in 1750 (and most people still) label ‘water’. That term refers to liquid H2O. It should be described not simply as H2O but as close-packed H2O particles in rapid relative motion." (312) Can the essentialist not acknowledge this point as a point about meaning, but still hold onto the essential referentialist conclusion? No, because "The lexicon required to label attributes like being-H2O or being-close-packed-particles-in-rapid-relative-motion is rich and systematic. No one can use any of the terms that it contains without being able to use a great many. And given that vocabulary, the problems of choosing essential properties arise again… Is deuterium hydrogen, for example, and is heavy water really water?" (312)

Essentialism can only answer these kinds of questions by ignoring the ‘systematicity’ that Kuhn is drawing our attention to, and instead by arbitrarily counting certain things as essential, others as accidental – a procedure surely inimical to a scientific approach, and making a mockery of the idea of natural kinds. Kuhn’s view is that we must understand the progress of science as periodically involving the junking of (at least parts of) taxonomies of natural kinds, and their replacement by others. ‘Rigid’ designation no longer seems quite to deserve the name – for, though scientific schemas do indeed (of course, and contra relativistic and sociologistic fantasies) describe/explain the world across time and space, they are themselves often destined, even in many of their fundamentals, not to have the permanency of what they are used to depict.

Bird again tries to counter Kuhn, by suggesting that Kuhn’s reasoning does not touch the ‘essence’ of Putnam’s conclusion that "in all possible worlds water consists (largely) of H2O." The word "largely" here is interesting. Presumably, Bird is allowing what Kuhn also allows: that water with some impurities is still H2O. But what, for example, if those impurities are XYZ? What if those impurities turned out to be somewhat more numerous than expected; what if about 25 per cent of water on the Earth’s surface were ‘discovered’ to be XYZ (so that water is still ‘largely’ H2O)? Would essentialism still look so attractive, then?

It is only given the post-Lavoisieric framework that we are forced to see water as largely H20. Absent that framework, ‘water’-in-all-its-states is not necessarily viewed as a natural kind (as the quotes above from Kuhn make clear: liquidity was regarded as an essential property of water) -- and still less is H20. Kuhn is bringing talk of possible worlds, one might say, back from its metaphysical to a more everyday (i.e. everyday scientific) use. A taxonomy supplies a ‘set’ of possible worlds between which normal science goes on to choose. If something really threatens the taxonomy, we (imagining ourselves now into the position of scientists actually confronted by such an anomaly) cannot retreat to philosophers’ assurances about what all possible worlds must turn out to be like. Rather, sometimes, we must face the need to uproot fundamental assumptions about the set of possible worlds available to us and enabled for us by our taxonomy, our ‘ontology’, our thought-style.

Redubbing is then at least as important as dubbing; and, of course, in concert with Kuhn’s reasoned scepticism as to Correspondencism, progress through revolutions is not well-described as bringing us taxonomies which themselves come closer and closer to matching the universe’s ‘own’ taxonomy.

Kuhn’s conclusions are as follows: "[D]ubbing and the procedures that accompany it ordinarily do more than place the dubbed object together with other members of its kind. They also locate it with respect to other kinds, placing it not simply within a taxonomic category but within a taxonomic system. Only while that system endures do the names of the kinds it categorizes designate rigidly." (314-5, our italics)

Part of the fundamental problem with essentialism then is to do with what we discussed earlier in "The issue of incommensurability" around:

• the anti-contextualist focussing on single words (e.g. ‘water’),
• the attempt to understand the reference of single words without any placement of them in an assertion and indeed in a broader context within which the assertion is intelligibly available; and
• the absurdity of ‘point by point’ renditions of ‘translation’ – recall the issue around translation discussed in ‘Incommensurability 1’..

And part of the problem, relatedly, is the need for a still broader wholism, which we also touched on earlier: this is to do with Kuhn’s sense that a taxonomy of terms must be taken relatively wholistically, and that that fundamental taxonomy/ontology inflects or is a whole style of thinking, which sometimes needs radical alteration, rather than supposed piecemeal alteration (of the kind which essentialists always present scientific change as constituting): "Here and there the old and new lexicons embodied differently structured nonhomologous taxonomies, and statements involving terms from the region where the two differed were not translatable between them." (315). We are really, here, in a new terminology, expressing Kuhn’s constant insistence that ‘conceptual schemes’ are, because of their wholistic character, incommensurable, that one never really transplants an idea or expression from its context to a new one, for to remove an idea from its context is to denature it.

Kuhn’s taxonomic conception has enabled him to defend and re-specify the notion of incommensurability against the idea that it is reference, not meaning, that is important. Whilst this re-specification was needed and effective, it was not enough to satisfy Kuhn himself, who thought that there remained a need for a more substantive understanding of incommensurability, why it was necessary in the first place. A turn to evolutionary theory seemed helpful .

An evolutionary parallel had been drawn in SSR, where the idea of the evolutionary tree as resembling, more, a proliferating bush, had been called upon to help dissipate the idea that for science to be evolving, it had to be evolving toward something. Much later, especially from 1990 on, Kuhn argued that the parallel needed to be made much stronger, that there was a great deal to be gained from developing his own ideas in the form of a Darwinian theory of scientific development. There are various ways in which this analogy can be elaborated. One main one was in construing Darwinism as a theory of animal speciation, and in recognising that what Kuhn had been trying to say about the growth of the sciences was that that was akin to the proliferation of scientific species. The introduction of these new connections to Darwinism into Kuhn’s scheme would lead to a retrospective change of emphasis: the main importance of paradigm shifts would be seen to be in the generation of new sciences , rather than in just the replacement of paradigms within the same specialism. It would provide an enhanced conception of incommensurability too. That could now be thought of as an evolutionary mechanism, one which, by ensuring discontinuity between specialisms, would provide an isolating mechanism, serving to separate each from each, and thus to give them their own, independent, distinct identities.

In 1990, then, Kuhn was ambitious for his Darwinian project, which does seem to have a strongly naturalistic intent, not to be meant as just a metaphoric conceit, but a first use for his new ideas on this was to try to sort out the world changes problem, to make use of the idea of the ‘evolutionary niche’ as a restatement of , if not entirely a replacement of, phenomenal worlds.

Back, then, to the base problem:

Premise one: there is an ‘external world’ of nature.

Premise two: there is a plurality of ‘phenomenal worlds’ that scientists inhabit.

Problem : how can incommensurably discontinuous phenomenal worlds be accommodated within the one external world?

Answer: if we consider phenomenal worlds as ‘evolutionary niches’ then a ‘diversity of phenomenal worlds’ is simply subsumed into the now routinely accepted idea of a ‘plurality of evolutionary niches.’

Now to unpack this argument.

