Brit. J. Phil. Set. aa (1971), 287-306 Printed in Great Britain 287 Review Articles KUHN*S SECOND THOUGHTS THOMAS KUHN'S Structure of Scientific Revolutions is a justly famous book, and one which has caused quite a stir among philosophers of science since its first publication in 1962. In this second edition 1 Kuhn happily makes only two changes in the original, already classic text. But he adds a 36-page 'Postscript 1969', in which he responds to his many critics and indicates how his views have developed. 2 The discussion in this Postscript centres around Kuhn's two basic ideas the idea of paradigms as the basis of scientific research, and the idea of scientific communities as the units responsible for paradigm-based research. Let us consider "communities" first, since Kuhn himself begins with them. He is worried about the circularity involved in defining a paradigm as that which the members of a scientific group share, and then defining the group by its shared paradigm. Now most philosophers of science, if they paid any attention at all to the sociological dimension of science, would presumably have a ready solution to this Kuhnian puzzle. They would insist that the content of science is primary, so that if scientists do organise themselves into different groups this must be a sociological reflection of their different problems, theories and techniques. Such philosophers of science would, therefore, define the group by the common scientific content of its activities, and not vice versa.' Kuhn flirts with a different solution to his puzzle: "Scientific communities", he says, "can and should be isolated without prior recourse to paradigms; the latter can then be discovered by scrutinising the behaviour of a given community's members" (p. 176; also his (197c*), p. 271). Does this mean that the membership of a scientific group is somehow to be determined independently of the scientific content of its activities? This would indeed be "an inversion of our normal view of the relation between scientific activity and the community that practices it" (p. 162). How could such a thing be done? At this point Kuhn assures us that the isolation of scientific communities "has recently become a significant subject for sociological research" and refers us to this research (p. 176; also his (19706), p. 252). Perusal of this literature will reveal that most sociologists solve the problem of isolating scientific communities by somehow taking the word of scientists themselves. Thus Price and Beaver investigate a group the members of which receive membership lists, preprints and other memos what they call the "basic difficulty of study" is solved for 1 Thomas S. Kuhn (1970), The Structure of Scientific Revolution! (International Encyclopedia of Unified Science, vol. II, no. a), 2nd ed. ( enlarged, pp. xii+210. Chicago and London: The University of Chicago Press. $1.50 (paperback). 1 There are considerable overlaps between this Postscript and Kuhn's (19706) and (1971a) cited in the bibliography; I shall refer to all three. * Thus they would apply some 'internal-external' distinction and regard internal history as primary and external history as secondary. Cf. especially Lakatos (1071); and also Kuhn (19716)
288 Alan E. Musgrave them by the scientists who organised themselves into this group ((1966), p. 1011). Diana Crane locates the members of her group by taking all the names listed by the compiler of a bibliography ((1969) p. 338). Other 'methods' do exist, however they involve sorting scientists into groups by inspecting footnotes in scientific papers, and seeing who cites whom. 1 The sociologists to whom Kuhn refers us take pride in what they call the "objectivity" of their methods. What they mean is that their methods can be applied without taking any notice of the scientific content of the activities investigated. Kessler emphasises that his method "Even when performed by a human being... is completely mechanical" ((1965), p. 224). The results achieved using the Scientific Citation Index (a list of who cites whom prepared by a computer) are "based on a purely objective method which does not require a personality appraisal or a reading of the works by these men". 