B. I. B. LINDAHL Department of Geriatric Medicine, Karolinska Institute, Huddinge University Hospital, S-141 86 Huddinge, Sweden

The theme of this issue of Theoretical Medicine focuses on a few of the many mechanisms governing the evolution of science. The five articles within this theme deal with both internal research methodological factors, regulating directly the evolution of scientific knowledge, and external, social factors, regulating the constitution and performance of the research community. Among the former factors are the principles for hypothesis testing and theory change. Among the latter are the methods for measuring researchers' impact in science and criteria for judging the impact of scientific discoveries. (These latter methods and criteria function both as instruments for studying the evolution of science and as factors influencing the pace and direction of science.) The Nobel prize in physiology or medicine has been chosen as a paradigmatic example of both how the importance of scientific discoveries may be evaluated and what influence such an evaluation may have on the evolution of scientific knowledge. All five papers deal directly or indirectly with factors influencing the selection of Nobel prize winners or with the effects on science of the Nobel prize. The interaction between internal and external factors in science, highlighted by the papers in this issue of Theoretical Medicine, is often overlooked in the study of scientific evolution. Philosophers tend to restrict the interest in the theory of science to the internal questions, while leaving the external to the history and sociology of science, and other empirical disciplines. Carried to extremes this way of working would be somewhat like studying biological evolution only from the point of view of molecular biology, without regard to findings and theories on more complex levels of organization - like those of cellbiology, embryology, population genetics and sociobiology - and without a longer historical perspective - like that of paleontology. In order to further emphasize this point, I will make a few remarks about the analogy between the evolution of science and the evolution of nature, before presenting and commenting on the articles of this issue.

Theoretical Medicine 13" 97-116, 1992. © 1992Kluwer Academic Publishers. Printed in the Netherland.~.



There are striking similarities between the evolution of science and the evolution of nature. These are clearly evident in the accounts of the evolution of scientific knowledge given by modem philosophy of science. For example, Karl Popper uses directly the terms of biology on the evolution of theories: We choose the theory which best holds its own in competition with other theories; the one which, by natural selection, proves itself the fittest to survive ([ 1], p. 108). Popper could even be said to deal with the question of adaptation, as a strategy for survival. His 'theory of evolution' leaves only minimal, if any, space for this means of survival. An adjustment of the theory, which would make it less vulnerable, would amount to 'adhocness', the opposite of 'boldness', and would therefore mean a setback for the evolution. If the individual does not fit the environment - if there are discrepancies between the theory and the experimental results - then the individual/the theory is doomed to destruction, according to Popper. (This strong interpretation of Popper's theory has been made by, among others, Imre Lakatos.) 1 Less literally, but in a similar way, one may see parallels between biological evolution and Thomas Kuhn's theory of the evolution of scientific knowledge. Kuhn refers explicitly to this parallel when discussing whether or not science evolves towards a goal ([3], pp. 170-173). He retums to this analogy also in a later essay and points out that "my view of scientific development is fundamentally evolutionary", and adds that "scientific development is, like biological evolution, undirectional and irreversible" ([4], p. 264). Unlike Popper, Kuhn does not apply the biological concepts literally. Neither does he argue explicitly that the parallel includes his view on the selection process itself. But there are close similarities nonetheless. Just as biology views the evolution of nature to be regulated through an interplay between heredity, environmental influence and adaptation, Kuhn views the evolution of scientific knowledge as an interplay between paradigm, facts, and ad hoc modification. Compared with Popper's 'theory of evolution' Kuhn's can be said to allow a wider scope for the individual's adaptation. Like the evolution of nature, the evolution of scientific knowledge, according to Kuhn, amounts to a change not only in the individual (the theory) but also in the control mechanisms. A discrepancy between a theory and the observed facts, therefore, need not always lead to rejection of the theory. The discrepancy may be evaded, at least for the time being, through ad hoc modification. The problems that the discrepancy between theory and observed facts give rise to does not necessarily mean a setback for the evolutionary process, according to Kuhn; they may even be driving forces of the evolution: ... anomalous experiences may not be identified with falsifying ones. Indeed, I doubt that



the latter exist ... On the contrary, it is just the incompleteness and imperfection of the existing data-theory fit that, at any time, define many of the puzzles that characterize normal science ([3], p. 146). The difference between Popper's and Kuhn's theories of scientific evolution lies in the fact that Popper essentially views the evolution of science as a piecemeal engineering process, whereas Kuhn sees it as both a gradual process of 'normal or paradigm-based research', consisting in 'puzzle-solving', and as a series of leaps and bounds, i.e. 'revolutions'. In the light of the way Popper and Kuhn explain the evolution of scientific knowledge, it may be tempting to try to view the evolution of science as a whole as a system of several simultaneous ecological processes, in which the evolution of knowledge is, so to speak, the core (equivalent to the change in genetic material in nature), a subprocess contained in a larger social process of evolution. Seen in this way, one might say that science, like nature, evolves at all levels through a perpetual selection of the fittest individuals; in science, the fittest vehicles of knowledge. In his book The Selfish Gene Richard Dawkins develops a view on the evolution of human culture along these lines [5]. Although he does not go as far as developing, what could be called, an 'ecological' view of science, his way of reasoning provides an interesting point of departure for an elaboration of such an idea. Dawkins introduces the concept ' m e m e ' for an idea propagating in the human culture like genes in nature. 2 The 'memes' in Dawkins analogy are the 'replicators' and the scientists the 'vehicles' of the memes. 3 One could of course also think of other 'vehicles' in science, e.g. journals, articles, and other carriers of scientific knowledge. (Incidentally, this also gives an interesting new meaning to Suppe's introductory remark that "theories are the vehicle of scientific knowledge" ([6], p. 3).) Though there are always dangers in using analogies, the parallel between the evolution of nature and of science seems to have a great potential heuristic value. It is therefore not surprising, as Stephen Toulmin points out, that the attempts to use this analogy go as far back as to Darwin's own time ([7], ch. 5). The analogy between science and nature may help us see that similar questions can be raised concerning the evolution of science as philosophers have begun to raise more systematicly concerning the evolution of nature. 4 For example: How shall the selection mechanisms be understood? What is meant by 'fitness'? What scientific value do theories about the individuals' (the vehicles') success in evolution have? Is it possible to predict a particular vehicle's success with the help of existing theories? What is meant by 'evolution'? Is evolution progressive or should these concepts, 'evolution' and 'progress', be kept apart? How shall the concept 'vehicle' be defined? To raise philosophical questions in this way about the evolution of science as a whole would be to study central issues in science of science in a way