One of the unattractive aspects of the notion of ‘phenomenal worlds’ for Kuhn must surely be that it invites subsumption under the standard dichotomy of ‘objective’ and ‘subjective.’ There is an ‘objective world’ of nature out there, and there is, on the human side of the divide, a subjective – phenomenal - world. But to allow the matter to rest there is to expose Kuhn to those critics who, for example, want to call him an ‘idealist’ since to call the world according to science subjective is seemingly to say that it does exist only in the mind. Kuhn’s resort to evolutionary theory tries to preserve the thought, but to bypass the dichotomy between the object and object sides – in the same way that J. J. Gibson tries to bridge the same dichotomy with the idea of affordances. This was our point about one-and-a-half worlds, since a phenomenal world is not a purely subjective one, being partially constituted by the objective world itself. Therefore, Kuhn sees in the aspect of the Darwinian analogy of evolutionary niches a way of eroding the sharpness of the usual distinction between the subjective and the objective, the dichotomisation of the phenomenal and natural worlds. It will allow him to say that phenomenal worlds are, themselves, real worlds:

Can a world that alters with time and from one community to the next correspond to what is generally referred to as "the real world"? I do not see how its right to that title can be denied. It provides the environment, the stage, for all individual and social life. On such life it places rigid constraints; continued existence depends on adaptation to them; and in the modern world scientific activity has become a primary tool for adaptation. What more can reasonably be asked of a real world? , [TRSS, p.102] emphasis added.)

Our own difficulties with this go back to our discussion of the initial introduction of the ‘world changes’ idea itself. It is quite clear that, from an historian’s point of view, the contemporary scientific world which that scientist inhabits is, for that scientist, the real world with which the scientists must contend. In that world, the world of nature is treated as consisting in [say] two distinct realms, that within the space between the earth and the moon, and that beyond the lunar sphere. Within that scientific world the world of nature is very different from the way it is in our contemporary scientific world, for in the pre-Copernican world, the nature of motion differs between those two realms. Two associated emphases of Kuhn’s are important: his emphasis on the collective character of such ‘realities’, and upon the categorical mode of scientific speech. The working scientist’s reality is the working world of the scientific community, with its entrenched apparatus for conceiving, representing and intervening in the world of nature that unquestionably is no matter of individual subjectivity . ‘Phenomenal world’ does, though, seem to us a poor and misleading description for the characterisation of the portrayal of the world of nature that is installed in any of these working worlds. Within that working world, its entrenched portrayal of nature has the status of reality, which is reflected, first, in the categorical mode of speech: that Earth is not a planet is not a claim advanced in a provisional and cautious way. Harold Garfinkel [speaking for sociological purposes] talks about facts as ‘grounds for further inference and action’, and means this in a definitional sense. From an observer’ s point of view, a ‘fact’ is that which, in the community under observation, is treated by its members as grounds for further inference and action [rather than for questioning, argument etc.]. In the same sense, the entrenched portrayal of nature in a scientific community is a reality, i.e. it is that which, the historian determines, provided the grounds of further inference and action for scientific inquirers. Kuhn’s resort to Darwinism thus seems to us a rather roundabout, and still rather ineffective way, of trying to get these points across. Let us, however, look and see how Kuhn deploys the idea of an evolutionary niche.

An evolutionary niche is not a part of ‘the world of nature’ in the way that a tree or an atom might be conceived to be, but why should one deny reality to an evolutionary niche, say that because it is not part of the world in the way that a mountain is, that it is not part of the natural world at all? The existence of an evolutionary niche is, of course, creature -dependent. A feature of the world such as that of a berry’s being edible by pigeons is not one which pre-exists the existence of those pigeons The feature only exists in relation to the species, and the evolutionary niche is thus identified in an interactional fashion - the evolutionary niche only exists between the world of nature and the species of creature, but, of course, given that relationship it is perfectly alright to say that the evolutionary niche exists in the world of nature. An evolutionary niche is no more a ‘subjective’ aspect of nature than is a mountain [after all, the mountain may figure in, be part of, the evolutionary niche] and is no less a part of nature than the mountain is, but it comprises a part of nature in a different way than the mountain does.

It is important to Kuhn, then, that the evolutionary notion of ‘adaptation’ be understood in terms of the notion of ‘niche’ rather than the other way around. It is, of course, common for Realists to insist upon ‘death and furniture’ arguments. The idea that the world can be given meaning might not be wholly without merit, they may concede, but there is a limit to what can be done. The external world of nature is fixed, and sooner or later, will inhibit whatever interpretations we may care to project upon it. We cannot walk through the furniture, and, more seriously, if we do not conceive of the world of nature in the right way, there will be fatal consequences – if we define something with the wrong chemistry as edible, then we will poison ourselves. We are forced to adapt to the external world. But Kuhn is questioning this notion of adaptation, treating it as too rigid and one-way, and therefore as providing a false dichotomy:

Is it the creatures who adapt to the world or does the world adapt to the creatures? Doesn’t this whole way of talking [about evolutionary niches] imply a mutual plasticity incompatible with the rigidity of the constraints that make the world real and make it appropriate to describe the creatures as adapted to it? [TRSS p.102]

Kuhn’s position is that what actually evolves is not, then, the creature in adaptation to a given, and unchanging nature, for niches and creatures ‘evolve together.’ Returning to the scientific case, Kuhn is now licensed to claim that our ‘worlds’ are niches:

‘Conceptually, the world is our representation of our niche’ [TRSS, p.102-3]

One cannot make, in these terms, any trans-historical comparisons of phenomenal worlds, asking whether any one of them is better ‘adapted’ to natural reality than any other, for the notion of the niche is a two way relation, and therefore one which is tied to the specific combination of environment and organism. One can’t make comparison of fit with other environments and organisms. The analogy, applied to paradigms, means that we can say that each is a reality in its own right, a relationship between the scientific community and its environment, and that we cannot say that one paradigm is better adapted to the same environment than others, since ‘the environment’ is now functionally defined, is a relative conception itself. Thus Kuhn dissociates the role that ‘subject sided’ and ‘object sided’ elements in his own thought, from that of the sharply separated contrast that they more usually make. If this movement were rigorously carried through, it would eventuate in the dissolution of a ‘two moments’ doctrine into a therapeutic reorientation of us back to our everyday (e.g. everyday scientific) lives and concepts.

In sum: the niche is not something which pre-exists the species that is adapted to it, but, rather, ‘what actually evolves, therefore, are creatures and niches together’. (TRSS, 102) And, in favour of Kuhn’s intent here, it should be said that ‘niche’ or (similarly) ‘ecosystem’ is an improvement over what Kuhn inherited; because it sounds less like an ‘object’ than ‘environment’ or ‘world’ does. It thus has a better chance of avoiding doctrines of ‘the given’ and of Sceintific Realism without falling into Idealism.

Thus the real point of the evolutionary analogy is to bridge the opposition between the ‘object-sided’ and ‘subject-sided’ worlds.

But perhaps a better way of making that bridge-- or of showing, therapeutically, that the very idea of needing a bridge here is still too concessive -- is available:

We are unclear from the published work how seriously Kuhn intended his Darwinian turn. It could be an enriching of a helpful metaphor that he has already used, but it does look (in TRSS) as though it is intended much more literally than that, and is Kuhn is about to set out on an ambitious and thoroughly naturalistic account of science as something that does actually (within the terminology of post-Darwinian biology) evolve. If this was Kuhn’s intention then we find it entirely unpersuasive, and unnecessary.