2 Price and Beaver complain that there has never been "an objective analysis of an Invisible College structure" and proceed to provide one, making it clear that "we have been at pains to preserve our primitive ignorance of the scientific content of the work of this group and also our lack of any personal knowledge of the participants in it" ((1966), p. ion). These sociologists of science take pride, then, in their curious "objectivity", that is, in paving no attention to the scientific content of the activities of the scientists they study. So the question recurs: does Kuhn propose to isolate the members of his scientific groups without taking into account their scientific activities? The answer, not unexpectedly, is "No". His own summary of the distinguishing marks of members of a group is as follows: having "undergone similar educations and professional initiations", having "absorbed the same technical literature" so that a community has "a subject-matter of its own", and finally having their "professional judgement relatively unanimous" (p. 177; also his (1970A), p. 253). But the sociological methods to which Kuhn himself had referred can hardly be relied upon to isolate groups in this sense. Clearly, for example, the fact that one scientist cites another hardly guarantees that they share a subject-matter (he might, after all, cite him in distinguishing their subject-matters), or that their "professional judgement" coincides (he might, after all, cite him in disagreement). Citations, not to mention the papers containing them, will have to be read and understood to see if they provide evidence of common group membership in Kuhn's sense. But Kuhn's sociologists, as we have seen, appear to have a methodological aversion to reading what they so assiduously count, and therefore cannot solve Kuhn's problem. 8 It seems that Kuhn's own sociological citations should be taken with a pinch of salt. 1 The "method of bibliographic coupling" (Kessler (1965)) is based on this technique. Kessler proposes it as a new method of compiling subject-indexes to journals. But it is worth noting that he tests its efficacy by comparing its results with those achieved by "traditional" methods, which do involve reading the papers to be classified into groups. * Garfield (1970), p. 671. The result achieved was to produce a list of the fifty most cited authors for 1967, two of whom got the Nobel prize in 1969 (they were listed in positions 6 and 41). This remit is described as "impressive" by its author. 1 I need hardly point out that their aversion is misguided, and that taking into account the content of citations, and of scientific activities in general, is a far from "subjective" method.
Kukn's Second Thoughts 289 But let us proceed, granting that communities in Kuhn's sense have, somehow, been isolated. They exist, he says, at "numerous levels" (p. 177), from the community of all scientists, to those of physicists, chemists, etc., then to subcommunities (e.g. solid-state physicists), and finally to sub-sub-communities. It is these last communities that Kuhn wants to concentrate upon: "Communities of this sort are the units that this book has presented as the producers and validators of scientific knowledge" (p. 178). They are relatively small, typically containing "perhaps one hundred members, occasionally significantly fewer" (p. 178; also his (19706), p. 253) elsewhere "fewer than twenty-five people" is mentioned (p. 181). Kuhn asserts that, with his new emphasis on the micro-community structure of science, "several difficulties which have been foci for critical attention are likely to vanish" (p. 180). Quite so. As we shall see, what vanishes is the conception of "normal science" which was originally attributed to Kuhn. According to this conception, the scientific community engages in "normal research" for relatively long periods between short bouts of "extraordinary research". During normal periods there is consensus on the guiding principles of research (the "paradigm"), a consensus reinforced by the dogmatic style of scientific education. Rival paradigms are not taught, their invention is discouraged, and controversy over fundamentals ceases. Instead, the scientific community concentrates on "puzzle-solving", on forcing nature to fit the paradigm to which it is committed. If nature is stubborn and a scientist fails to solve his puzzle, then he is blamed, not the paradigm. Only in "extraordinary" periods, when rival paradigms compete, do unsolved puzzles or "anomalies" turn into critical arguments against paradigms. But such periods are short-lived soon consensus emerges on a new paradigm, and the scientific community devotes itself once again to "normal science". This, roughly, is the conception of "normal science" to which Kuhn's critics took exception. They could not quite agree, as Kuhn indicates ((19706), p. 233), whether it is a bad thing which fortunately does not exist, or a bad thing which unfortunately does exist. What does emerge clearly from Kuhn's present writings is that it is a conception to which he does not now, and perhaps never did, subscribe. Several people criticised Kuhn for exaggerating the degree of consensus normally prevailing in the scientific community. Now