philosophers have come to analyse the foundations of biology in what is called philosophy of biology. Just as the biological sciences cannot replace, but do enhance, the philosophical study of the evolution of nature, disciplines like information science, history of science and ideas, and sociology of science provide opportunities for a fuller philosophical understanding of the evolution of scientific knowledge. The five articles of this issue of Theoretical Medicine deal with both levels. They partly analyse different aspects of the evolutionary process itself, and partly reflect upon this analysis. THE PROPAGATION AND IMPACT OF SCIENTIFIC KNOWLEDGE Eugene Garfield and Alfred Welljams-Dorof discuss citation frequency as a measure of researchers' impact in science. They review previous studies of most-cited authors, discuss methodological problems in using data on citation frequency, and comment on the possibility to forecasting Nobel prize winners only on the basis of citation data. In their review Garfield and Welljams-Dorof point out that high rankings by citation frequency are strongly correlated with Nobel prize authors: "In the highest percentile, e.g. the top 0.1% of authors, a significant percentage have won the Nobel prize or go on to win the prize in later years". It is, as Garfield and Welljams-Dorof point out, remarkable that this single and comparatively simple method manages so well to catch both present and future Nobel laureates. Since Garfield founded the Institute for Scientific Information in 1960, with its variety of information services, among others the Science Citation Index, 5 citation frequency has become a widely used means of measuring the impact of authors, journals, and individual articles in science. As Garfield and WelljamsDorof point out, researchers are ranked according to their productivity (articles per author), author impact (citations per author), and article impact (citations per paper). Partly as a consequence of this practice, authors often consider the citation frequency of journals when publishing their papers. Though the use of citation frequency data has great advantages, not least due to its reliability,6 it is also a complicated indicator whose appropriate use requires careful interpretation. Garfield and Welljams-Dorof discuss several important factors to consider: the size of the field or specialty in which the author works; type of articles cited, e.g. empirical or method papers; the 'obliteration by incorporation' phenomenon; premature and post-mature discovery. In a previous article, Garfield calls attention also to other factors: citation traditions; problems of defining the field of research; and the aptitude of conveying results [13]. In addition there are also the most commonly recognized phenomena of self-citation and multiple authors.



Ultimately the question of validity is of course determined by how narrowly one defines that which one intends to measure, in this case the 'impact' of new knowledge on the evolution of science. This conceptual problem is something that Garfield and Welljams-Dorof do not go into, though they provide an interesting clue to it by way of introduction. To analyse philosophically the concept of impact and try to determine which role this impact plays in science is beyond the scope of Garfield's and Welljams-Dorof's paper. It is, however, an important issue to address in the philosophical study of the science of science. It is hardly likely that anyone would claim that high citation frequency in general, without further qualification, is a sign of scientific impact. Otherwise, it would not be necessary to take into account such factors as whether the citation is made inside or outside the author's field of research, or what kind of article it is that is cited, and several of the other problems Garfield and Welljams-Dorof discuss. Scientific impact presupposes an influence on the theory change. At the beginning of their paper Garfield and Welljams-Dorof say, as an explanation of why high citation frequency is correlated with Nobel prize winners, both present and future, that their papers ought to be "seminal and more influential" than the average. It is probably not accidental that Garfield and WeUjams-Dorof here distinguish between 'seminal' and 'influential'. There may in fact be a great point in this. (Note also that papers by Nobel prize winners are assumed to be both seminal and more influential than the average.) Dawkins points out that the fecundity, and consequently also the survival value, of a scientific idea may be measured "by counting the number of times it is referred to in successive years in scientific journals" ([5], p. 194). But if 'degree of scientific impact', which is what Garfield and Welljams-Dorof intend to measure, should not become synonymous with 'citation frequency', then, to use again the biological analogy, mere 'propagation' must be distinguished from actual 'mutation events'. Because, in fact, scientific ideas may very well continue to propagate, and through that survive within a research field, without contributing to the evolution of scientific knowledge within this field. Trivial examples are the use of out of date sources within research that has not succeeded in reaching the front line, or the references, in historical reviews, to classical works on theories abandoned long ago. But even when continued propagation is a sign of the ideas contributing to theory change, this contribution may be achieved in two very different ways: as Kuhn has taught us, either through being a part of the prevailing paradigms, 7 or through influencing and changing these presuppositions. The first may then even have a retarding effect on the evolution, whereas the latter more clearly accelerates it. Both lead to high citation scores. To analyse citation data is basically a matter of detecting the different reasons



for papers being cited. As Garfield points out: A 'method' paper ordinarily is cited for a different 'reason' than a theoretical work like that of Onsager on order-disorder, or that of Einstein on the stimulated emission of radiation ... In the one case, the impact may be immediate and practical, even 'economic'; in the other, the impact may be intellectually, at least, more far-reaching ([15], p. 280). It must also be taken into account that papers may not always be cited for the purpose they have been written. Papers need not even always be cited for their scientific qualities. But, despite all these methodological problems, does not the strong correlation between high citation frequency and a universally recognized and undisputed sign of scientific excellence, the Nobel prize, convincingly testify to the high validity of this measure of researchers' impact in science? This question brings us to the last issue of Garfield's and Welljams-Dorof's paper: the possibility of forecasting Nobel prize winners only on the basis of citation data. Despite the strong correlation between high ranking by citation frequency and Nobel prize authors, shown in Garfield's and Welljams-Dorof's review, citation frequency has (not surprisingly) proved to have a low predictive value for Nobel awards. Garfield has already in an earlier paper pointed out that citation analysis cannot predict individual Nobel prize winners: So even though we may compile for each and every major discipline and subspecialty a list of people who may be of Nobel class, there is no definitive way to determine who will win the Nobel prizes next year or the year after. But, as it turns out, our lists do anticipate most of the people who eventually do win Nobel prizes ([16], p. 610). According to a study by Garfield in 1973 [17], the change of winning the Nobel prize if one is among the authors cited more than 1000 times during the past 12 years is 0,4%. I f one is among the 50 most cited in this group, the chance is 1,9%. 8 The reasons for these low predictive values is of course the fact that there are so many other researchers with the same or even higher citation score as the Nobel prize winners. Or, to use Garfield's and Welljams-Dorof's concept, the pool of authors ' o f Nobel class' is so great compared to the few who actually win the prize. What then distinguishes the works of Nobel prize winners from the works of others ' o f Nobel class'? How have Nobel prize winners been selected? What criteria of scientific excellence can be discerned? These are questions Franz Luttenberger addresses in his paper. THE SELECTION OF NOBEL PRIZE WINNERS Franz Luttenberger examines the basis for the Nobel prize in physiology or medicine to Paul Ehrlich 1908. Ehrlich shared the prize with Elie Metchnikoff for their work on immunity. The principal issue of the paper is the Nobel