Kuhn’s is attempting to break away from the empiricist philosophy of science that had been his inheritance, but such philosophical inheritances are deep, subtle and penetrative. Kuhn’s need for Kantian thoughts, and therefore, for phenomenal worlds, arises, we think, from a residual element of the empiricist tradition, namely the idea of the visual field as a location in its own right, and one which must possess contents. ‘The contents of one’s visual field’ is a perfectly acceptable commonplace expression, but it is referring only to whatever one can see from one’s current vantage point. Whether the traffic light is among the contents of one’s visual field asks simply: is one now looking toward the traffic light? The capacity to identify things in one’s visual field obviously depends upon prior experience, as is clearly the case with knowing what a traffic light is, but one’s capacity to make such identifications is not itself any part of the visual field. What is observed is not, therefore, any kind of admixture of natural and mental elements, and there is, therefore, no need to be troubled in the way that Kuhn is by the need to understand how such elements are fused in experience.

There is in fact available a ready way of disposing of Kuhn’s puzzlement before it even starts, and thus of negating the felt need for bolstering of one’s view by reference to alleged naturalistic support for it (viz. nonmetaphorical evolutionism), by means of Gilbert Ryle’s distinction between ‘thick’ and ‘thin’ description. The difference between someone who sees ‘a rain cloud’ and someone who sees merely ‘a cloud’ in the same place is not a difference in the cloud that they see. Both can be said to see one and the same cloud, just as they can both be said to see something different – in this case, one can see something that the other cannot. It is not, either, that one can see one kind of cloud and the other sees a different kind of cloud. The one who sees the ‘rain cloud’ can tell, as the other cannot, what kind of cloud they are both looking at. The description ‘cloud’ is a thin description when compared with ‘rain cloud’ which is much thicker, i.e. is replete with understandings that do not inform the thinner description. The one who sees the ‘rain cloud’ does not witness a cloud with additional features than one who sees only the cloud does, for the features of the cloud that the former notices are also within the visual field of the latter. But the one who sees the rain cloud can make more of what is seen than can the other, can notice things about this cloud that the other cannot. The difference in what they can respectively see lies not in the ‘contents of their visual field’, but in what they can bring to bear on their observation. The one who sees the rain cloud can discern the significance of those same features that the one who sees the plain cloud may not notice or understand. To say that it is a rain cloud is not to provide a mere report of an observation, but to involve a certain predictive element: it is a ‘rain cloud’ because it will bring rain soon, because it is being blown in this direction, will pass over high land etc. The capacity to make such a prediction involves a deal of background understanding about how the size, colour, location of the cloud and the direction of the wind affect the behaviour of clouds in general.

Thus, there really need be no compulsion to find, as Kuhn does, something of a puzzle as to how the Galilean and Aristotelian sciences can both be looking at the same thing and ‘seeing something different’. They are, of course, seeing the same thing thinly described, namely, the stone swinging on the end of a piece of string, but they are observing the swinging stone with respect to its motion. The motion of the stone is not to be given, for scientific purposes, by a thin description such as ‘swinging back and forth’, for they -- the two scientists -- differ over the kind of motion ‘swinging back and forth’ is, whether it is constrained fall or pendulum motion. These are two thick descriptions of the motion of the string, and presuppose the different apparatus of ideas that make up Aristotelian and Galilean physics respectively. The thick description of the stone’s motion is not meant to provide only an accurate capture of the thinly described contents of the visual field for, of course, both constrained fall and pendulum motion would each allow them to report in thin terms exactly the same back and forth movement. It is misleading to think that the physicists are engaged in attempting faithfully to describe their experience, to report accurately what they have found in their visual field, and to recognise that they are treating their observations as a means of applying specific scientific systems.

Their case is different from our ‘cloud’ example, where we wanted a contrast between the thinner description ‘cloud’ and the thicker description of the same thing (‘rain cloud’). In the case of the swinging stone example, however, we are dealing with two thick descriptions. It needs, after all, to be recognised that ‘pendulum motion’ is in an important sense not, as it may seem to those of us who have inherited Galileo’s system, a thin description at all, but one which depends upon assumptions about what propels the motion, what would happen if certain counterfactual conditions obtained, and so on.

Being thick descriptions, because they are both paradigm-based, Galileo’s and Aristotle’s are rival descriptions, and they cannot be treated as jointly compatible with the same observations. To intimate the latter would to treat the observation as though it were itself adequately described in ‘thin’ terms, but this is not so. There is no scientifically useful description which is neutral between the two rival descriptions. A neutral description would have to be at best something like: a stone swinging on a string. But to speak of ‘a stone swinging on a string’ is not to give a scientific description at all: it is naïve, ordinary, and too basic to do anything with. Such a description would never or rarely be included in the report of an experiment. The report (if by a Galilean, would run, "A pendulum was set in motion; it…"). In other words, part of the contest between the two traditions is precisely over what it is that is being observed (which point Kuhn himself well appreciates in other contexts). The divergence between the two thick descriptions does not reside in the visual or perceptual field, for it does not reside in nature itself. It is the working world of science [not nature] that accommodates these different phenomenal worlds. Kuhn’s difficulties with ‘many worlds’ can, we think, be put down to his confusions about the relations

• between different kinds of descriptions
• between tenses,
• and in the articulation of different discourses.

We have drawn out the way we see the first of these confusions, cashing it out in terms of ‘thick’ and ‘thin.’

What Kuhn himself teaches us, is that the language of scientists-under-a-paradigm is, of its nature, categorical, and he also teaches us that paradigm shifts involve the retrospective eradication of a prior mode of discourse. What was categorically said under a prior paradigm can no longer seriously be asserted at all.

Kuhn’s inclination to find an ongoing problem here, insofar as it is an inclination leading him to want a theory of meaning or a substantive metaphysics, is a result of the disregard of what he is otherwise teaching us in his own descriptive account of the course of scientific revolutions, which is that ways of describing things are withdrawn from us and retrospectively overruled (see e.g. SSR pp.114-5). We have taken it to be Kuhn’s singular merit that he has sought to point out that the supposed problems of the philosophy of science are in most cases ones that the scientists must solve in practice. We might count this lesson as echoing some of Marx's arguments, and as paralleling those of Wittgenstein’s philosophy or of ethnomethodological sociology..

Kuhn does not, however, appear always to appreciate that this is his crucial contribution, and occasionally falls into imagining that what the scientists are doing poses a philosophical problem in the classic sense: one that requires a philosophical doctrine for its solution. Thus, it is a perfectly correct for Kuhn [the historian] to say that up until a certain date chemists identified only ‘mixtures’, and that prior to that date ‘compounds’ were absent from chemistry: therefore, ‘first mixtures, and then compounds’. But this is of course a description of the change in chemistry’s concepts, and has nothing to do with the change in the nature of chemical substances. It is a very different thing to describe an historical change in chemistry’s concepts than it is to engage in reconstituting chemistry’s concepts, which is what those whose activities Kuhn is reporting on were actually doing. And it is another thing altogether to imagine chemical substances themselves actually changing their nature some time in the 18th century, coincident with the change in chemistry’s vocabulary. We are not saying that Kuhn requires one to imagine the latter: but that the misinterpretations of him along such lines are at least understandable, given how long herhe persisted in making it appear as though there were a deep problem here which might yield to a theoretical solution..

