T H E O R Y C H A N G E I N I M M U N O L O G Y P A R T I: EXTENDED THEORIES AND SCIENTIFIC PROGRESS

KENNETH F. SCHAFFNER Department of History and Philosophy of Science, University of Pittsburgh, 1017 Cathedral of Learning, Pittsburgh, PA 15260, USA

ABSTRACT. This two-part article examines the competition between the clonal selection theory and the instructive theory of the immune response from 1957-1967. In Part I the concept of a temporally 'extended theory' is introduced, which requires attention to the hitherto largely ignored issue of theory individuation. Factors which influence the acceptability of such an extended theory at different temporal points are also embedded in a Bayesian framework, which is shown to provide a rational account of belief change in science. In Part II these factors, as elaborated in the Bayesian framework, are applied to the case of the success of the clonal selection theory and the failure of the instructive theory. Key words: Bayes' Theorem, Bayesianism, clonal selection theory, extended theories, rationality, scientific change, scientific progress, theory change, theory competition, theory structure

1. INTRODUCTION The past three decades have witnessed major transformations in the philosophy of science, none perhaps more significant than the attention given to scientific theory change. The impact of Kuhn's [1] and Feyerabend's [2] early monograph and essay led to Lakatos' [3] attempt to utilize and transcend Popper's [4] philosophical approach, and to a subsequent variety of other analyses of the dynamics of scientific change, including those of Toulmin [5], Laudan [6], Kitcher [7-9], and Shapere [10]. An historical overview of the depth and effect of these changes from the traditional 'received view' of scientific theories and theory change can be found in Suppe's Introduction and Afterword in his [11]. One of the messages contained in these important contributions on scientific change was that the 'unit' with which scientists worked was larger and more complex than what the 'received view' understood by a theory. In fact, focus on this older sense of 'theory' obscured a number of problems concerning scientific change, the dynamic character of scientific explanation, and the complex nature of inductive support of scientific theories. It is one of the theses of the present paper that we still do not have an

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adequate vocabulary in terms of which to describe and explain the nature of intertheoretic competition and scientific change. I am going to begin by summarizing some of the features of Lakatos' [3] model of scientific progress, and suggest how certain further developments of his approach move us toward the concept of an 'extended theory', as well as to some hitherto largely unaddressed questions regarding (1) theory individuation, (2) diachronic theory structure, (3) the relation of various levels in biomedical theories, and (4) the relation of problems (1) through (3) to scientific rationality and theory change. I will embed my analysis within a Bayesian framework. I am then going to apply and elaborate my approach by utilizing a high-fidelity account of recent theory change in immunology: the case of the clonal selection theory and its competition with the now discarded 'instructive theory' of the immune response. The subject of immunology would seem to be a most appropriate one for this special issue of Theoretical Medicine insofar as research in this domain has led to 21 Nobel Prizes in Physiology or Medicine over the past ninety years (see Silverstein, [12], Appendix B). In addition, the principal discoverer and champion of the clonal selection theory, F. Macfarlane Burnet, was himself a Nobel Laureate in 1960, and in his Nobel Address of that year [13] discussed his then recent work on the clonal selection theory as well as his other major accomplishments in immunology.

2. THE CONCEPTOFAN'EXTENDED THEORY'

2.1. From Kuhnian Paradigms to Lakatosian Research Programmes The major shift from the 'received view' of scientific theories was occasioned by Kuhn's introduction of the notion of a 'paradigm'. Though Kuhn was roundly criticized by, among others, Shapere [14] and Masterman [15] for vagueness and for conflating many different notions (Masterman discerned 21 different senses of 'paradigm' in Kuhn's [1]), the idea that a scientific theory had a number of components other than a small number of axioms" (which might possibly be scientific laws) has generally been accepted by both philosophers of science and scientists. Kuhn himself in his [1] Postscript made an attempt at clarification of his original 'paradigm' notion, and introduced the concept of a four-component 'disciplinary matrix'. One of those components, the 'exemplar', retained Kuhn's earlier focus on the paradigm as a "concrete scientific achievement" that functioned as a "locus of professional commitment" and which was "prior to the various laws, theories, and points of view that ... [could] be abstracted from it" ([1], p. 11; my emphasis). Such a paradigm was usually embodied in a scientific textbook or, earlier, in books such as Ptolemy's