Committee's evaluation of the importance of Ehrlich work. In connection with this Luttenberger comments on the initial problems of interpretation in the execution of Nobel's will and accounts for the development of statutes and a formal organization for awarding the prize in physiology or medicine. He shows how two of the main criteria in Nobel's will, the importance and recency of the discovery, were applied in practice. He makes clear that also other considerations than purely scientific, such as geographical distribution and the striving for consensus, influenced the deliberations and decisions to award the Nobel prize at this time. Of principal philosophy of science interest is the significance that Luttenberger shows the difference in scientific style had for the evaluation of the scientific value of Ehrlich's work. As appears from Luttenberger's analysis of the arguments for and against a prize to Ehrlich, the chief opponent, Svante Arrhenius, as well as, through him, Johan Erik Johansson in the Nobel Committee, had a different theoretical approach than Ehrlich to the chemical interpretation of the immune reaction. As Luttenberger points out, Ehflich's professional background was in organic and structural chemistry and he consequently focused on the molecular structure of the immune reactants; whereas Arrhenius had his training in physics, mathematics and chemistry and concentrated on the reactant's physical properties. These differences could have stopped at being only a form of 'division of labour' in the immunological science if it had not been for the fact that they considered themselves dealing with, in some sense, the same problem and that they (especially Arrhenius) could only accept one of the views being correct. Their different points of departure and ways of approaching the immunochemical problem coloured their views of what was a proper way to study the immune response, an appropriate way of interpreting the immunological facts, and ultimately what constituted good science. This controversy about the scientific value of Ehrlich's work clearly illustrates Kuhn's point that the success and impact of a theory depends on the paradigm 9 of 'normal science' in the particular scientific community in question and at the specific time in history. In this controversy between Ehrlich and Arrhenius it was a matter of the prevailing ideas and models, the paradigms, of two different scientific communities at the same time in history. (Yet it was not necessarily an example of 'extraordinary science', in Kuhn's sense. As Luttenberger points out, Ehrlich was even open to the idea of combining the two views.) The controversy was basically a matter of competition between two fields of chemistry, the biological and the physical. Kuhn's theory about the influence of paradigms on the success and impact of theories in the history of science is of general interest when discussing the Nobel



prize. According to Kuhn, since the paradigm(s) of a scientific discipline change(s) with time, so also the conditions for evaluating the importance of different contributions to this discipline will vary [3]. This is perhaps not so difficult to accept. (Especially not since Kuhn's theory of science, as we will see, is not completely relativistic. It is still possible to compare theories from different periods of evolution.) What is possibly more controversial, especially in the context of Nobel prizes, are the conclusions Kuhn draws from his theory of scientific evolution through paradigm shifts, concerning the possibility of discerning individual discoveries and determining their influence on the evolution of scientific knowledge. The idea that it would be possible to discern individual discoveries that have influenced science in a decisive and lasting way, and that are sharply marked off in time and each of them attributable to a single scientist, is, according to Kuhn, associated with the view that scientific knowledge evolves by accretion; a view abandoned by modem historians: In recent years ... a few historians of science have been finding it more and more difficult to fulfil the functions that the concept of development-by-accumulation assigns to them. As chroniclers of an incremental process, they discover that additional research makes it harder, not easier, to answer questions like: When was oxygen discovered? Who first conceived of energy conservation? Increasingly, a few of them suspect that these are simply the wrong sorts of questions to ask. Perhaps science does not develop by the accumulation of individual discoveries and inventions ([3], p. 2). 10 Kuhn's critique is based on his well known theory that scientific knowledge evolves through revolutions. What has characterized the major turning points in the history of science, according to Kuhn, has been that the assimilation of the new theory required "the reconstruction of prior theory and the re-evaluation of prior fact, an intrinsically revolutionary process that is seldom completed by a single man and never overnight" ([3], p. 7). Considering the fact that the basic idea of the Nobel prize, according to Nobel's will, is to award important individual discoveries (and inventions, but not in Kuhn's sense of the term ll) and considering also the fact that the Nobel Committee, now for 90 years, has been successful (in some sense) in discerning individual discoveries and evaluating their importance, Kuhn's critical remarks give topical interest to several questions concerning the basis of the Nobel prize. Four questions are of particular interest: (1) What concept(s) of discovery has (have) the Nobel Committee applied? (2) Which criteria have the Nobel Committee used when selecting 'the most important discovery' within the domain of physiology or medicine? (3) If the Nobel Committee's evaluations of individual discoveries did not presuppose 'the concept of development-byaccumulation', on what view(s) of scientific change(s) was (were) they based? (4) Which role(s), if any, did past and present paradigms, in Kuhn's sense, 12 play in the Nobel Committee's evaluation of discoveries?