The introduction of the concept of ‘compound’ was not intended to initiate the existence of some entirely new sort of phenomenon, one that exists as well as the phenomenon of mixtures. The concept of ‘compound’ was a rival to that of mixture [this is its interest to Kuhn, after all] and it is introduced so as to replace the latter [although, of course, the word ‘mixture’ remains in use in chemistry, but now with a ,changed meaning,, as a contrast class to ‘compound’]. If the revolutionary aspiration of ‘compound’ is successful, then the word ‘mixture’ [in its original use] will be withdrawn from further discourse in chemistry, except [in its new use] to refer to something quite specific and less chemically interesting (e.g. soil being carried along in a river is a (physical) ‘mixture’ in this sense) – and one can date (though not to the very day, even in principle) the occurrence of that transition. Before this date, ‘mixture’; for this period of years the rivalry of ‘mixture’ and compound’; after this date, ‘compound’ only (plus merely physical mixtures). However, and this too is a descriptive observation, it is also equally clear that the introduction of ‘compound’ operates with retrospective force: it is not introduced to apply only ‘from this date forward’, but is to apply to cases that were adduced in the past as cases of ‘mixtures.’ In the new scientific discourse, these substances never were mixtures, they were compounds all along.

Of course, it is the historian’s role to note and report such changes, not to endorse them, and the fact that for scientific purposes one discourse retrospectively pre-empts another is not something for which the philosopher need contrive a workaround.

There is only the appearance of a worrying divergence here between scientist and historian. What is necessary in the historian’s terms to avoid Whig excesses is very different from what is involved in taking part in the installation of a paradigm, and Kuhn’s phraseology of world changes here is really only a [striking] conceit. Says Wittgenstein, say what you like, so long as you don’t blind yourself to the facts. As it proved, however, Kuhn’s conceit proved a risky one, and ,served to confuse himself sometimes, blinding him to facts that, otherwise, are plain and pretty much indisputable. In sum, the ‘world changes’ locutions by no means sink Kuhn’s project; but they are, we think, very needful (at least now) of being deflated down to earth. With our Rylean and Wittgensteinian manoeuvres, combined with the adducing of the morals of Kuhn’s impressive discussions of kinds and of taxonomies (and of his somewhat more contorted discussions of Kant and Darwin), we hope to have put the reader in a position to understand why Kuhn wanted to say some of the things he said that have most bemused people -- and of why, in the end, he didn’t really need to say them. Or at least: Of why one doesn’t need to say them any more.

Clearly, we are convinced that the real Thomas Kuhn has been far less influential than the legendary one, something that was obviously very frustrating to the real one, with whom we are in agreement that the legendary Kuhn’s influences have often been for the worse. We have tried to show that many of the supposed major errors for which Kuhn has been condemned are not to be found in his work. Certainly he does say things of that sort that upset Weinberg for example (as detailed in the Introduction) but, considering those things more sympathetically and in context, there seems little need for Weinberg to find them as disturbing as he does – indeed, if he had rather tried to understand why Kuhn thought it persuasive to say these things and what he meant by them, he might have found them much less troubling. There is little point in blaming the real Kuhn for the fact that the legendary Thomas Kuhn has had such an influence – Kuhn is not the only or even first major thinker of recent times to have had his thought extensively misunderstood and his intentions badly distorted, but the fault there lies very largely with those who have exploited and misrepresented Kuhn to advance causes very different than those his work did and could support.

By and large, we have portrayed Kuhn as continuously concerned largely with one issue – spelling out the meaning of proper historical studies of episodes in history of science for the philosophy of science. Late Kuhn came to think that his constant concern was best expressed as being with change of belief in science (cf. TRSS, 95-6, 112) The same late Kuhn came to fear that his – and others’ – emphasis on history had helped mislead so many, from whom he now needed to dissociate himself, and also that this emphasis had in any case been too great. He thought that much of what was done could have been done without the history [or, at least, so much of it] and more on philosophical grounds alone. Kuhn was surely right that, as a matter of fact, the emphasis on history had (and has) misled many. But was the message to take from this that one should downplay history, to the extent that Kuhn even comes, at one point in the 90s (TRSS, 112) to claim that everything important in his work could be deduced ‘from [philosophical] first principles’? We suspect that this was an overreaction on Kuhn’s part. Kuhn demanded a lot of his readers, especially in SSR – sadly, the (vast) degree to which they (be they Scientific Realists or PostModernists, Falisificationists or SSK-ers) fell short of these expectations deformed, we believe, the shape of much of Kuhn’s later work. So concerned was he not to be identified with ‘historicizing’ and ‘sociologising’ circles – because of he had been misread in these circles, and also because of the difficulty of being taken seriously by philosophers (like Shapere, Putnam, Popper and Quine) if one was seen as moving in those circles – that Kuhn came to say that it was only really philosophy – and indeed ‘science’ (biology, psychology, ‘artificial intelligence’), insofar as it bolstered that philosophy – that was his interest, his overriding concern. But was Kuhn here expressing a recent realisation, or giving voice to a thought that had always been with him? It seems that it must be more the former, a formulation of something that, whilst it might always have been true, was something that Kuhn had only lately clearly seen.

But even so, a Kuhn-loyalist might ask whether we ourselves have not misrepresented Kuhn by placing as much emphasis as we have on Kuhn’s historical studies, mistaking the fact of their prominence in Kuhn’s writing up to the mid-nineteen seventies for a sign that they were more important to Kuhn than they really were? We have urged the importance of reading Kuhn’s historical studies as a means to better understanding of his philosophical arguments. We do not want to deny that anyone could get a clear conception of Kuhn’s philosophical arguments from reading SSR alone, and reading it carefully, but it is equally clear from the last forty years of Kuhn’s reception that reading SSR alone can and usually does give a woefully false impression of what Kuhn means by what he says there. The historical studies provide a basis for seeing much more clearly what Kuhn has in mind in his philosophical arguments, and for moderating many of the anxieties that those provoked – there is no need to imagine that the edifice of science is shaken by the ‘revelation’ that Copernicus had much less responsibility for the revolution named after him than such naming might suggest, and that the scientific - technical - merits of his work were less than he advertised them as being, and less an improvement on previous work than he had supposed, and even that over a long period of time astronomy went through a serious conceptual change. If these are the sorts of thing that Kuhn is trying to tell us, then how hysterical and wild were many of the reactions to his work appears more clearly. One might put it like this: Only to a historian (i.e not a practising scientist), and only then before they have done the required historical work, does a scientific revolution need to appear both real and dramatic.

There certainly is a constancy of purpose, then, throughout Kuhn’s career, though the way in which it was pursued varied, perhaps especially after the publication of SSR. After that, Kuhn remained preoccupied with the issues arising from the book, but did consider, and in his view, importantly revise some of the ideas expressed there, as he attempted again and again to explore, to clarify, to express more effectively, or to defend the thoughts in SSR. But was Kuhn’s thought ever quite consistent? We think that there are quite different strands in it, and that these are in tension with each other. This tension, we find unresolved in Kuhn’s published works. We do not think that the difference between these three strands is one that Kuhn would himself acknowledge, and, indeed, it is perhaps his failure to appreciate the difference between them that has given him the most trouble and left him most unsatisfied.

