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 II: THE CLONAL SELECTION THEORY

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 In Part I of this essay [1] I reviewed various proposals that have been made in the past thirty years suggesting an analysis of scientific change requires a broader conception of a scientific theory than one encountered in the 'received view' of the Logical Empiricists, I began from some of the features of Lakatos' [2] model of scientific progress, and suggested how certain further developments of his approach move us toward the concept of an 'extended theory'. I also related this notion of an extended theory 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 (I) through (3) to scientific rationality and theory change. In addition, I suggested that these issues were best embedded within a Bayesian framework. In this Part of the essay, I shall apply and elaborate my approach by utilizing a high-fidelity account of recent theory change in immunology: the case of the clonal selection theory (CST) and its competition with the now discarded 'instructive theory' of the immune response.

Theoretical Medicine 13: 191-216, 1992. © 1992Kluwer Academic Publishers. Printed in the Netherlands.

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2. THE CLONAL SELECTION THEORY AS AN EXTENDED THEORY Bumet's theory was initially proposed in his [3] and further elaborated by him in 1958 in the Abraham Flexner lectures at Vanderbilt on "Clonal Selection as Exemplified in Some Medically Significant Topics", published as The Clonal Selection Theory of Acquired Immunity [4]. The theory initially encountered resistance and was even 'falsified' several times in its early life as I shall recount in detail below. 1 Such falsifications subsequently turned out to be experimental artifacts, and the power of the theory was gradually appreciated, with the theory becoming generally accepted by 1967. 2 Currently the clonal selection theory serves as the general theory of the immune response, and all finer structured theories involving detailed cellular and molecular components are required to be consistent with it. 3 In his [8] Bumet sketched what he characterized as the 'essence' of his theory. It does articulate in a somewhat more explicit, modem, and concise manner what was asserted in 1957, but it is most useful for my purposes in this paper to begin with a concise account of the theory. Bumet introduced the fundamental assumptions as follows ([8], p. 213): 4 (1) Antibody is produced by ceils, to a pattern which is laid down by the genetic mechanism in the nucleus of the cell. (2) Antigen has only one function, to stimulate cells capable of producing the kind of antibody which will react with it, to proliferate and liberate their characteristic antibody. (3) Except under quite abnormal conditions one cell produces only one type of antibody. (4) All descendants of an antibody-producing cell produce the same type of antibody. (5) There is a genetic mechanism [Bumet preferred somatic mutation] capable of generating in random fashion a wide but not infinite range of patterns, so that there will be at least some cells that can react with any foreign material which enters the body. (For readers unfamiliar with immunology, a diagram (Figure 1) which indicates how clonal selection works in a simplified manner may well clarify these essential assumptions of the theory.) The clonal selection theory, however, is really an extended theory in the sense characterized earlier. The theory was formulated in 1957, elaborated in 1959, and tested a number of times by a variety of experiments from 1957 on. In a significant sense it was 'accepted', in the sense of being granted high probability in the immunological community by 1967, as indicated by a review of the papers in the 1967 Cold Spring Harbor Symposia on Quantitative Biology volume on 'Antibodies'. This Cold Spring Harbor volume constitutes the

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'0 6 O II

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Memory Cell

Effector cells

Fig. 1. Diagram of a contemporary version of the clonal selection theory. Stage 1 shows representatives of three resting lymphocytes bearing receptors for antigens complementary to antibodies with U, V, and W types of specificity. A bacterium (BAC) with antigenic determinants which bind with V specific antibody activates the middle lymphocyte. In Stage 2, the activated lymphocyte proliferates to form an expanded cloned population. In Stage 3, some of these cells become long-term memory cells, but most differentiate into effector cells and release soluble antbody of the V type. proceedings o f a conference held June 1-7, 1967 and attended by 300 of the most prominent immunologists o f that time. Even in that book, however, Felix Haurowitz exhibited a kind o f ' K u h n i a n ' resistance when he wrote: It may be a heresy to talk in this group about direct template action. However, I would like to show in a diagram [Figure 2] that template action of the antigen could still be reconcilable with our present views on protein biosynthesis. As shown in the diagram, the antigenic determinant might force the nascent peptide chain to fold among its surface, and thus might prevent the incorporation of certain amino acids. Growth of the peptide chain would continue as soon as a suitable amino acid is incorporated. Such a process might also cause the elimination of one amino acid, or of a few amino acids from the peptide chain, but would otherwise not alter the amino acid sequence ([13], p. 564).