although Kuhn still makes it a defining condition for a community that its members are agreed on something (I shall discuss presently exactly what this something is), this consensus condition becomes innocuous when the scientific community dissolves into numbers of micro-communities. Whole sciences need no longer be given over, for long periods, to the articulation of a single, universally accepted paradigm. Kuhn could allow for all the disagreement his critics wanted, by having his micro-communities compete with each other. But does Kuhn allow active competition between different groups? His general position is not unequivocal. On the one hand he says that "professional communication across group lines" is comparatively rare and "often arduous"; and he insists that "communities... which approach the same subject from incompatible viewpoints... are far rarer [in the sciences] than in other fields" (p. 177). On the other hand, he says that there are "such things
290 Alan E. Musgrave as schools in science, communities which approach the same subject from very different points of view" ((1970ft), p. 252); and he predicts that "Research would... disclose the existence of rival schools" ((1970ft), p. 253). x Kuhn's response to a particular example adduced by several of his critics is more enlightening. His critics claimed that there has been a continuing controversy over theories of matter in the history of physics. Kuhn agrees, but thinks it "no counterexample" to his idea of normal science being governed by consensus (p. 180; also his (1970ft), p. 255). He allows that different micro-communities quarrelled over theories of matter. And he even allows that members of the same community did so, citing the controversy over the existence of atoms in early nineteenth-century chemistry as example. These are significant remarks. According to Kuhn's Postscript fundamental metaphysical controversy, either between communities or even within the same community, can accompany "normal research". This takes us far from one of his original central theses (e.g. pp. n, 15) that in normal periods fundamental metaphysical controversy ceases. Kuhn still insists that the members of a community practising normal science "take the foundations of their field for granted" (p. 178; cp. p. 21). But now "foundations" need no longer include metaphysics so what does it include? According to Kuhn's Postscript, all that early nineteenth-century chemists needed to agree upon to remain in the same community were "research-tools" like the laws of constant and multiple proportions and combining weights. They could, and did, "disagree, sometimes vehemently, about the existence of atoms" (p. 180). Now this means that chemists could, and did, disagree vehemently about the explanation or interpretation of their "research-tools". Atomists like Dalton and Berzelius insisted that these "tools" made no sense unless seen as manifestations of the existence of atoms. And Dalton, as is well-known, refused to accept Gay-Lussac's law because he could not fit it into his atomist metaphysic. As we shall see, Kuhn does not favour a return to the positivist view that such metaphysical disputes have no real influence on the practice of science proper. And this has important repercussions on his view of the nature and functions of "paradigms". (One of Kuhn's changes in his original text tends in a similar direction. He originally suggested that Newton's Principia became the universally accepted paradigm in the eighteenth century. He now qualifies this picture of Newtonian dominance, albeit guardedly, by saying (pp. 30-3) that on the Continent different "techniques'' persisted for a long time in the analysis of terrestrial phenomena.) A further "difficulty" seized upon by Kuhn's critics also vanishes with his present emphasis on the micro-community structure of science. Some critics took Kuhn to assert that critical debate over paradigms was a comparatively rare phenomenon. And they argued, against this, that even in periods between 1 Current sociological research is not much help, however. Price and Beaver find that over half of those who helped produce the papers distributed in their "invisible college" were not themselves members of it ((1966, p. 1013). And Diana Crane finds that half the persons mentioned by members of her group as having "influenced" their work were not members of that group ((1969), p. 340). Such data might suggest that "professional communication across group lines" is not quite so arduous as Kuhn says it is. But data like this can tell us nothing about the presence or absence of critical debate between groups to find out anything about this, the content of scientific papers would have to be studied.