We have generally endeavoured to keep our own – Wittgensteinian – views pretty much in check, though it may have become increasingly apparent that we find Kuhn most defensible when he is closest to offering therapeutic possibilities, when he is dissolving the philosophy of science, using his account of science thoroughgoingly to subvert and overcome the main traditions (the ‘received views’) in philosophy of science. This, we think, is a very important and much-underestimated theme in Kuhn. So much so, that we regard our exegesis earlier in this book, combined with our bringing out of therapeutic aspects of Kuhn’s work on the methodology of science, on incommensurability, and so on, as amounting to a recovery of Kuhn’s thought, a making of that thought available to a contemporary intellectual scene that falsely considers that it knows what Kuhn is saying and has absorbed it (or refuted it). Kuhn’s ‘Wittgensteinianism’ is present in his ‘underlabouring’ for the historiography of science; it is present in his ‘anthropological’ attitude to past science; it is crucial for his distrust of normative ambitions in the philosophy of science, and for his scepticism as to explanations of ‘the real nature of science’ or of ‘how scientific progress is possible’; it is crucial for his emphasis (discussed further below) on science ‘as nitty-gritty’ (thus distinguishing science properly from metaphysics, i.e. from speculation); it is part and parcel of his displacement of epistemology by description, and of his severe questioning of the fantasy of a transcendental standpoint in philosophy. Furthermore, it is involved in his very style of writing , especially in SSR. Kuhn, like Wittgenstein, demands thought from his readers, not the transformation of his work into slogans.

However, we do not want to – and could not possibly – claim Kuhn exclusively for the Wittgensteinians; for Kuhn plainly wants to be a good old philosopher too, and for him that means, more or less, a philosopher in the analytic tradition represented by such as Quine, Davidson and Putnam.

We think that in his skirmishes with these distinguished thinkers Kuhn in the main more than holds is own, and successfully maintains that his notions of incommensurability and world changes do not entail the errors that they are criticised for. In fact, we would go further: two of the main trends of modern American philosophy – Davidsonian antagonism towards ‘conceptual schemes’, and Kripke/Putnam essentialism – were in large measure designed to combat an intellectual tendency epitomized in Kuhn – but in our view, not only does neither attack on Kuhn successfully hit home, but Kuhn provides one with the intellectual resources to counter these very attacks. Kuhn shows in great detail, throughout his career, how there is room for what talk of ‘conceptual schemes’ wants to get at (though that term may well not always be the best term to use, and of course, Kuhn himself inclined increasingly towards different terms, such as ‘scientific taxonomy’); and Kuhn argues efficiently that Essentialism is a useless and abstract shuffle (though of course Kuhn allows that we can perhaps helpfully speak of scientific revolutions as being shifts between untranslatable taxonomies of natural kinds, if that will help us to understand what is going on in science; thus he points toward a non-Essentialist, non-metaphysical use of the term ‘natural kind’, deflating the Putnam’s and Kripke’s hopes for the term).

Even so, Kuhn is too ready to accept that he needs to elaborate a philosophical rationale for his notions (too eager to escape the abuse of his views in the writings of the likes of Barnes and Fuller, not to mention the travesties practiced on him by the broader coffee-table culture); and is thus drawn into treating metaphysical issues more ‘seriously’ than he need do . In doing so, we think that he is neglecting other of his own arguments, those of the therapeutic sort (see above), and is in tension with those. Kuhn’s efforts to make his meaning more precise, his (partial) defence of ways of speaking he had adopted provisionally, earlier, often tends to become a reification, or a theorisation, to an extent greater certainly than we would have wished.

Sometimes, Kuhn’s tendency to metaphysics and to ‘theorizing’ (e.g. his tendency in later years to say explicitly that he has hopes of being part of developing a new ‘theory of meaning’) tends to involve the development of what might be called a ‘relativistic’ metaphysics (for example, on occasion in relation to ‘World Changes’, as we discussed above in Chapter 65 ). Sometimes, it is more empiricism or positivism which is the covert metaphysics that Kuhn is leaning towards – we have discussed this tendency in relation to his inability to transcend the myth of ‘the given’. Hoyningen-Huene’s major and still-really-valuable ‘reconstruction’ of Kuhn’s thought plays into Kuhn’s tendency to have a ‘relativistic’ (pluralized ‘Kantian’) metaphysical view or theory, and fails to recognise the ‘Wittgensteinian’ aspect of Kuhn’s work. Some recent critics have tended instead to emphasize the positivistic Philosophy latent in some moments of Kuhn’s work.

The two most recent book-length studies of Kuhn – Bird’s and Fuller’s – have been hostile to Kuhn. Bird and Fuller come from completely different standpoints – Bird is a naturalistically inclined analytic philosopher; Fuller is a major player in politically-oriented Science Studies. But both miss Kuhn’s therapeutic moment almost completely; both emphasize Kuhn’s affinities to positivism most strongly.

There is a third element in Kuhn’s thought, a ‘scientific’ naturalistic streak that only appears overtly on odd [very odd] occasions. Bird believes that there is not enough of this in Kuhn. We think the reverse. The major manifestation of Kuhn’s naturalism is in his latter day enthusiasm for Darwinism (and more generally for quasi-biological renditions of the nature of science), and for outlining thereby what is certainly stated as if it were a serious intention to consider the development of scientific specialisms in terms of natural selection, with the notion of ‘incommensurability’ as a mechanism of speciation, a means of insulating different specialisms each from the other. We cannot see how Kuhn could possibly have pursued this idea seriously (i.e. literally), nor why he should really think it would gain anything for him [the idea of the ‘evolutionary niche’ could serve his philosophical purposes sufficiently well on a metaphorical basis]. An earlier outburst of such gratuitous naturalism arose in his ‘Second thoughts on paradigms’ when he abruptly announced that his account (already somewhat problematic and overly ‘cognitivist ’, in our view) of the way in which a child learns to discriminate between water fowl is a process of the sort that

‘can easily be modelled on a computer; I am in the early stages of such an experiment myself. A stimulus, in the form of a string of n ordered digits, is fed to the machine. There it is transformed to a datum by the application of a preselected transformation to each of the n digits, a different transformation being applied to each of the n digits, a different transformation being applied to each position in the string. Each datum thus obtained is a string of n numbers, a position in what I shall call an n-dimensional quality space. In this space the distance between two data, measured with a euclidian or a suitable noneuclidian metric, represents their similarity. Which stimuli transform to similar or nearby data depends, of course, on the choice of transformation functions. Different sets of functions produce different clusters of data, different patterns of similarity and difference, in perceptual space. But the transformation functions need not be manmade. If the machine is given stimuli which can be grouped in clusters, and if it is informed which stimuli must be placed in the same, and which in different clusters, it can design an appropriate set of transformation functions for itself. Note that both conditions are essential. Not all stimuli can be transformed to form data clusters. Even when they can, the machine, like the child, must be told at first which ones belong together and which apart.’ (ET, 310)

One never again hears of this – thankfully, in our view. But the naturalistic strand is clearly there, in the 80s and 90s as well as in the 70s. We are not sure how deep this strand runs through Kuhn’s thought, but suspect that it may be one which is implied in Kuhn’s self-reflexive tendency to think sometimes that his own efforts ought to be comprehensible in terms of his own scheme, leading him to think of what he is doing as close kin to science.