Without relating his analysis to Kuhn's theory of science, Luttenberger deals directly with the first two questions and, partly as a consequence of that, also indirectly sheds light upon the latter two issues. 1. A part of the explanation of why Kuhn finds it questionable and hardly feasible to try to discern individual discoveries, sharply marked off in time and each attributable to a single scientist, lies in the fact that his concept 'discovery' is quite inclusive. It comprises the whole process from (i) "the awareness of anomaly", through (ii) "a more or less extended exploration of the area of anomaly", and ending in (iii) the adjustment or change of paradigm ([3], pp. 52-53; cf. p. 62). The last stage, (iii), appears to comprise also the construction ('invention') of theory) 3 This seems to be exactly Kuhn's point, that discovery involves not only observation of fact but also the conceptualization of theory. Kuhn takes the discovery of oxygen as an example: Though undoubtedly correct, the sentence, 'Oxygen was discovered', misleads by suggesting that discovering something is a single simple act assimilable to our usual (and also questionable) concept of seeing. That is why we so readily assume that discovering, like seeing or touching, should be unequivocally attributable to an individual and to a moment in time ([3], p. 55). Luttenberger interprets the Nobel Committee as defining 'discovery' as "the detection of hitherto unknown biological phenomena or processes, or in some cases, of new cures and therapeutical devices". Although the first part of this definition, "the detection of hitherto unknown biological phenomena or processes", may seem to indicate a more narrow, observational oriented, concept 'discovery' than Kuhn's, it is obvious from Luttenberger's account of the controversy and deliberations preceding Ehrlich's prize that 'the result' of discovery includes theory. (Luttenberger talks of "the results" of a discovery in the criteria (i), (ii) and (v). See paragraph 2 below.) Even if the resultant theories were not supposed to be understood as a part of the discovery, the theories were still crucial in the evaluation of the scientific work. The Nobel Committee appears to have taken into account a process at least as comprehensive as the one Kuhn calls 'discovery'. If this is correct, a closer examination of the Nobel Committee's deliberations and decisions may provide a basis for challenging Kuhn's thesis about the difficulties in isolating and evaluating individual discoveries. 2. Luttenberger discerns six criteria for selection of 'the most important discovery' within the domain of physiology or medicine: (i) "that the results of a discovery had proven themselves to be of wide-ranging significance"; (ii) "that these results had been verified by the scientific community"; (iii) "that all issues of priority were established"; (iv) that "the work in question could clearly be distinguished as the candidate's own"; (v) "that [the research contribution] had been brought to a point where the given problem had been solved entirely, and



the result constituted 'a finished whole'"; and (vi) that "[the discovery] carries both theoretical weight and practical significance". 3. All these criteria tell us a great deal about the Nobel Committee's view on science at the time of Ehrlich's prize. Jtldging from these criteria the committee viewed the evolution of science as a process of more or less distinct achievements, each attributable, in some cases at least, to a single scientist (although the prize may in exceptional cases be divided between two or three scientists). Whether or not the committee could be said to have embraced a concept of development-by-accumulation depends of course partly on how we should understand the committee's views on problems being 'solved entirely' and results constituting 'finished wholes'. This criterion, (v), could, but need not, be understood to entail that the committee required that scientific achievements, in order to be important, should be permanent, in the sense Kuhn claims past historians viewed important discoveries to be permanent. However, this fifth criterion need not amount to more than e.g. the full assimilation of a new theory by the scientific community. This would then still be compatible with a theory of scientific evolution through paradigm shifts. Again, a further analysis of the Nobel Committee's evaluation procedure may provide an interesting point of departure for a discussion of Kuhn's theory of science. 4. That paradigms played a role in the Nobel Committee's deliberations has already been noted, when commenting upon Luttenberger's analysis of the differences in scientific styles between Ehrlich and Arrhenius. These were paradigms according to which the competing theories had been developed. The committee's evaluation of these two approaches/paradigms, as well as its comparison of earlier with more recent theories/paradigms, raises an interesting question about how dependent the committee itself was on prevailing paradigms when making these evaluations. Does not the evaluation of paradigms presuppose paradigms of a higher order, meta-paradigms of some kind? Are for example the Nobel Committee's criteria for selection of 'the most important discovery' (parts of) such a meta-paradigm? Since the members of the Nobel Committee were themselves actively engaged in the research fields within which the discoveries evaluated had been made, one may wonder if it is not, after all (despite Kuhn's objection [4]), as Popper contends, that researchers are prisoners caught in the framework of their theories only "in a Pickwickian sense", i.e. "if we try, we can break out of our framework at any time" [19]. Kuhn is not entirely clear on this point. On the one hand he contends that successive theories are incommensurable: though, to some extent, the language of the one theory may be translated into that of the other, permitting comparisons and argumentation for and against each of them, such arguments are usually not decisive for the researcher's conversion from one theory to the other, according to Kuhn; that transition is not made by deliberation and choice, but



rather like a gestalt switch ([3], pp. 198-204). On the other hand Kuhn makes perfectly clear that it is possible to determine which of two successive theories are from an earlier phase of development and which from a later: "Considering any two such theories, chosen from points not too near their origin, it should be easy to design a list of criteria that would enable an uncommitted observer to distinguish the earlier from the more recent theory time after time" ([3], p. 205; cf. [4], p. 264). To sum up: Luttenberger's paper does not only give new insights into the process behind the selection of Nobel prize winners in general and the choice of Paul Ehflich in particular. His paper also provokes the reader to reflect upon the roles of paradigms and possibly also meta-paradigms in science as a whole.

INTERTHEORETIC COMPETITION AND THEORY CHANGE Kenneth Schaffner's contribution consists of two parts, published as two separate papers. In the first he develops a concept '[temporally] extended theory', partly based on Imre Lakatos' 'methodology of scientific research programmes', and discusses three criteria for comparison and choice between theories - 'theoretical context sufficiency', 'empirical adequacy', and 'simplicity'. In the second part he applies this concept and these criteria in an analysis of the rationale behind the success of one of the central theories in Macfarlane Burnet's immunological work, the so called 'clonal selection theory'; a theory originally proposed by Burnet in 1957. Burnet shared the Nobel prize in physiology or medicine with Medawar in 1960 for the discovery of acquired immunological tolerance. Schaffner points out that Burnet's clonal selection theory was then not yet generally accepted. It was even considered refuted only two years after Bumet had been awarded the prize. The experiments 'disproving' the theory later turned out to be partly artefacts. The theory gradually gained acceptance and was, Schaffner points out, generally accepted by 1967. The main competitor of the clonal selection theory had been the so called 'instructive theory', originally developed in the early 1930's. By seeing the clonal selection theory and the instructive theory as extended theories Schaffner is able to show how these two competing theories may be understood to have been constructed and, when they were compared with each other, how the evaluation and support of only a part of one of the theories influenced the development as well as the acceptance or rejection of this theory as a whole. The concept 'extended theory' also explains in what sense a theory can be said to survive and remain 'the same', in spite of the fact that essential parts of the theory have been re-evaluated and modified.