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or Newton's Principia, but obviously could also be a (collection of) scientific article(s). This aspect of a paradigm has at least two significant, but interacting components: one is sociological and the other is temporal. 1 In introducing the notion of professional commitment and scientific communities as defined by (and defining) a shared paradigm, Kuhn identified an important characteristic of scientific belief systems that has had a major impact on the sociology of science. 2 In stressing a temporal developmental aspect of a paradigm - normal science is the solving of a variety of puzzles not initially solved by the paradigm, as well as the paradigm's further elaboration and filling in of finestructured details - Kuhn focussed attention on the temporally extended and subtly varying features of a scientific theory. What a falsificationist-minded philosopher might be inclined to see as a refuting instance of a theory, Kuhn interpreted as a puzzle that a modified form of a theory, derived from the same paradigm, could turn into a confirming instance. Lakatos, initially retrained as a Popperean, discerned in Kuhn's monograph a most serious critique of Popperean falsificationist methodology - one which had not only significant methodological consequences but which also raised profound moral and political questions. 3 In attempting to come to a rapprochement between Popper and Kuhn, and sensitive to Duhemian problems with falsificationism, Lakatos developed his 'methodology of scientific research programmes'. A research programme captures among other elements, the temporal dimension of a paradigm, but introduces a somewhat different internal dynamic structure. A research programme is constituted by four parts. It contains methodological rules: "some [of which] tell us what paths of research to avoid (negative heuristic), and others what paths to pursue (positive heuristic)" ([3], p. 132). A research programme also contains a 'hard core' - in general there are the essential hypotheses of a theory - and a 'protective belt' - a set of auxiliary hypotheses "which has to bear the brunt of tests and get adjusted and readjusted, or even completely replaced, to defend the hard core". The negative heuristic instructs us not to subject the hard core to falsification. An excellent example for Lakatos of a research programme was Newton's gravitational theory. There the hard core was Newton's three laws of dynamics and his law of gravitation, and the protective belt comprised various auxiliary assumptions concerning the orbits of planets, new force functions, etc. Lakatos was fond of warning that it would typically take many years to determine whether a research programme was progressing or degenerating, since simple falsifications would not function in this context. As already mentioned, other philosophers of science have seen the need to work with a more general 'metascientific unit' than the traditional theory, and

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they have tended to agree with Lakatos' position that falsification of the assumptions of the metascientific unit would be complicated if not non-existent. Along the lines of the latter view, Laudan, who introduced a Lakatos-like notion of a 'research tradition', wrote that "research traditions are neither explanatory, nor predictive, nor directly testable. Their very generality, as well as their normative elements, precludes them from leading to detailed accounts of specific natural processes" ([6], pp. 81-82). This, it seems to me, is far too weak a view of the control experience plays in science, and suggests that such philosophers of science have not provided us with a characterization of a metascientific unit which has sufficient structure to capture the types of debate that actually occur in cases of scientific theory competition. Paradigms, research programmes, and research traditions undergo considerable changes as their proponents do battle with competitors, and eventually, as I will argue, for good theoretical and experimental reasons there are (at least temporary) winners and losers. What I shall develop in the next subsection is a notion of a (temporally) 'extended theory' which I believe is a more appropriate metascientific unit in terms of which to analyze scientific change.