This tendency to self-reflexive application is present both in SSR and periodically ever since – it can be seen as cute, and clever; and Kuhn was indeed right to worry that he might refute himself, and so to try to guard against this. (He knew that his esteemed predecessors in Logical Positivism had failed most essentially because of self-refutation, because their Verificationist criterion ruled itself out of order). But we think that Kuhn’s understandable worry on this score, and his understandable wish to enjoy the cuteness of being able to speak of his own place in history in the same way as he could speak of the history of science, had a seriously negative consequence. It encouraged Kuhn to believe, erroneously, that what he was doing was actually itself a kind of science. As Wittgenstein would put it, Kuhn has, like many distinguished thinkers before him, the alleged method of science far too much and too constantly before his eyes. One might say that this is not surprising, for an ex-scientist, for a historian and philosopher of science – one might also say, however, that it is especially ironic and unfortunate that, despite all Kuhn’s achievements, he remained in too great thrall to the very image of science as a ‘telos’ for all human inquiry that he did so much to dispel.

So: Kuhn encouraged himself to think that his brand of philosophy was either super-science (metaphysics), or continuous with science (positivism, or Quineanism), or simply science (‘naturalism’). And this had the added virtue of providing a further bulwark against the likes of Barnes, Fuller, Sandra Harding, Barbara Herrnstein-Smith, Lyotard, etc. etc.: if what Kuhn was himself doing was science, then it could hardly be the ‘soft’ political/sociological/historical stuff that those folks (along with Popper, Scheffler, etc.) claimed it was.

Kuhn played, dangerously, with the idea that the philosophy of science was in crisis, that he himself would help to engineer the new paradigm, etc This involved forgetting the deflationary/therapeutic dimensions (and also the historiographical ones) of his own practice; it involved dangerously prognosticating the future of philosophy of science; it involved failing to hold clearly in view that plainly the philosophy of science is philosophy, not science. It involved, in short, a lapse into scientism, into fantasising that one was oneself engaged in science; in biology, say, or in something like it.

The positivists were right to be dismayed by the discovery that their own practice failed their own criteria, because for them philosophy was through and through (continuous with) science. But Kuhn had the resources available to him to not make such a mistake – he didn’t need to worry that what he was doing could not meet the ‘criteria’ (i.e. the existence of paradigms, etc.) that he found exemplified in real science (as opposed to programmatic – pseudo – science). He should have been content to be a philosopher (and a historian, etc.). But he couldn’t help wanting, so it seems, the cuteness, and the prestige, not to mention the ‘protection’ against misunderstanding, apparently involved in the status of (post-positivist) empiricist philosopher, or of (relativistic) metaphysician, or of ‘scientific naturalist’ [e.g. psychologist, biologist, computer programmer]. This, to us, is a matter of regret, since it adds nothing to and engenders confusion about the real substance of Kuhn’s achievement..

Where Kuhn is at his best – and this we think is completely consonant with (and indeed representative of) the deflationary, Wittgensteinian aspect of his thought – is rather in the following important suggestions that Kuhn makes re. how to think about science:

>>That science is about the detailed understanding of phenomena

>>That paradigm innovation is rooted in knowledge of the phenomena and not in any exceptional understanding of truth (let alone of ‘methodology’)

>>That the unit of science is the solved problem, and that scientific innovations gain their purchase by virtue of ‘technical bite.’

>> That revolutionary paradigms are unfinished productions.

These are not the attention grabbing formulations that attracted fame and misfortune to Kuhn, but they are the ones that make clear, first of all, that he does not view science at all in the way that philosophers of science are often apt to do, which is as the fulfilment of metaphysics, providing us with the ultimate categories for the characterisation of nature [which is itself assigned, by those metaphysically inclined, the status of ultimate reality]. This is not to deny that scientific categories ‘fit nature’, but that they do in a way, to an extent, relevantly to certain problems and relative to a paradigm, and perhaps most important, seemingly in a way the relevant scientific communities deems better than the previous paradigm; further, that it is not the business of science to produce a set of general categories of the kind that metaphysics seeks. Kuhn has done away with the idea of the philosopher of science as the transcendental adjudicator of different scientific schemes [though his Darwinian ‘naturalism’ is in part a covert attempt to re-introduce such a transcendental standpoint], one who might provide grounds for deciding which of several different paradigms should be deemed to ‘best fit’ nature, for the judgement as to whether one paradigm fits nature better than another is one which is unavoidably internal to science itself, where the question of ‘fit with nature’ is cast in the form of highly specific configurations of technical issues, and where the decision between paradigms [insofar as it is a decision at all] is cast in the form of an assessment as to the success and importance of a solved problem.

In trying to make clear where we think Kuhn has gone wrong, as well as right, and what lessons one might arguably draw for the future of intellectual reflection upon science, are we departing overly far from Kuhn’s own views and self-understanding? But our first (if not our last) basis for appraising Kuhn in this book has been on the basis of his own arguments and relative to the objections of his critics. This is why we have placed such emphasis on trying to understand what Kuhn does say. If one does that, then one sees that his case is well argued compared with that of so many of the critics, and that he is largely exempt from their strictures since these merely miss their target. It is not always the case that Kuhn's ideas are well argued, as we have tried to make clear in our Part Two, and it is sometimes quite plain that Kuhn is in serious difficulties (that are frequently very much of his own making). One can see that Kuhn has got himself into an uncomfortable position and is thrashing around. It is only after we have made such assessments of the stronger and weaker parts of Kuhn's corpus that we can make the diagnosis we are making here: that the more successful and least problematic parts are those which tend toward the therapeutic, and that the least satisfactory are those in which he seeks to affiliate himself to the main traditions in Anglo-American philosophy (including ‘scientific naturalism’). Thus, it does not matter whether Kuhn would or would not explicitly link his thought to Wittgenstein's (though of course Kuhn did himself on occasion suggest quite explicitly a certain degree of alignment for we can still find that there are strong affinities between the two (as illustrated in the way in which Kuhn's views on incommensurability, when understood aright, come so close to those of the Wittgensteinian Peter Winch. We want to explore the therapeutic and deflationary aspect of Kuhn’s thought a little further, in the last pages of this book.