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8

Fig. 2. The diagram shows the hypothetical template role of an antigen fragment (Ag) during the translation phase of antibody biosynthesis. The amino acid residues 1-3 and 7-9 have been assembled according to the triplet code provided by the messenger RNA molecule (mRNA). The antigenic fragment interferes with the incorporation of the amino acid residues 4, 5, and 6 since these cannot yield a conformation which would allow the growing peptide chain to fold over the surface of the antigenic determinant (black area in Ag). For this reason, the aminoacyl-RNA complexes no. 4-6 are rejected and the sequence 4, 5, and 6 either replaced by three other amino acids x, y, and z, as shown in the diagram, or omitted. The latter process would result in a deletion. (The Figure and legend is reproduced from Haurowitz F., Cold Spring Harb Symp Quant Biol 1967; 32: 559--67, with permission from the Cold Spring Harbor Laboratory.) In addition, Morton Simonsen in his [14] article in those proceedings indicated doubts about the simple form o f the clonal selection theory. What is most interesting about the clonal selection theory's route to 'acceptance' is that it was significantly 'refuted' in 1962. The peregrinations and modifications of the theory, and the factors affecting 'rejection' and 'acceptance' should serve as an excellent illustration and test o f the notions o f extended theory and of a generalized global Bayesian logic of comparative theory evaluation. 1. The Form of the Clonal Selection Theory in 1957-1959. The simple form

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of the clonal selection theory is introduced in the quotation from Bumet's [8] above. Now, however, I need to expand aspects of its temporally changing structure and exhibit it as an illustration of an extended theory. Here I will employ the 1957 (and 1959) articulations of the theory, distinguishing the following hypotheses and employing the % cy, 8 notation discussed in section '2. Generality' of Part I of this paper ([1], pp. 179-180). 71: Antibody formation is the result of a selective process: no structural information is passed from the antigen to the antibody. •2: Antibody specificity is encoded in the genome of the antibody producing (plasma) cell. 83: Antigenic determinants are recognized by (gamma-globulin) surface receptors on lymphocytes, and this receptor is identical in specific type with the soluble antibody produced by the cell's clonal descendants. o4: Antigen reacting with the surface receptors stimulates the cell to proliferate as a clone. 85: All antibodies produced by a cell or its descendants are of the same specific type(s) (in primary, secondary, and tertiary structure). 5 Y6: There is a mechanism for the generation of antibody diversity (probably ~6: somatic mutation). ~7: One cell (most probably) produces only one type of antibody (however, since cells are diploid, it is possible that two different types of antibody might be produced by one cell). These seven hypotheses are primarily central hypotheses of the clonal selection theory. Some of these are more detailed realizations of higher level hypotheses such as o 6 is of ~(6- Several less central but important hypotheses of the theory are: t~8: Some descendants of proliferating cells differentiate to plasma cells and release soluble antibody, but others persist in the parental (lymphocyte) state and carry long-term immunological memory (for the secondary response). o9: Self-tolerance is generated by elimination (in embryo) of forbidden (antiself) clones. t~10:Some cells function directly (i.e., not via release of soluble antibody) as in the homograft response. 6 The distinction between centrality and less central assumptions is based on my interpretation of remarks made by Bumet in his [3, 4] and his retrospective [8]. Each of the hypotheses should be conceived of as having a "1" superscripted to it as some of these will change. On the basis of my earlier claim, Y1 and Y6 cannot change; other hypotheses may or may not change depending on historical circumstances. The postulates probably do not constitute a minimal non-redundant set, and