Schaffner's concept 'extended theory' is partly an elaboration of central parts of Lakatos' 'research programme'. Their respective approaches to the question of theory change have several points in common. They both emphasize the importance of considering the status and functions of individual constituents of theories (i.e. the hypotheses, etc., that make up the theories) when analysing theory change. Schaffner's and Lakatos' approaches differ, however, when it comes to their views on what the status and functions of these constituents really are (or might be). There are also differences in the way they carry out their analyses. Lakatos analyses the theories (at least to some extent 14) in context, as parts of a 'research programme', whereas Schaffner concentrates on the theories themselves and discusses the criteria and methods for comparison and choice between theories, without explicitly trying to subsume these different components under a general concept for the whole evolutionary process, such as the Lakatosian 'research programme'. Lakatos' distinction between the concepts 'theory' and 'research programme' is not entirely clear. A 'research programme' consists of a 'hard core' (of e.g. laws), a 'protective belt' (of auxiliary hypotheses), and two sets of 'methodological rules' (the one determining what paths of research to pursue, the other what paths of research to avoid) ([2], pp. 132-138). An example of a methodological rule of the latter kind is that the research may not be aiming at falsifying the hard core. If we confine the analysis of Lakatos' concept 'theory' to what appears from the only Lakatos source Schaffner refers to [2], two interpretations are possible: (i) 'theory' is synonymous with 'research programme'; and (ii) 'theory' is a part of the 'protective belt'. If we go a bit further in our analysis we may find it plausible to make also a third interpretation: (iii) 'theory' is a part of the 'hard core'. The first interpretation is supported by Lakatos' example: "The classical example of a successful research programme is Newton's gravitational theory: possibly the most successful research programme ever" ([2], p. 133). It is also supported by clarifications, such as "a theory [i.e. programme]" and "theory (or, rather, 'programme')" ([2], pp. 142, 168; the square brackets are in the original). Although this interpretation may seem well-founded, Lakatos does at the same time seem anxious to distinguish 'theory' from 'research programme'. He says in a footnote: "Unfortunately in 1963--4 1 had not yet made a clear terminological distinction between theories and research programmes ..." ([2], p. 137). Perhaps a more narrow interpretation, taking into account the temporality of theories, would be closer to the concept of theory Lakatos had in mind. This interpretation has been suggested in a thesis on Lakatos' methodology of scientific research programmes: (i') 'theory' is a temporal version of a scientific research programme [20]. The second interpretation, (ii), can be made based on Lakatos' explicit



reference to a "protective belt of auxiliary theories" and the recurrent use of the expression "auxiliary theories" ([2], pp. 126, 175, 176). The third interpretation, (iii), is not supported by any explicit statement, as (i) and (ii) are, but may perhaps be inferred from Lakatos' example of a progressive Newtonian problem shift: A physicist of the pre-Einsteinian era takes Newton's mechanics and his law of gravitation, (N), the accepted initial conditions, I, and calculates, with their help, the path of a newly discovered small planet, p. But the planet deviates from the calculated path. Does our Newtonian physicist consider that the deviation was forbidden by Newton's theory and therefore that, once established, it refutes the theory N? No. He suggests that there must be a hitherto unknown planet p" which perturbs the path of p. He calculates the mass, orbit, etc., of this hypothetical planet and then asks an experimental astronomer to test his hypothesis ... Were the unknown planet p" to be discovered, it would be hailed as a new victory of Newtonian science. But it is not. Does our scientist abandon Newton's theory and his idea of the perturbing planet? No. He suggests that a cloud of cosmic dust hides the planet from us ... ([2], pp. 100-101). The theory in this example, N, is Newton's mechanics and his laws of gravitation. Lakatos calls the idea of the perturbing planet and the idea of a cloud hiding it 'auxiliary hypotheses'. Later in the text he explicitly points out Newton's law of gravitation (and his three laws of dynamics) as parts of the 'hard core' in Newton's programme ([2], p. 133). It therefore seems as if Lakatos contends that a theory, like N in this example, may be a part of the hard core.

It is of course possible that Lakatos deliberately uses "theory" in all three senses, in a similar way as he points out that "research programme" may be used for both science as a whole and for historical parts of science, like 'Cartesian metaphysics' ([2], p. 132). Schaffner seems to base his analysis on the first interpretation of Lakatos' concept 'theory'. When characterizing Lakatos' notion 'research programme', he refers to the example in which Lakatos equates Newton's gravitational theory with a research programme. Schaffner's own concept, 'extended theory', is somewhat narrower, however. Formulated in Lakatos' terminology, Schaffner's concept could be interpreted as: 'extended theory' comprises both a part (or the whole) of the hard core and a part (or the whole) of the protective belt, but not the methodological rules. Schaffner points out, however, that in contrast to Lakatos' 'research programme' there is no absolute distinction between hard core and protective belt in the concept 'extended theory'. Schaffner defines 'extended theory' as a set of hypotheses of varying "commitment strengths", ranging from (the most) "central" to (the most) "peripheral". (The parentheses "(the most)" are my interpretations. In part II Schaffner distinguishes between "primarily central" and "less central" hypotheses.) Schaffner's 'extended theory' differs from Lakatos' 'research programme' also in that the central hypotheses are classified according to their 'levels of generality'.