2.2. The Extended Theory as the Appropriate Metascientific Un# of Global Evaluation in the Biomedical Sciences I find it useful to begin from Lakatos' account as outlined above. I shall introduce various features of what I term an extended theory through criticisms of some of Lakatos' essential characteristics of research programmes. As briefly suggested above, I am using the notion of an extended theory to introduce a diachronic unit which (1) permits temporal theory change and which (2) also allows for some logical changes - namely some of the assumptions within the diachronic unit will change while the integrity of the whole is preserved. The latter is a necessary condition since we must be able to individuate one extended theory from another (or others) with which it competes. 1. Centrality. Returning to Lakatos' notion of a research programme let us begin by suggesting that there is no absolute distinction between hard core and protective belt, but rather a roughly continuous (and often shifting) set of varying commitment strengths ranging from hypotheses which are central to those which are peripheral. Such peripheral hypotheses are not dispensable without replacement, and often do serve to help individuate an extended theory from its competitor(s). 'Intrinsic centrality' refers to those entities and processes conceived of as essential elements in a Shaperean 'domain', which are designated by the selected postulates or laws in a representation of an extended theory. 4 The concept of a 'domain' was introduced in his [18] by Shapere to describe an historically integrated scientific subdiscipline. For Shapere a

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"domain" is a set of "items of information" with an "association" with the following features: (1) The association is based on some relationship between the items. (2) There is something problematic about the body so related. (3) That problem is an important one. (4) Science is "ready" to deal with the problem. ([18], p. 525) Though suggestive, the concept of a domain is difficult to make precise and Nickles [19], for example, believes that domains are better characterized as determined by a theory (or previously successful theories) that explains the "items of information", thus providing a unifying principle. However, this misses Shapere's important point which permits a 'domain' to exercise an important extrinsic control over what is an acceptable and/or complete theory of the domain. (Other essential elements in the domain which are explained by derivation from these postulates are of crucial importance, but do not figure as central features in the extended theory.) There may also be other postulates in the extended theory which will be central in the sense of individuating the theory from other competitors, but which may not be sanctioned by a preexisting consensus as constituting domain elements. These will be extrinsically central hypotheses, by which I mean hypotheses which cannot be given up easily without turning the extended theory of which they are a part into one of its competitors. Detailed illustrations of these notions will be provided later, but as a simple example one can think of an intrinsically central assumption of the well-known operon theory in molecular genetics as the sequence hypothesis, namely that the genes dictate the primary, secondary, and tertiary structure of proteins such as the repressor protein and the structural genes' proteins. 5 A central extrinsic assumption is that the regulation takes place at the level of transcription via repressor-operator binding. The utility of this distinction will become more evident in the following section in which we discuss a Bayesian kinematics and dynamics of belief change for competitions between extended theories. 2. Generality. The second distinction I make between Lakatos' account and the structure of an extended theory is that the hard core is not unilevel but is distinguishable into at least three different levels of generality. 'Generality' here must be distinguished from 'vagueness'. The essence of the notion of 'generality' is that an hypothesis which is general can be instantiated at a lower level by a broad range of more detailed specific hypotheses, each of which may be logically inconsistent with the other (temporally later) specific hypotheses. This occurs naturally because of the arnpliative character of theory elaboration at lower levels (see my [21] for a discussion of this feature of biological theory elaboration). Provisionally I will distinguish three levels of decreasing generality or increasing specificity, though these distinctions are both