Attempting to affiliate Kuhn and Wittgenstein in the way we are attempting here may do the former no favours, especially since there are so many who 'know' that the therapeutic view of philosophy can't be right, and will respond that Kuhn the wild idealist, relativist and irrealist - while he might be wrong headed [or never really have existed] - just is so much more interesting than Kuhn the Wittgensteinian 'quietist.' But Kuhn’s ‘Wittgensteinian’ implications are dangerous, but in a way that the commentators on him are generally unwilling to recognise: they are dangerous to the philosophy of science rather than to science itself. The Wittgensteinian traits to be found in Kuhn diminish the content of the philosophy of science relative to what has traditionally been envisaged for it, and, we hold, if developed still further threaten to evaporate that pursuit altogether. As it is, the legendary Kuhn has had the greater influence, being used by the commentators to allow themselves to continue with philosophy of science – even if they have tried to change its name to, for example, ‘sociology of scientific knowledge.’ Their creation of the legendary Kuhn has been used to license continuation of the argument as to whether science can ‘represent reality’ or not? From Wittgenstein’s point of view, argument over this global question will be futile, since it is only [to put it in Kuhn’s terms] in the context of a scientific controversy itself, and as part of that controversy, that the question as to whether this or that paradigm best represents reality can be raised, if at all. And the question is there, of course, to be answered by further scientific controversy and further scientific work. The hard lesson of Kuhn [again, just that of Wittgenstein] is that the questions as to whether science represents reality or makes progress are not philosophical questions about science, but can only ever be misleadingly abstracted versions of concrete scientific questions.

This is really a point on which Wittgenstein is more resolute than Kuhn, who seeks to accommodate to Realism without giving up those views that make him so uncomfortable for most Realists. Wittgenstein does not think that anything that matters is lost if Realism is ‘given up’ since it has no substantive content, no material differences with its supposed rivals such as phenomenalism or idealism: the disputes amongst these camps,

‘…between Idealists, Solipsists and Realists look like [this]. The one party attack [sic] the normal form of expression as if they were attacking a statement; the others defend it, as if they were stating facts recognised by every reasonable human being’ (PI 402)

That all the sound and fury might have signified nothing is something perhaps too terrible for many to contemplate.

Kuhn is like a Wittgensteinian dissolutionist and much less like the 'realist' in thinking that 'realism' does not matter to the motivation and progress of science. Kuhn too shows that the central problem of the philosophy of science - about the relationship between scientific schemes and the intrinsic properties of nature - is wrongly posed. However, there is no further court of appeal - the only possible talk about the intrinsic properties of nature must take place in and through the paradigm- based work of scientists. There is no way of standing back from the succession of paradigms and asking for an independent way of determining whether this is a progressive movement, whether there is a continuing advance toward determining the intrinsic properties of reality itself.
It may seem like a kind of cynicism to observe, as Kuhn does, that the succession of paradigms is a matter of progress, since the story of scientific change is characteristically written by the victors - a version of might-makes-right perhaps?

But Kuhn’s picture is much less voluntaristic than many constructionists want it to be -- the respects in which for Kuhn science resembles the arts are palpably not respects licensing an 'anything goes' approach(even in the arts). This is why, contrary to Feyerabend’s allegations, Kuhn’s work cannot really be understood as involving, even if only ambiguously, a methodological injunction of the sort Feyerabend thinks he sees – for Kuhn, the ways in which not just anything goes are built into the nature of the discipline(s) which he is discussing, and neither require nor can be given 'supplementation' by methodologists/philosophers. In this respect Kuhn differs from Popper, who wants his ‘methodology’ to recommend efforts at refutation, and from Feyerabend, who wants to recommend proliferation of paradigms.

Postmodernists, ‘social epistemologists/constructivists’ and the like tend to think that Kuhn has licensed voluntarism in science – this is a complete misunderstanding. Even Popper is too much of a voluntarist for our ’s or Kuhn’s liking – he speaks of ‘criticism’ and imagines ‘bold conjectures’ where these would be and are frequently just irrelevancies. Philosophical ‘Realists’ tend to see all of the above (including Kuhn) as problematically voluntaristic – but even they are not as clear as Kuhn is on the ways in which the concrete reality of scientific practice makes their dreams of rational choice between theories hopelessly abstract! We suggest that Kuhn is actually the least voluntaristic philosopher of science that there is!

Kuhn’s central ‘argument’ is a descriptive one. As our reflections on Kuhn’s implications for the social sciences showed, Kuhn’s ‘argument’ is just that this is how things have happened in the natural sciences. Paradigms have emerged, there have been revolutions. The development of science has narrowly constrained the range of possible options, even at points of crisis. The idea of individuals attempting to foment scientific revolutions or counter-revolutions for their own sake is just a meaningless one in this context. In an area of science which is unified around a paradigm then scientists will be working on their problems, and they won’t be interested [let alone have time to take an interest ] in stuff which does not bear upon their problems. That someone else is attempting to develop a new paradigm when, so far as they can see, there is no need for one is hardly likely to seem other than perverse. Feyerabend really wants scientists to be keen on the proliferation of paradigms on [democratic and epistemological] principle– either this is what scientists would do, if the matter was made clear to them, or, if they do not, then they ought to be converted into the kinds of people who do value these principles. But Kuhn’s point is that the possession of paradigms is not a principled matter in that way at all. People subscribe to the paradigm simply, so to speak, because, they subscribe to the paradigm: it speaks to them in ways that other scientific doctrines don’t, they are convinced by it even if others aren’t and are categorical in their attachment to it. Attempting to make changes in science of the sort that Feyerabend envisages would not just be a matter of introducing something new – the proliferation of paradigms – into a science that would otherwise remain unchanged, but would, if Kuhn’s account of paradigm shift is accepted, be a matter of having to change pretty much everything about science, including the kind of people scientists are.

To speak more generally, for a moment: One of the things that underlies the typically philosophical concern with rationality (and much thinking about people’s activities in the human sciences) is that doing things involves deliberative decisions, that people weigh up pros and cons, and opt for the side that offers to them the most favourable balance of pros and cons. This is what so-called models of rational action are like, but, as Kuhn has emphasised throughout the study of scientific revolutions, the way in which scientific development pans out does not originate in deliberative decisions – the extent to which people react and respond to circumstances is much more important – they characteristically do not choose to respond as they do, they ‘just’ respond as they do. Thus, it is just that people can’t find something interesting, that they can’t get the hang of it, that it leaves them cold, that they can’t leave it alone and must keep picking at it, and so on.

To reiterate: Many of us still need to be reminded that there just is no way to nature other than through scientific paradigms, and there is therefore no way to nature other than through the invidious comparison of paradigms. There is no such thing as comparing paradigms as live options other than through engagement in the revolutionary controversy, and no live-option basis for comparing them other than those which scientists themselves use in those controversies. The considerations involved are characteristically highly technical and markedly prospective, not to mention relative to concerns and sensibilities. At the time that the sides line up during a revolutionary crisis, there are not perhaps any categorical considerations which favour one side over the other, and the pros and cons being bandied about can affect one individual very differently from another, whilst the future prospects of the paradigms is a matter of mere speculation. Anyone who wants to adjudicate between the paradigms is taking part in - not standing aside from - the revolutionary struggle, and only someone who has some knowledge of and stake in the issues can seriously take part. When the revolution is over and the paradigm shift has taken place (if that is the outcome of the struggle) then the two paradigms are no longer both live options. Exercises in showing that the science might have persisted with the rejected paradigm rather than gone over to the new one [cf. Pickering,1984)] are of historical interest only. The whole logic of SSR is that sciences never reinstate rejected paradigms. The scientific revolution, when it is over, is so much water under the bridge.
The fact that there is not, at the time of revolutionary upheaval, there is nothing to vindicate the shift from one paradigm to another does not mean that subsequent developments cannot show that decision to be vindicated [nor, of course, in the light of what is said in the previous paragraph, do we need to think that the shift must somehow, sooner or later, be vindicated – that it has been made is the fateful thing] . The nature of scientific revolutions is such that within the sciences themselves there is no one except 'the victors' left to write the story of paradigm change.