This classification is crucial to Schaffner's view on theory change. A researcher (proponent) may, according to Schaffner, aim at falsifying hypotheses at all levels of generality, except those at the most general level. Schaffner points out this (what Lakatos would call) 'methodological rule' as yet another difference between his own view on theory change and that of Lakatos. According to Lakatos, as we have seen, the methodological rules in research programmes forbid researchers from aiming at falsifying the hard core. Schaffnet disagrees with Lakatos at this point and contends that "investigators often do direct their experiments and theoretical modifications at the hard core". Schaffner disagrees because he interprets Lakatos to mean by 'hard core' m o r e than just, what Schaffner calls, 'central hypotheses at the most general level'. (Schaffner concretizes this latter concept through several examples in his analysis of both the clonal selection theory and the instructive theory.) Schaffner's analysis leads up to an interesting interpretation of the conditions for a theory being accepted in favour of another and how this weighing may be understood in quantitative terms, using Bayes' theorem. Schaffner assumes that the acceptance of one theory (or hypotheses) T 1, in favour of another T2, is based on a judgment, that the probability of T 1 being true, given the produced evidence (e.g. experimental results), is greater than the probability that T 2 is true, given the same evidence. Schafther shows not only how the probabilities of two competing theories at the same point in time may be calculated, but also how changes in the probability of one and the same theory at different points of time - ie. the probability of a temporally extended theory - may be calculated. The result of Schaffner's analysis is a model for explaining theory change, in several respects far more elaborate than Lakatos' methodology of scientific research programmes.

THE ORIGIN AND EFFECTS OF PRIZES IN SCIENCE Harriet Zuckerman broadens the perspective of the discussion, from physiology and medicine to science at large and from the Nobel prize to major scientific awards in general. She calls attention to the fact that during the past 20 years the number of prizes in the sciences has increased dramatically, five times in North America alone. Zuckerman discusses some of the principal explanations of this increase and whether the new prizes have amounted to any major changes in the reward system of science. She also enters upon the perhaps most fundamental issue concerning the significance of the Nobel prize for science, namely what effects awards of this magnitude may have on the work of individual researchers and on the evolution of scientific knowledge as a whole. Zuckerman points out as an explanation of the creation of new awards in



science, that the scarcity of Nobel prizes, the limit of prizes to three fields and to three recipients for each prize, have ruled out the recognition of co-workers of larger projects and a great number of outstanding contributions to science. Perhaps one may view the marked proliferation of prizes during the last two decades as a late reaction to the tremendous expansion of science in the 20th century. As Derek Price points out in his well-known introductory remarks to Little Science, Big Science... and Beyond (1986): ... using any reasonable definition of a scientist, we can say that 80 to 90 percent of all the scientists that have ever lived are alive now. Alternatively, any young scientist, starting now and looking back at the end of his career upon a normal life span, will find that 80 to 90 percent of all scientific work achieved by the end of the period will have taken place before his very eyes, and that only 10 to 20 percent will antedate his experience ([21], p. 1). Referring back to Kuhn's critique of the attempts to explain major turning points in the history of science by pointing out individual discoveries, each attributable to a single scientist, it is not difficult to see how much more complicated this task must be when it comes to science of our times. In addition to the problem Kuhn centers on, that the process of discovery may be so long that several scientists will succeed one another before it is completed, and besides the well recognized problem of collaborative research, there is also the problem of simultaneous independent discoveries. What impact the increased number of active researchers has had on the first problem is not known. (It is, as we have seen, partly a matter of how we define 'discovery'.) The second problem has clearly increased, if not in proportion of the general increase of active researchers, at least in absolute numbers. Zuckerman shows in Scientific Elite how the Nobel awards to scientists in the U.S. reflects the increase in collaborative research: During the first 25 years of the awards ... 41 percent of the laureates were honored for collaborative work ... During the second quarter century the proportion jumped to 65 percent, and it now [1977] stands at 79 percent of all prize-winners ([22], p. 176). However, in only about half of these cases did the laureates share the award with their co-workers: "from 19 percent during the first twenty-five years of the prizes to 24 percent during the second twenty-five years, and 41 percent during the third" ([22], p. 176). The third problem, simultaneous independent discoveries, might have increased in absolute numbers, but has probably decreased in proportion to the general increase of active scientists, due to radically improved communications. However, Robert Merton points out that although "the history of science records thousands of instances of similar discoveries having been made by scientists working independently of one another", there is still a need of more systematic studies of this problem ([23], pp. 371, 381).



Regarding the effects of major awards on the pace and direction of the evolution of scientific knowledge. Zuckerman doubts in her paper that these could be of decisive significance. She emphasizes that these prizes are usually confered on scientists whose contributions have since long been accepted. Zuckerman even contends that "major prizes may impede rather than advance scientific development by diverting scientists' energies from research on deep intractable problems to those whose solutions come more readily and will attract prize juries' attention". During the first years of the Nobel prize, when science was still conducted in the small-scale manner of the nineteenth century, the prize must have played a different role than it does today. In contrast to Harriet Zuckerman's first point, concerning the effect of the Nobel prize on science today, Elisabeth Crawford points out, in her work on the Nobel prize in physics and chemistry 1901-1915, that it could at that time in fact be of greater value to science if a wellestablished scientist, instead of a young, was awarded. The utility of the prizes for the financing of research came about mostly because they were awarded to established scientists (chairholders and directors of research institutes) who could capitalize on them in a number of different ways. Awarded in this manner, the prizes became more useful than they would have been if Nobel's idea that they function as a form of financial assistance for younger scientists had been realized ([24], p. 206). Natural science today is dominated by large-scale laboratory projects, often financed by governmental agencies, private foundations and industry. This transition from, what has come to be called, 'Little science' to 'Big science', has been thoroughly discussed by, among others, Jerome Ravetz [25]. 15 In Scientific Elite Zuckerman discusses how this transition has affected the role of the Nobel prize in science. In this study Zuckerman also examines another effect the Nobel prize may have on the researcher's work; an effect that brings us back to the first paper in this issue of Theoretical Medicine. The productivity of laureates, as indicated by the number of [scientific] papers published, declines sharply in the five years following receipt of the prize. Having published an average of 5.9 papers a year in the five years before an award, they declined in output by a third, to an annual average of 4.0 papers. ... the greater the increment in rank represented by the Nobel prize, the greater the immediate decline in the production of scientific papers... Laureates' published productivity declined even further in the sixth to tenth years after their awards, dropping by 27 percent in addition to the reduction of a third that occurred immediately after the award. The laureates published an annual average of 2.9 papers as compared with their earlier rate of 4.0 papers ([22], pp. 221,224-225, 229) This marked decline in publication could not be explained only by increased age. Zuckerman shows that the publication by scientists of the same age scarcely