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initially subjective6 and also may simply represent points on a continuum. The most general hypothesis I will term the y level. These hypotheses typically characterize a type of process involving a set of fundamental entities; illustrations will be provided below. I will assume a set of more specific subsidiary hypotheses, termed the t~ level, and finally a most specific highly detailed level I shall term the ~i level. In this terminology, there may be many mutually inconsistent ~ realizations of y level hypotheses, and similarly many mutually inconsistent 8 realizations of cy level hypotheses. The relation of being a realization may jump the level, and a 7 level hypothesis may be directly realized by a 8 level hypothesis. Hypotheses at the y, cy, or fi levels may be central or peripheral. In general, 8 level hypotheses will, de facto, turn out to be molecular level hypotheses but there is no reason in principal why a molecular level hypothesis cannot be t' level. The reason for the de facto relation between levels of generality and levels of aggregation has to do with the number of plausible realizations envisagable, and when one gets to the molecular level there are a sufficient number of constraints and auxiliary knowledge available that this level of aggregation usually will utilize ~5level of generality hypotheses (or mechanisms). 3. Change of Central Hypotheses. My third point of difference with Lakatos involves the fact that investigators often do direct their experiments and theoretical modifications at the hard core. In the terminology of extended theories this means that modifications at the ~ or 6 level of generality will be considered, though Lakatos is correct as regards a ban against attempted falsification at the T level for T central hypotheses by the theory's proponents. We re-examine such a situation in section 4 below. 4. The Semantic Conception of an Extended Theory. An extended theory as I am describing it in this article is neutral between what has been termed 'syntactic' and 'semantic' approaches to scientific theory representation. The semantic conception of a scientific theory was initially proposed by Beth and developed independently by Suppes [22, 23], Suppe [11], and van Fraassen [24, 25] and has more recently been applied to biological theories by Giere [26], Beatty [27], Lloyd [28, 29], and Thompson [30, 31]. Though what I will say in the present article will not require a commitment to the semantic conception, I do view that approach as possessing several advantages over the syntactic account, and elsewhere [32] have developed the notion of an 'extended theory" within the framework of the semantic conception. Space prevents me from elaborating on this dimension of the extended theory, but I do want to note that one of the attractions of the semantic account is that the traditional 'received view' of theories mentioned above characterized scientific theories primarily as linguistic structures - in terms of a small set of sentences (the axioms) -which would then be formalized. This required investigators to capture the form of a

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scientific theory, whereas it was also generally felt that there are several different linguistic means of representing a theory, which is in point of fact an extra-linguistic entity ([11], p. 45). Secondly, emphasis on the linguistic form of

a theory required some basic logic - usually the first order predicate calculus with identity - in which to express the theory. This not only was clumsy, but resulted in an impoverishment of theoretical language, since set theoretic language is richer than, say, first-order logic. In the semantic conception, though a clear characterization at an abstract level of the systems is essential, standard mathematical and biological English - as well as pictorial representations - can be utilized. This is a most important point and I shall rely on it further in Part II of this paper [33] where I characterize the clonal selection and instructive theories. Various equivalence arguments for syntactic and semantic approaches can be adduced, however, such as the fact that "an axiomatic theory may be characterized by its class of interpretations and an interpretation may be characterized by the set of sentences which it satisfies" [24]. And, as van Fraassen notes, these interrelations, and the interesting borderline techniques provided by Carnap's method of state-descriptions and Hintikka's method of model sets, would make implausible any claim of philosophical superiority for either approach. But the questions asked and methods used are different, and with respect to fruitfulness and insight they 1 specific contexts or for special purposes ([24], p. 326).7 may not be on a par w'th It must be stressed that employing a semantic conception does not eliminate the need to characterize the assumptions of a scientific theory in an explicit and clear manner. Typically this is done by axiomatizing the theory and (in one semantic approach) conjoining those axioms so as to constitute a "set-theoretic predicate". 8 (See [22, 23, 27, 31, 37].) I will proceed in a somewhat less formal but still rigorous manner in the following section where biological language will be used to characterize the two theories of interest. There is another way in which the semantic approach can give some additional structure to what was said above about levels of generality. We can, using the notion from model theory of a 'reduced model', extensionally represent increasing generality by increasing reductions of the detail in the model by simply eliminating those more specific axioms from consideration at that level of generality (i.e., deleting a gi which further specifies some oi). On the basis of these notions, we can then introduce the 'temporal' property of theory change by specifying a n e w time dimension in terms of which to represent the evolution of semantically characterized theories over time. This we accomplish notationally by a series of numerically increasing superscript integers, applying either to specific hypotheses (e.g. g4 t --->~ 2 ) or to an evolving theory T 1 ~ T 2.