Kuhn's Second Thoughts 291 major scientific revolutions, much discussion and revision of theory takes place, albeit on a smaller scale. Kuhn agrees: a revolution "need not be a large change" (p. 181) "micro-revolutions", as Kuhn calls them ((19706), p. 249, note 3), "occur regularly" (p. 181) in the intervals between major revolutions. He adds (p. 181) that micro-revolutions need not be preceded by any "crisis" in the community they may, for example, be produced by developments in other communities (in such cases, presumably, communication between groups is not so "arduous" that it does not take place). In his second amendment to the original text, 1 Kuhn allows that a state of crisis need not end with the revolutionary overthrow of the existing paradigm: it may be brought to an end with the solution of the "crisis-provoking problem" on the basis of the existing paradigm, or by temporarily shelving the problem. This amendment is also significant. Any anomaly can, it appears, produce a "crisis" and be seen, by one, some or all members of the relevant community, as "the end of an existing paradigm" (p. 84; also his (19706), p. 249). Kuhn's "normal periods" were, it now appears, misconstrued as dogmatic interludes between crises actually they are full of crises of their own. And paradigms were, it now appears, misconstrued as the unquestioned basis of normal science actually they are continually brought into question by anomalies. (I shall later consider how these revelations bear on Kuhn's description of normal research as ' 'puzzle-solving''.) Kuhn's present view of "normal science" will, it seems to me, cause scarcely a flutter among those who reacted violently against what they saw, or thought they saw, in his first edition. Yet one essential feature of it remains: Kuhn still insists that normal research in each of his micro-communities is based upon consensus about paradigms. Now we have already seen that this consensus need not extend to metaphysics. So what are the paradigms, consensus upon which remains a pre-requisite for normal research? This brings me to the second major topic of Kuhn's recent writings. Kuhn's critics pointed out that he used the term "paradigm" in several different ways. Kuhn agrees, and now distinguishes two fundamentally different senses of the term. In the first sense, paradigms are what we will find "by examining the behaviour of the members of a previously determined scientific community" (p. 175). Since for Kuhn the community will have been "previously determined" by sociological methods, he calls this the sociological sense of the term "paradigm". A paradigm in this sense is "the entire constellation of beliefs, values, techniques, and so on shared by the members of a given community" (p. 175). Kuhn now proposes to call it a "disciplinary matrix" instead of a paradigm. But how seriously are we to take this specification of a disciplinary matrix as the entire constellation of shared beliefs, values and techniques? What if sociological investigation yields a group whose members happen to share beliefs about the Trinity, values about drug-taking, and techniques of lovemaking? Such shared elements will not, clearly, figure in their "disciplinary matrix". The point is not entirely frivolous. Members of a sociologicallydetermined group may share many elements which are irrelevant to their 1 It affects page 84, and brings it into line with what Kuhn wrote in his (1961), p. 179.
292 Alan E. Musgrave scientific work. And conversely, they may fail to share elements which are scientifically relevant. Clearly, we shall have to employ a philosophical thesis to demarcate between what is relevant to scientific work and what not. Kuhn himself lists four typical components of a disciplinary matrix or paradigm in the sociological sense (the last component turns out, rather confusingly, to be paradigms in Kuhn's second major sense of the term). First, there are "symbolic generalisations" like / = ma. Kuhn makes two excellent points about these. The first, not new, is that they can function partly as laws and partly as definitions of their symbols, that scientific practice depends greatly on which function they are performing, and that the balance between these functions often changes over time. The second point is that symbolic generalisations are often better regarded as law-sketches rather than laws, for they yield very different laws as they are applied to different types of situation. The second component of Kuhn's disciplinary matrices are metaphysical beliefs like those in atoms, or in fields of force, or in heat as a substance, or in heat as a mode of motion. These were previously called metaphysical paradigms (e.g. p. 41). They play an important role in scientific work, for they "supply the group with preferred or permissible analogies and metaphors... help to determine what will