A caution is called for. We must be very careful not to suggest that Kuhn is - in his histories - trying to do something that we are now saying his writings about scientific revolutions say cannot be done. Kuhn's histories are meant to provide - we use the word without apology - objective historical accounts of what went on at a particular time in a scientific revolution, an aim which he specifically counterposes to that of writing 'Whig history' of science i.e. history 'from 'the victors' point of view.' Any contradiction is only apparent, for of course the kind of story which Kuhn seeks to tell is of a different kind to that which the scientific 'victors' want to tell. Kuhn's accounts have no stake in the scientific outcome of paradigm changes, whilst this is, of course, the very thing that matters to scientists, and, of course, the paradigm which is now in place is the measure, for them, of scientific achievements. The kind of histories Kuhn can write will not give scientists reasons to rethink their contemporary science -- such studies cannot scientifically re-animate the past. The reasons why scientists accept the paradigm they adhere to are (intrinsically) comparative ones and they are [in the science] the reasons why it is better. There is nothing else for them to say. Their predecessors' paradigms are no longer scientifically credible. Kuhn does not seek to rescue those predecessors from rejection, but from the condescension that sometimes accompanies rejection. Neither the historian nor the philosopher can be meaningfully engaged in second-guessing the scientist.
(??)


An Evil Influence?
Arguably, Kuhn has been not just the most influential philosopher of science in the second half of the twentieth century, but the most influential philosopher, full stop; even though he was not a 'proper' philosopher, and tended to be at his worst when trying to be one of those.
Kuhn's position with respect to science is, as we have already suggested, parallel with Wittgenstein's in respect of philosophy leaving everything as it is. It might be thought that Kuhn's influence is testimonial to the falsity of Wittgenstein's assertion for Kuhn has had, willy nilly, a tremendous influence and, intentionally or not, has contributed to a transfiguration of the intellectual landscape. Kuhn has been recruited to the 'science wars', and to the 'culture wars' more generally. He is subject to many vitriolic assaults precisely because he is seen as a totemic figure for the 'irrationalist' forces which are marshalled against the realist and rationalist forces on the side of science. Kuhn is invoked by both sides in these disputes as only one of several, but nonetheless a major, source of 'relativism' in contemporary culture. Kuhn certainly has not 'left everything as it is', it might be said.
One of the things wrong with ‘realism’ is that it invites ‘relativism’, the dissatisfactions that it gives rise to encourage the formation of an opposition to it, and one form that these can take is the ‘relativist’ mode. But if ‘realism’ is without substance, then so too must ‘relativism’ be. The implication: that those who set themselves out as relativists are not - except in their inclination to recite supposed relativist doctrines - relativists at all. Wittgenstein's contention that philosophy leaves everything as it is can be recast as the claim that: those who engage in intense philosophical opposition nonetheless agree with one another in their unreflective practice. Philosophy's leaving everything as it is just does not preclude it from changing opinions, but refers only to the fact that it need not and generally does not thereby modulate agreement in practice.

And who has ever really supposed that anyone can just enter into an area of scientific work and make an effective intervention? And who has suggested that any innovatory contribution has nothing whatever to do with the previously extant results of science? Who imagines that anyone can – and quite arbitrarily – put forward a new scientific paradigm and any old one that one is inclined to do, that one can just decide that’s how nature is? Everything that Kuhn says amounts to: natural science is anything but easy.

Of course, philosophy of science does make differences: we’d like our philosophical intervention to help put an end to a long and utterly futile dispute, we’d like people to see that the ‘science’ and ‘culture’ wars have been carried on by largely naked emperors, and that what people might have thought were reasons to e.g. devalue science or to take up arms against Realists are only bad reasons – just as are the reasons one has been given for sticking with the Realists. But even if our intervention were successful – dispelling a great cloud of philosophical confusion- our philosophy does not (or at least need not) have any direct ethical or political consequences. There are questions to be asked about the role of science in our society, the responsibility of scientists, and so on, but our philosophy cannot give answers to questions as to what, in these connections, anyone should do. Nor can it, but then, if our arguments are right, neither can any other philosophy honestly, responsibly and correctly answer these questions - for they are not philosophical questions. The fact that philosophers cannot tell you what to do should not stop anyone making up their minds on the important and pressing issues of the day – after all, in the contemporary cultural climate, philosophies are often chosen because they seem to be a crutch, a further support, for convictions you already hold [ philosophy the comfort blanket]. We are comfortable to hold our own convictions with whatever confidence – even certainty – we do without needing to garnish them with a further conviction: that what we think is not just right as we see it but is right because it is demonstrably in accord with the intrinsic nature of things.

It is an irony that we have sought to optimise the consistency of Kuhn’s thought in a way which, if accepted, would clearly deprive him of many of the characteristics that have won him his reputation and earned him his influence.
Thomas Kuhn's account of science definitely does not give most philosophers of science what they (think they) want from a philosophy of science. Kuhn, we have argued, neither provides a general and true theory of science, nor a set of normative prescriptions for how to pursue science correctly. That Kuhn does not do either of these can seem hugely disappointing, which is perhaps why friends and foes alike seek to read a theory and/or some prescriptions into his work.However, our inclination to 'deflate' Kuhn is not meant to diminish but to fortify his arguments. Kuhn's strength is in his 'negative' thinking. That Kuhn does not go for giving philosophers of science what they ask for is what we find more impressive in his work. Kuhn tries to get oneto rethink what the philosophy of science is, not to
manouevre within the space provided by the traditions of that discipline. It is this which makes him truly radical. Indeed - revolutionary.

Why do we praise Kuhn for 'negative' thinking? Lack of understanding is not necesssarily the same as ignorance, but is often the result of a lack of clarity in one's thought, and the lack of clarity can result from difficulties that one puts in one’s own way. One of the illusions which often has a strong hold on the mind is that the way to a better understanding is through the addition of further knowledge, but this is not always the case. Sometimes, the difficulty is not that we don't know enough, but that we don't properly appreciate what it is that we already know. In these cases, what is needed is to get a more perspicuous grasp on things we do already know, and a way of giving us a better view can be to rearrange the familiar facts. We have already drawn heavily on the following remark of Ludwig Wittgenstein's:
'Philosophy may in no way interfere with the actual use of language; it can in the end only describe it.

For it cannot give it any foundation either.
It leaves everything as it is.
It also leaves mathematics as it is..' (PI 124)

We would add that it leaves science as it is too, and that Kuhn has (largely) shown us how to see this. That is a (different kind of) ‘revolutionary’ achievement.

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