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KENNETHF. SCHAFFNER 3. CRITERIA OF COMPARATIVE THEORY EVALUATION

What I prefer to call 'global evaluation' in science is almost always comparative. (I distinguish global evaluation from local evaluation where the latter type is what statisticians do when they are involved in 'statistical hypothesis testing' and calculating 'P values' of 'null hypotheses' or computing Bayesian posterior probabilities for comparatively simple hypotheses (see my [32], ch. 5, for details).) The "almost" qualifier is introduced to cover those few situations where a domain exists on the basis of a folk tradition and where (1) any proffered theory is so poor vis-h-vis accounting for well-supported experimental results that the existence of this aggregate of stable facts can result in the proffered theory's rejection, or (2) a proffered theory accounts for a reasonable number of the results in the domain and is thus accepted at least provisionally. In examining the factors philosophers have employed in global theory evaluation and choice, I suggested in my [38] that they can be grouped under three general headings: theoretical context sufficiency, empirical adequacy, and simplicity. Other proposed criteria can be seen as more specific forms or combinations of these criteria, e.g., precision generally is a species of empirical adequacy; scope (and consilience) are also species of empirical adequacy, and ad hocness is a combination of the lack of empirical adequacy and simplicity. 9 These factors are, at least to the first approximation, sufficient for my purposes in the present paper. Theoretical context sufficiency is intended to cover both a theory's selfconsistency as well as consistency or entailment relations with other well confirmed theories. Empirical adequacy refers to the ability of a theory to explain empirical results whether these be singular reports of experimental data or empirical generalizations, such as Snell's law in optics or the Franck-Starling relation in cardiology. Simplicity is the most difficult notion to define explicitly: roughly it is a comparative notion and places a premium on those theories with fewer entities, fewer independent hypotheses, and fewer terms such as the number of constants required to characterize an equation. (I return to a discussion of several senses and explications of simplicity below.) Each of these factors can vary in their force and each can be jointly weighted differently. Kuhn [1] has noted that: judgments of simplicity, consistency, plausibility, and so on often vary greatly from individual to individual. What was for Einstein an insupportable inconsistency in the old quantum theory, one that rendered the pursuit of normal science impossible, was for Bohr and others a difficulty that could be expected to work itself out by normal means .... In short .... the application of values is sometimes considerably affected by the features of individual personality and biography that differentiate the members of the group ([1], p. 185). Such variation is important to permit creativity to function and to rationalize

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pursuit of new theories. 1° It is interesting to note, however, that though such variation does occur, it is not as much as Kuhn suggests, and as time passes there is a convergence of this variation toward a mean among scientists. This convergence, I believe, is an illustration of the swamping effect of accumulating empirical evidence discussed by Bayesians, a view on which I will now comment briefly, but which for reasons of space cannot be examined in detail (but see my [32] for details). Characterizing the factors which influence the acceptance and rejection of theories does not provide us with a sufficient basis on which to discuss the dynamics of intertheoretic competition. I have not yet indicated, for example, how these various factors might be combined to jointly and rationally influence a decision, nor have I suggested how we might move from one temporal state with its evidence to a later one with additional evidence and how the probabilities of the two competing theories might rationally change. The best currently available answers to these questions lie in my estimation in the Bayesian approach to scientific hypothesis and theory testing. This is a large subject, and has been the focus of a number of books in the past and also very recently in philosophy of science. The position I adopt in this essay follows the work of Richard Jeffrey [43-45], Abner Shimony [46] and others (but with some difference and emendation) that rational commitments to an hypothesis or scientific theory can be interpreted as a tempered personal probability or a judgmental probability. Shimony has provided a proof ([46], pp. 104-110) that tempered personalism, in which any seriously proposed hypothesis is given a probability (ever so slightly) greater than zero, satisfies the axioms of the probability calculus. A Bayesian explication also resolves to some extent the troublesome question of acceptance. Similar to Rosenkrantz's [47] views, I take the position that scientists can pursue their research and their explanations from an essentially probabilistic perspective. The approach taken here will be inferential, but it can easily (and appropriately) be embedded in a decision-theoretic context. Probabilities can be multiplied by utilities and decisions taken which maximize (or only 'satisfice') expected utility. (The term "satisfice" is Herbert Simon's; see his [48], pp. 204-206 and chs. 14 and 15). I view the inferential approach permitted by the Bayesian position as more flexible and in better accord with scientists' activities than the inductive-behavior alternative favored by Neyman and more recently, if I understand him correctly, by Hacking [49]. I should add at this point that Earman [50] disagrees with this type of position, contrasting the notion of 'acceptance' (actually two notions: one Kuhnian and one pragmatic) with the probabilification of hypotheses and theories one encounters in the Bayesian approach. In my forthcoming [32] I discuss the Kuhnian notion and both disagree with it and argue that we can capture the type of commitments we find