be accepted as an explanation and as a puzzle-solution... [and] assist in the determination of the roster of unsolved puzzles and in the evaluation of the importance of each" (p. 184). And yet, as we already saw with atomism, Kuhn no longer insists that metaphysical beliefs be shared by all members of a given group. This means that the "normal scientific" work of a group can contain disagreement about the interpretation of their results, about whether a proposed explanation or "puzzle-solution" is adequate, and about whether an unsolved problem is a significant one or not. Previously, Kuhn suggested that such disagreements. were eliminated from normal science by consensus over "metaphysical paradigms" (e.g. pp. 18, 48). The third component of Kuhn's disciplinary matrices are values to be attached to theories, like consistency or the ability to yield precise predictions and to suggest fertile problems. He remarks that values are "more widely shared among different communities" than the other components of disciplinary matrices (p. 184). This is, of course, significant for the analysis of competition between communities, when scientists must "choose between incompatible ways of practising their discipline" (p. 185). But before turning to the problem of theory-choice, and to the famous "incommensurability thesis", I shall consider the fourth component of Kuhn's disciplinary matrices. These are "concrete puzzle-solutions... employed as models or examples" (p. 175). They provide Kuhn's second major sense of the term "paradigm", which is philosophically "the deeper of the two" (p. 175). He now calls them "exemplars" instead of paradigms, and says that they are "the most novel and least understood aspect of this book" (p. 187). It is the common possession of different sets of exemplars which does most to determine the "community fine-structure of science" (p. 187). Exemplars figure essentially, first of all, in scientific education. Textbooks confront the student with exemplary problem-solutions, and invite him to work out similar problems for himself. A typical group of problems will involve the application of the same symbolic generalisations to different types of situation.
Kuhn's Second Thoughts 293 And in acquiring from exemplars the ability to solve problems, the student simultaneously learns about the content of physical theory and about the world to which it applies. This is an excellent description of, and partial justification for, the practice of including problems in science textbooks. But for Kuhn its significance does not stop there. "Scientists", he says, "solve puzzles by modelling them on previous puzzle solutions" (p. 189). Kuhn's description of normal scientific research as "puzzle-solving" stems from an analogy with textbook education: what the working scientist does is basically the same as what the student does. But is the analogy entirely appropriate? A crossword puzzle has an assured solution, and challenges the ingenuity of its solver. This is why Kuhn adopts the term: "I use the term 'puzzle' in order to emphasize that the difficulties which ordinarily confront even the very best scientists are, like crossword puzzles or chess puzzles, challenges only to his ingenuity. He is in difficulty, not current theory." ((1970a), p. 5, note 1). Now the textbook problems faced by students might with justice be called "puzzles": there is an assured solution known to their compiler (unsolved problems do not figure in textbooks); it is the student who is in difficulty, not current theory; hence, if he fails to solve a problem, he is blamed and not his theoretical tools. But is scientific research like this? Is it really the case that normally, when a working scientist fails to solve his problem, "the practitioner is blamed, not his tools" ((1970a), p. 7)? Kuhn can hardly continue to maintain this for he now allows, as we have already seen, that any unsolved puzzle or anomaly can be seen as "the end of an existing paradigm". Moreover, Kuhn now thinks it desirable that some scientists do react in just this way, and blame anomalies on the "tools" and not on the practitioner if they did not "there would be few or no revolutions" (p. 186). But such reactions are only possible, after all, because the mature scientist, unlike the science student, works on a problem which, unlike a puzzle, has no assured solution. It is always an open question whether the working scientist can model a satisfactory solution to his problem on previously obtained exemplary solutions to other problems. It seems to me, therefore, that "puzzle-solving" should disappear, and "problemsolving" resume its place, as the most adequate description of scientific research. At all events, the focus of Kuhn's present interest in paradigms as exemplary problem-solutions is different. He is interested in the sort of knowledge one acquires from