decreased at all over comparable periods, from an annual average of 1.9 to 1.8 papers in the first period and from 1.8 to 1.7 in the second ([22], pp. 221,229). (It is interesting to note that laureates still publish so much more than other researchers of their age.) Zuckerman finds that the changes in the laureates' scientific and social roles, causing the decline in their publication of scientific papers, at the same time do enhance the work of others dependent on them. Thus, according to Zuckerman, the decrease in the laureates' rate of publication need not indicate a decrease in scientific activity and actual contribution to science. Evidently, to estimate the true impact of the Nobel prize on the evolution of scientific knowledge other measures are needed. Zuckerman's paper shows, through its wide approach, partly based on her comprehensive empirical study, Scientific Elite, how the Nobel prize serves as a model for other major awards, and which roles the reward system as a whole plays in the evolution of scientific knowledge.

CONCLUDING REMARKS I began this introduction by emphasizing how the five articles of this issue of Theoretical Medicine highlight the interaction between internal and external factors in the evolution of scientific knowledge. I would like to conclude by referring to Toulmin's penetrating analysis in Human Understanding [7] of the importance of seeing the change of internal and external factors as two aspects of one and the same historical process. Toulmin develops this idea within the framework of an evolution-theoretic interpretation of the history of human understanding, including the history of science. This makes his analysis particularly relevant also to the discussion of the analogy between the evolution of science and the evolution of nature. Toulmin points out that science can be viewed both as a 'discipline', "comprising a communal tradition of procedures and techniques for dealing with theoretical or practical problems" and as a 'profession', "comprising the organized set of institutions, roles, and men whose business it is to apply or improve those procedures and techniques" ([7], p. 142). He argues that it is not possible to fully understand scientific change, e.g. why a new concept (or theory) has succeeded and won acceptance in science, without considering both these aspects of the historical process. So long as the intellectual content of a science (say) was construed as a 'logical system', the history of scientific ideas could still be separated from the history of scientific institutions and activities, and the resulting histories could be written independently ... Once we begin treating disciplinary and professional development as alternative aspects of the same populational process, this autonomy must be called in question, and the two parallel histories of the enterprise can no longer be wholly independent ... we can



separate the 'internal' life-story of ideas from the 'extemal' life-stories of the men whose ideas they are, only at the price of over-simplification ([7], 142-143). Toulmin sees Darwin's theory of natural evolution as an example of a more general form of historical explanation. He analyses the process of conceptual change, e.g. in science, as only another example of the same form of explanation. In Toulmin's analysis both the evolution o f nature and the evolution o f knowledge ('conceptual change') are matters of 'variation and selective perpetuation': a process of "innovative factors, responsible for the appearance of variations in the population concerned [e.g. a population of concepts], and selective ones, which modify it by perpetuating certain favoured variants" ([7], p. 134). In addition to illustrating the interaction between internal and external factors in the evolution of science, the articles in this issue also clearly shows how essential the studies of the theory and history of discovery (and not only of the logic of justification) are for the understanding of the evolution of scientific knowledge. As Thomas Nickles points out in Scientific Discovery, Logic, and Rationality [26], the distinction between 'discovery' and 'justification' may not always be so easy to uphold. We have seen an example of this in the discussion of Luttenberger's paper. When the concept 'discovery' is so inclusive, as Kuhn's seems to be, and perhaps also the Nobel Committee's, that it comprises the adjustment or change of paradigm, 16 much of the 'justification' must already have been made before the 'discovery' is completed.

Acknowledgement - I would like to thank Professor Aant Elzinga and Dr K. W. M. Fulford for helpful comments on an earlier draft of this introduction.

NOTES 1 Lakatos takes this interpretation as a point of departure for developing his theory of 'scientific research programmes'. (For a discussion of this theory, see Lakatos [2]. We will come back to this theory in the comments on Kenneth Schaffner's two papers.) 2 Dawkins says: "If a scientist hears, or reads about, a good idea, he passes it on to his colleagues and students. He mentions it in his articles and his lectures. If the idea catch[e]s on, it can be said to propagate itself, spreading from brain to brain" ([5], p. 192). 3 Dawkin's definition of 'replicator' and 'vehicle' reads: "The fundamental units of natural selection, the basic things that survive or fail to survive, that form lineages of identical copies with occasional random mutations, are called replicators. DNA molecules are replicators. They generally ... gang together into large communal survival machines or 'vehicles'. The vehicles that we know best are individual bodies like our own" ([5], p. 254). 4 For an overview and extensive bibliography, see Ruse [8]. 5 For information on the pre-history of the Institute for Scientific Information and the development of Science Citation Index (first published in 1963), see [9-t 1]. 6 I.e. "The degree of stability exhibited when a measurement is repeated under identical