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in cases of theory competition in a Bayesian framework as comparatively high probabilities or 'odds'. (In the present article it will not be possible to discuss this issue in any detail, though the example in Part II [33] will indicate how this matter can be resolved in a specific case.) As regards 'pragmatic acceptance', this appears to me to amount to a conditional commitment based on the same types of considerations. I believe that one can work with a theory or hypothesis and explore its consequences without requiring a new notion of 'acceptance' beyond what the Bayesian framework licenses. However to fully develop this idea and to show how it can adequately model scientists' deliberations and decision making processes from the planning of experiments to publication, as well as the process of community affirmation (e.g., the awarding of Nobel prizes), would be to take me far beyond the scope of this essay, and is appropriately left for a future research program. It is important to note that in contrast to earlier work in inductive logic by such eminent philosophers as Reichenbach [51, 52] and Carnap [53], recent inquiries in this discipline have moved much closer to the writings of statistical theorists. The preponderant move of inductive logicians has been toward the Bayesian position and is exemplified in Jeffrey's [43, 45], Salmon's [54], Hesse's [55], Rosenkrantz's [47], Howson and Urbach's [56], and Franklin's [57, 58]) monographs. Kyburg's [59] position and Levi's [60, 61] analyses have some affinities with a Bayesian view but are also importantly different. Hacking [49], Seidenfeld [621, and Giere [63-455] dissent from a Bayesian orientation, the latter preferring the Neyman-Pearson approach (but also compare his recent [66] "satisficing" approach), and the two former scholars a modified Fisherean account. Glymour [67] is anti-Bayesian and develops his own "bootstrapping" theory (also see Earman, ed. [68]). Earman's comprehensive review and analysis [50] concludes with a split decision about the strength of the Bayesian research program. This brief overview of some recent developments in inductive logic and Bayesianism should make it clear that there is considerably more to say about these matters than can be presented in the present article. What I offer in the following pages is accordingly only the simplest rudiments of the approach that can be given here: those sufficient to explicate the shift in opinion from the instructive theory to the clonal selection theory as described in the long illustration in Part II [33]. What readers of this essay will need to know is that Bayesians permit the introduction of 'prior' probabilities of statements (hypotheses and theories) into their evaluation machinery. In addition, Bayesians (as well as traditional statisticians) need to characterize the 'likelihood' of obtaining an experimental result if the theory (as well as its competitor(s)) is true. Then the 'posterior' probability (after a particular experimental outcome is obtained) is given by

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Bayes' Theorem: P(Hle) o¢ P(H)-P(elH) which says that the posterior probability of H given (I) e varies as the product of the prior probability and the likelihood (e given H). We can change the variation sign (~) into an equality sign for comparative situations yielding what is termed the 'Odds' form of Bayes' Theorem: (0)

P(Hile) P(Hjle)

=

P(Hi) "P(elHi) P(Hj) • P(elHj)

indicating that the ratio of the posterior probabilities, the posterior odds that one should rationally offer for H i against Hi, is a function of the prior odds multiplied by the likelihood ratio, where H i and Hj are competing hypotheses (or theories). In my approach to interpreting the locus of the force of evaluational factors within the Bayesian framework, I view the 'prior probability' as being affected by judgments of theoretical context sufficiency and simplicity, and the 'likelihood' as representing the effect of 'empirical adequacy'. How to incorporate formally (and notationally) the effects of the 'background' knowledge needed to incorporate these judgments will be shown further in Part II of this paper [33]. On the basis of this interpretation, additional arguments for the effects of a d h o c changes in the theory as well as the role of central versus peripheral hypotheses of a theory can be given useful clarifications. These will also be pursued further in Part II. It is difficult to provide much more in the way of a general set of factors affecting a logic of comparative global theory evaluation in an a p r i o r i way (and for reasons of space not much more can usefully be said about the Bayesian framework here); for more detail one must go to specific cases, which is the task of Part II of this essay.