them, "the ability to recognise a given situation as like some but unlike others one has seen before" (p. 192), and in its repercussions on the problem of perception. The days of "sense-data" are long past. Nowadays we all agree that a great deal goes on (Kuhn calls it "neural programming") between the stimuli impinging upon us and our actual sensations. But Kuhn objects to describing this "programming" as a process, even an unconscious process, of interpreting stimuli in the light of rules or generalisations. For we cannot experiment with different ways of having a sensation, as we can with different ways of interpreting a sensation once we have had it (p. 194). Kuhn insists, therefore, that the ability, acquired from exemplars, to "programme" a stimulus in a certain way cannot be inculcated by learning explicit rules, and is "misconstrued" if reconstructed in terms of such rules (p. 192). It represents "tacit
294 Alan E. Musgrave knowledge" in Polanyi's sense (p. 191). Kuhn answers the charge that such "knowing" is unanalysable and irrational by informing us that he is "currently experimenting with a computer program" which simulates it (pp. 191-2; also his (1971)). Kuhn's point emerges more clearly with his example. The layman confronted with a cloud-chamber will see water droplets he will need to interpret these as the track of a particle. The physicist, on the other hand, literally sees the track of a particle he only needs to interpret this track as signifying, say, the presence of an electron. The difference in the initial perceptions should not be ascribed, says Kuhn, to differences in the amount of unconscious interpretation which is taking place. For "interpretation begins where perception ends. The two processes are not the same, and what perception leaves for interpretation to complete depends drastically on the nature and amount of prior experience and training" (p. 198). What hinges on this rather subtle distinction? It enables Kuhn to mean it literally when he says that scientists imbued with different paradigms (now "exemplars") see the world differently. They do not, for Kuhn, see the same thing and merely interpret it differently. And this brings me to the problem of theory-choice and incommensurability. Some of Kuhn's critics took him to be claiming that the victory of one theory over another in a scientific revolution is not brought about by rational argument. Rational standards can play no role in theory-choice, since each theory itself sets different standards for science. The victory of the new theory is accomplished partly by irrational propaganda, which prods a few scientists into making the necessary "leap of faith", and partly by the demise through natural causes of the old-guard. Revolutionary change substitutes one way of viewing the world and of practising science in it for another one, incommensurable and not merely incompatible with the first. Hence science cannot be said to make progress through scientific revolutions unless we define "progress" as what the scientific community decides. Kuhn now makes it clear that he subscribes to none of these radical theses. On the problem of theory-choice his thesis is, he says, "a simple one, long familiar in philosophy of science" (p. 199). It is merely that scientists cannot prove that one theory is superior to another in such a way as to compel assent to it. Instead, they must employ rational persuasion, appealing in the process to those values "usually listed by philosophers of science: accuracy, simplicity, fruitfulness, and the Like" (p. 199). Kuhn does emphasise one point which most philosophers of science ignore: that scientists, while agreeing in general on what is to be valued, can quite genuinely disagree about their verdict in concrete cases. He suggests that this "individual variability in the application of shared values may serve functions essential to science". For it helps to ensure that no promising line of research is neglected, and thereby serves as the "community's way of distributing risk" (p. 186). For Kuhn, then, theory-choice is far from being an irrational affair indeed, he finds Feyerabend's defence of irrationalism "vaguely obscene" ((1970^), p. 264). He does accept some responsibility for his critics' misunderstanding him on this: "I now think it a weakness of my original text that so little attention is given to such values as internal and external consistency in considering