conditions" [ 12]. 7 Kuhn uses the term "paradigm" in several different ways. (See Masterman's analysis [14] and Kuhn's response to that [3], pp. 181-187). However, this need not concern us here. The concept may here be understood as "the entire constellation of beliefs, values, techniques, and so on shared by the members of a given community" and "the concrete puzzle-solutions which, employed as models or examples, can replace explicit rules as a basis for the solution of the remaining puzzles of normal science" ([3], p. 175). 8 Garfield does not express these probabilities explicitly in predictive values like this. The predictive values have been calculated from the figures Garfield gives in the paper and on information about the total number of Nobel laureates in the year in question, 1972 [18]. Garfield's study concerns the percentage of authors who won the Nobel Prize 1972 among those cited 1961-1972. Garfield finds that "Out of more than 1.8 million authors cited ... less than 2,100 were cited more than 1,000 times. In this list will be found all of the Nobel Prize winners for 1972 ...". Garfield does not specify what he means by "all of the Nobel Prize winners", but I have understood this to include only laureates in physics, chemistry, and physiology or medicine; in all 8 laureates 1972. Only one of them, Stanford Moore (chemistry), was among the 50 most cited. 9 See note 7. lo It should be noted that Kuhn uses 'invention' in a different sense than Nobel. Kuhn restricts the concept 'invention' to the construction of theories ([3], pp. 89-90), whereas Nobel seems to have in mind the contrivance of new manufactures. For Kuhn the invention of a theory is a matter of giving order to a collection of data. Kuhn distinguishes between "discoveries, or novelties of fact" and "inventions, or novelties of theory" ([3], p. 52), but at the same time it seems as if he views invention as a part of discovery. He even points out that the distinction is "exceedingly artificial" ([3], p. 52).) Kuhn seems to view invention of theory as the last stage in the process of discovery. He says that the process of discovery "closes only when the paradigm theory has been adjusted so that the anomalous has become the expected" ([3], p. 53); and this adjustment (or change) of paradigm seems to be exactly what Kuhn means by invention of theory: "the new paradigm, or a sufficient hint to permit later articulation, emerges all at once, sometimes in the middle of the night, in the mind of a man deeply immersed in crisis. What the nature of that final stage is - how an individual invents (or finds he has invented) a new way of giving order to data now all assembled - must here remain inscrutable and may be permanently so" ([3], pp. 89-90.) 11 See note 10. 12 'Paradigm' here understood as it is defmed in note 7. 13 See note 10. 14 I say "at least to some extent" because Lakatos sometimes also uses 'theory' as synonymous with 'research programme'. See interpretation (i) in the next paragraph. 15 Ravetz talks of an 'industrialization of science' at about the time of the Second World War; a transition from 'academic science' to 'industrialized science'. 16 See point 1 in my comments on Luttenberger's paper above p. 105.

REFERENCES 1. Popper KR. The Logic of Scientific Discovery. 9th impression. London: Hutchingson, 1977. 2. Lakatos I. Falsification and the methodology of scientific research programmes. In: Lakatos I, Musgrave A, eds. Criticism and the Growth of Knowledge. Reprint of the 1974 ed. Cambridge: Cambridge University Press, 1989:91-196. 3. Kuhn TS. The Structure of Scientific Revolutions. 2nd ed, enlarged. Chicago: The



University of Chicago Press, 1970. 4. Kuhn TS. Reflections on my critics. In: Lakatos I, Musgrave A, eds. Criticism and the Growth of Knowledge. Reprint of the 1974 ed. Cambridge: Cambridge University Press, 1989:231-78. 5. Dawkins R. The Selfish Gene. 2nd ed. Oxford: Oxford University Press, 1990. 6. Suppe F, ed. The Structure of Scientific Theories. 2nd ed. Urbana: University of Illinois Press, 1977. 7. Toulmin S. Human Understanding. Vol 1. Oxford: Clarendon Press, 1972. 8. Ruse M. Philosophy of Biology Today. Albany: State University of New York Press, 1988. 9. Garfield E. Information science and technology have come of age - organizational names should show it. In: Garfield E, ed. Essays of an Information Scientist. Vol 3. Philadelphia: ISI Press, 1980:448-51. 10. Lazerow S. Institute for Scientific Information. In: Encyclopedia of Library and Information Science. Vol 12. New York: Marcel Dekker, 1974:89-97. 11. Weinstock M. Citation indexes. In: Encyclopedia of Library and Information Science. Vol 5. New York: Marcel Dekker, 1971:16--40. 12. Last JM. A Dictionary of Epidemiology. 2nd ed. New York: Oxford University Press, 1988. 13. Garfield E. Citation analysis and the anti-vivisection controversy. In: Garfield E, ed. Essays of an Information Scientist. Vol 3. Philadelphia: ISI Press, 1980:103-8. 14. Masterman M. The nature of a paradigm. In: Lakatos I, Musgrave A, eds. Criticism and the Growth of Knowledge. Reprint of the 1974 ed. Cambridge: Cambridge University Press, 1989:59-89. 15. Garfield E. Where the action is, was, and will be - for first and secondary authors. In: Garfield E, ed. Essays of an Information Scientist. Vol 1. Philadelphia: ISI Press, 1977:280-3. 16. Garfield E. Are the 1979 prizewinners of Nobel class? In: Garfield E, ed. Essays of an Information Scientist. Vol 4. Philadelphia: ISI Press, 1981:609-17. 17. Garfield E. More on forecasting Nobel prizes and the most cited scientists of 1972! In: Garfield E, ed. Essays of an Information Scientist. Vol 1. Philadelphia: ISI Press, 1977:487-8. 18. Nobel Foundation. Nobel Foundation Directory 1991-1992. Stockholm, 1991. 19. Popper K. Normal science and its dangers. In: Lakatos I, Musgrave A, eds. Criticism and the Growth of Knowledge. Reprint of the 1974 ed. Cambridge: Cambridge University Press, 1989:51-8. 20. Cassel F. On Incompatibility In and Between Scientific Research Programmes. [Dissertation]. Stockholm: Akademilitteratur, 1984. 21. Price DJdeS. Little Science, Big Science ... and Beyond. New York: Columbia University Press, 1986. 22. Zuckerman H. Scientific Elite: Nobel Laureates in the United States. New York: The Free Press, 1977. 23. Merton RK. The Sociology of Science. Theoretical and Empirical Investigations. [Storer NW, ed]. Chicago: The University of Chicago Press, 1973. 24. Crawford E. The Beginnings of the Nobel Institution. The Science Prizes, 1901-1915. Cambridge: Cambridge University Press, 1984. 25. Ravetz JR. Scientific Knowledge and its Social Problems. Oxford: Clarendon Press, 1971. 26. Nickles T. Introductory essay: scientific discovery and the future of philosophy of science. In: Nickles T, ed. Scientific Discovery, Logic, and Rationality. Dordrecht: Reidel, 1980:1-59.

Discovery, theory change, and the Nobel Prize: on the mechanisms of scientific evolution. An introduction.

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