NOTES 1 I put aside for the moment the radical thesis of historical discontinuity that the paradigm notion seems to entail. 2 See the festschrift for Robert K. Merton, Coser, ed. [16] for examples in the essays by J. Cole and H. Zuckerman and by S. Cole. The former two authors write "Kuhn's model of revolutionary change has been especially influential in studies of scientific specialties" ([16], p. 140). 3 Lakatos (personal communication, 1969). 4 Thus what are seen as 'central' in this sense will depend on how a theory is axiomatized. Maxwell in his account of his electromagnetic theory used the vector

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potential as a fundamental notion whereas Hertz (and Heaviside) axiomatizing the 'same' theory did not (see [17], chs. 5 and 6). 5 See Jacob and Monod [20], p. 352. It is difficult to give a more precise general characterization of 'intrinsic centrality' than I have above, though I do not think that there would be problems with recognized scientific experts relatively easily reaching a consensus on the intrinsically central features of a scientific theory, even if they thought the theory false or unsupported. 6 The subjective element could be objectified with the aid of a 'theory of generality' but this is best left for the future. 7 But see Worral's [34] views on this. 8I have written elsewhere (see my [21] and [35]) that frequently it will not be easy or helpful to axiomatize a biological or medical theory, in contrast with the utility that such axiomatizations have in physics, e.g., in Newtonian mechanics, Maxwell's electromagnetic theory, or quantum mechanics. This is because quite frequently typical biological and medical theories are best represented by families of analogically related models, and a linguistic representation of all of the changing hypotheses of the models is a formidable task and does not add much to the biological sentential and pictorial figure representations found in standard textbooks such as Watson, ed. [36]. Nevertheless, when we are focussing on the specifics of theory competition and theory change axiomatization can be clarifying, and essential, in identifying a theory's commitments and changes over time, as will be demonstrated below. 9I am not strongly committed to only these three factors for global theory evaluation. In my ([39], p. 376) I also proposed a principle of the unity of fundamental biological processes, though I now think that the scope of such a principle is quite narrow and the principle might better be formulated as one that gives weight to closely analogous precedent mechanisms/narrow generalizations. Other writers have suggested still additional criteria for theory assessment, among them Kuhn [1] in his Postscript and again in his [40], Newton-Smith [41], and Darden ([42], ch. 15). 10 See Laudan ([6], pp. 109-114) for a discussion of the logic of pursuit.

REFERENCES 1. Kuhn TS. The Structure of Scientific Revolutions. 2nd ed. Chicago: The University of Chicago Press, 1970. 2. Feyerabend PK. Explanation, reduction, and empiricism. In: Feigl H, Maxwell G, eds. Scientific Explanation, Space, and Time. Minneapolis: University of Minnesota Press, 1962: 28-97. (Minnesota Studies in the Philosophy of Science; Vol III). 3. Lakatos I. Falsification and tile methodology of scientific research programmes. In: Lakatos I, Musgrave A, eds. Criticism and the Growth of Knowledge. Cambridge: Cambridge University Press, 1970: 91-196. 4. Popper KR. The Logic of Scientific Discovery. [German ed, 1934]. New York: Free Press, 1959. 5. Toulmin S. Human Understanding. Vol 1. Princeton, NJ: Princeton University Press, 1972. 6. Laudan L. Progress and Its Problems. Berkeley: University of California Press, 1977. 7. Kitcher P. The Nature of Mathematical Knowledge. New York: Oxford University Press, 1983. 8. Kitcher P. 1953 and all that. A tale of two sciences. Philosophical Review 1984; 18: 335-73. 9. Kitcher P. Explanatory unification and the causal structure of the world. In: Kitcher P, Salmon S, eds. Scientific Explanation. Minneapolis: University of Minnesota

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