Kuhn't Second Thoughts 295 sources of crisis and factors in theory choice" (p. 185). Yet he insists, and here he convinces me at any rate, that it was a misunderstanding. What, then, of progress through revolutionary change? Kuhn allows this also. He claims that the value most often appealed to in comparing rival theories is their "demonstrated ability to set up and solve puzzles presented by nature" (p. 205). And he says that Newton's theory progresses beyond Aristotle's, and Einstein's beyond Newton's, as "instruments for puzzle-solving" (p. 206). Thus Kuhn is far from relativism, for there are theory-independent standards in the light of which a new theory may constitute progress over the old. What Kuhn still doubts is only whether progress in puzzle-solving, or rather problem-solving, ability constitutes "progress towards the truth", if we mean by this that Newton's ontology represents reality better than Aristotle's, or Einstein's better than Newton's. For in some respects, says Kuhn, Einstein's ontology marks a return to an Aristotelian ontology. Thus Kuhn sharply separates the empirical success of a theory from the verisimilitude or "truthlikeness" of its ontology. Here he differs from Popper. Notice, however, that they do not appear to differ on the criteria of empirical success: what Kuhn describes as a theory's "ability to set up and solve puzzles presented by nature", Popper describes as a theory's empirical content, its ability to provide analyses of a variety of physical situations (presented ideally by the theory itself, however, not "by nature"), and its corroboration, its predicting successfully what happens in those situations. Their difference is merely that Kuhn will not follow Popper in calling progress in content and corroboration an increase in verisimilitude. The main point, however, is that Kuhn does not, and never did, subscribe to that radical form of the "incommensurability thesis" which implies relativism. Incommensurability for him means only that those nourished on differing exemplars will see the world differently and will consequently often use the same term in different senses. Kuhn insists that the resulting difficulties of communication "cannot be resolved simply by stipulating the definitions of troublesome terms": this is so because these terms have been learned from exemplars, and the ability to apply them cannot be made explicit in the form of a definition or rule or criterion (p. 201). I must confess that I remain unconvinced by this, and especially by Kuhn's examples. One must admit, of course, that terms change their meanings with different theories, in the sense that, to use one of Kuhn's examples, a Copernican will class the earth as a planet while an Aristotelian will not. But I fail to see why, if this leads to a "communication problem", the Copernican cannot explain that on his theory the earth, since it revolves around the sun like the other planets, must be classed with them. I also fail to see why the Aristotelian cannot understand this, without of course necessarily accepting it or why he cannot make the Copernican understand his own reasons for classing the earth differently. 1 The same applies to Kuhn's other examples ("element", "mixture", "unconstrained motion"). What are the "exemplary problem-solutions" which, according to Kuhn, give scientists their tacit knowledge of the meanings of such words? Is not their meaning given instead by perfectly articulable theories? 1 Perhaps it is worth noting that neither needs recourse to a theoretically neutral observation language for at this stage of the discussion, adherents of incommensurability usually launch into a diatribe against that positivist daydream.
296 Alan E. Musgrave Not that too much hinges on all this. For Kuhn allows that when incommensurable concepts lead to "communication breakdown" there is a way out. The participants can "recognise each other as members of different language communities and then become translators" (p. 202). And having translated each other's theory, the participants can engage in rational persuasion. Kuhn's apparatus of "language communities" and "translation" may seem a heavy-handed way to describe what goes on when adherents of rival theories use a term or two differently and try to understand each other especially when Kuhn admits that they will share their everyday and most of their scientific language (p. 201). It is the linguistic parallel, however, which enables Kuhn to retain the last vestiges of one of his characteristic theses. In his first edition, Kuhn described the adoption of a new paradigm as a "conversion experience which cannot be forced" (p. 151) and which occurs "all at once" like the gestalt switch (p. 150). Critics took this to mean that theory-choice was an irrational leap-of-faith, an interpretation which Kuhn denies. But he does now say that we can be persuaded to adopt a theory without being converted to it: "The two experiences are not the same, an important distinction that I have only recently fully recognized" (p. 203). Kuhn derives this new subtlety from his linguistic parallel. In being persuaded to adopt a new theory, a scientist will usually have to translate that theory into his own language. However: "To translate a theory or worldview into one's own language is not to make it one's own. For that one must go native, discover that one is thinking and working in, not simply translating out of, a language that was previously foreign" (p. 204). Since "going native" happens all at once, and one cannot choose to do it, it has the features of a "conversion experience". Kuhn suggests that these conversion experiences come more easily to the young (thus elaborating the adage "You can't teach an old dog new tricks"), and that without such an experience a scientist will be unable to do effective work even with a theory to which he might be fully persuaded. Therefore, he claims, such experiences remain "at the heart of the revolutionary process" (p. 204). This is all that remains of the idea that the adoption of a new theory incommensurable with the old is accomplished by "community conversion". Incommensurability has ceased to be a logical affair, and conversion has become a purely psychological, as opposed even to a socio-psychological, matter. Again, this present view will hardly upset those who objected to what they saw, or thought they saw, in Kuhn's first edition. In his recent writings, then, Kuhn disowns most of the challenging ideas ascribed to him by his critics. I suppose one should not complain of this, especially when Kuhn's "I never said it" ploy often convinces. His original text really does not contain some, at least, of the revolutionary views which so disturbed his critics (in particular the views that theory-choice is irrational and that progress through scientific revolutions is a myth). But I shall not substantiate this with textual analyses, since this review is already overly long. Instead, I shall end by confessing that Kuhn's Postscript left me feeling a little disappointed. I find the new, more real Kuhn who emerges in it but a pale reflection of the old, revolutionary Kuhn. Perhaps this revolutionary Kuhn never really existed but then it was necessary to invent him (since Feyerabend
Newtonianism in the Eighteenth Century 297 gives substance only to some of his parts). It is true that Kuhn continues to emphasise the importance of the social dimension of science. His Postscript ends as it began, by exhorting us to pay heed to the "community structure of science", and to compare it with the community structure of other disciplines. Such exhortations had to be taken seriously when they were accompanied by the claim that by following them we would overthrow many of our cherished ideas about the nature of science. But now, it seems, following them will merely acquaint us with rather humdrum sociological aspects of what many of us already thought takes place. Sociological puzzle-solving will not be subversive of our basic philosophical commitments. And with luck, philosophers of science can still decline the invitation to indulge in it without being "read out of the profession". REFERENCES ALAN E. MUSGRAVE University of Otago CRAKE, D. (1969) Social Structure in a Group of Scientists: A Test of the 'Invisible College' Hypothesis. American Sociological Review, 34, 335-52. GARFIELD, E. (1970) Citation Indexing for Studying Science. Nature, 337, August 15, 669-7i- KFSSI.FR, M. M. (1965) Comparison of the Results of Bibliographic Coupling and Analytic Subject Indexing. American Documentation, 16, 223-33. KUHN, T. S. (1961) The Function of Measurement in Modern Physical Science. Itit, 53, 161-93. KUHN, T. S. (1970a) Logic of Discovery or Psychology of Research. Criticism and the Growth of Knowledge. Eds. I. Lakatos and A. Musgrave. London and New York: Cambridge University Press. KUHN, T. S. (19706) Reflections on My Critics. Ibid. KUHN, T. S. (1971a) Second Thoughts on Paradigms. The Structure of Scientific Theories. Ed. F. Suppe. Urbana: Illinois University Press. KUHN, T. S. (19716) Notes on Lakatos. Boston Studies in the Philosophy of Science. Eds. R. Buck and R. S. Cohen. Dordrecht: D. Reidel Publishing Company. LAKATOS, I. (1971) History of Science and its Rational Reconstructions. Boston Studies in the Philosophy of Science, Vol. 8. Eds. R. Buck and R. S. Cohen. Dordrecht: D. Reidel Publishing Company. PRICE, D. J. and BEAVER, D. de B. (1966) Collaboration in an Invisible College. American Psychologist, 31, 1011-18. NEWTONIANISM IN THE EIGHTEENTH CENTURY IT IS maintained in each of two recent scholarly monographs 1 that one can understand the entire development of science in the eighteenth century in the framework of the struggle between Newtonianism and its critics. Both works 1 Robert E. Schofield, Mechanism and Materialism: British Natural Philosophy in the Age of Reason, Princeton and London: Princeton University Press (1970). 4.50 (90s.), pp. vii+336. Arnold Thackray, Atoms and Powers: An Essay on Newtonian Matter- Theory and the Development of Chemistry. Cambridge, Mass, and London: Harvard University Press (1970). 4.20 (84s.), pp. xxiii+326.