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some may be consequences of others, especially if background theories are taken into account. 7 Nevertheless this seems to be an accurate and useful reconstruction of the clonal selection theory in its earliest form. It should be noted that though y level hypotheses are generally systemic, ~ level generally cellular, and 8 level usually molecular, there are exceptions. Hypotheses ~2 is actually genetic and ~3 is clearly interlevel. Recall that the provisional distinctions between y, c~, and 8 are intended to represent levels of generality and not necessarily levels of aggregation. 2. The Main Competitor of the CST: The Instructive Extended Theory. There were several competitors to the CST when it was proposed by Burnet in 1957. Jeme's natural selection (but non-cellular based) theory, Talmage's selection theory, and Burnet's (and Fenner's) own earlier indirect template theory had been proposed and were still fairly plausible accounts. 8 The main competitor theory at this time, however, was the direct template theory or, to use Lederberg's term, the instructive theory. This theory had initially been proposed in the early 1930's, first by Breinl and Haurowitz [16], and also independently by Alexander [17] and Mudd [18].9 Initially Breinl and Haurowitz had believed that an antigen might interfere with the lining up of amino acids in the peptide chain, and that this might result in differences in the order and orientation of the amino acids ([21], p. 34). Later an elegant chemical mechanism (at the atomic molecular and 8 level of specificity) based on hydrogen bonding and other weak bonds was developed for this theory by Pauling [22]. According to this hypothesis, it was only the tertiary structure (or folding) of the antibody molecule that was interfered with by the antigen. The theory in its post-1940 form (which persisted largely unchanged until the late 1950's) can be characterized in terms of the following hypotheses: ]tl: Antigen contributes structural information to the antibody. fi2: The function of antigen is to serve as a template on which the complementary structure of antibody molecules are formed. 83: The order of amino acids in the active site of the antibody molecule is irrelevant. ~54: Template action is by stabilizing of the hydrogen bonds and other weak bonds in the antibody molecule. (This is actually a 842 hypothesis, the Breinl and Haurowitz (1930) hypothesis being 84 t - see above.) ~5: Antigen penetrates into the antibody-producing cell. It follows from Y1 that antigen must be present whenever antibody is formed, whether it be initial formation or renaturation (refolding) of the antibody after chemical denaturation (unfolding). There are several additional less central hypotheses which have been abstracted from later versions of the direct template theory, principally from Haurowitz's writings (see [21]): l°

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~/6: Immunological memory (secondary response) is attributed to persisting antigen interacting with antibody. No c~ or 5 level mechanism is proposed. (Note that this is not only a general non-specific hypothesis but also amoIecular level hypothesis.) Y7: Tolerance is attributed to a common mechanism of immunological paralysis which occurs without excess of antigen. This theory was again modified with respect to the mechanism of tertiary folding by Karush [23], who proposed: (543) covalent disulphide (S-S) bonds were instrumental in stabilizing the tertiary structure of antibody molecules. Thus the 542 of Pauling goes in the Karush version to 543 (in our formalism).

3. Arguments Between the CST Proponents and the Instructional Theorists. The main objection of the instructional school against any type of selection theories (initially directed against Ehrlich's early 1900 side-chain theory) arose in the late 1920's out of Landsteiner's classic work on eliciting antibody responses to a variety of artificially synthesized antigenic determinants. 11 It was thought extremely unlikely that the antibody producing animal (or its ancestors) could have earlier experiences with these previously non-existent and newly synthesized molecules, and also unlikely that as much information as would be required to anticipate such antigenic structures could be carried in the organisms' genomes. Instructional theories provided a simple explanation of the ability of animals to synthesizeantibody against "various artifacts of the chemical laboratory" to use Haurowitz's phrase, such as azophenyltrimethylammonium ions. Burnet found this objection "intuitive" and not compelling, and suggested that the information necessary to encode about 104 different antibody types should not overly tax a genome. In 1962 Burnet wrote: A majority of immunologists find it difficult to accept the hypothesis that 104 or more different patterns of reactivity can be produced during embryonic life without reference to the foreign antigenic determinants with which they are 'designed' to react. This response is perhaps more intuitive than logical. After all we know that in the course of embryonic development an extraordinary range of information - probably many million 'bits' - is interpreted into bodily structure and function. There is no intrinsic need to ask for another 10,000 specification to be carried in the genetic information of the fertilized egg ([25], p. 92). Bumet suggested there were at least three ways the some 10,000 patterns could be obtained: germline, somatic mutation, and a then recent suggestion by Szilard that different patterns can be produced and manipulated by the cell's own enzymes. No special stress on somatic mutation appears at this point in Burnet's account. In the early 1960's, after the initial confirming experiment of Nossal and Lederberg [9], the clonal selection theory ran into considerable experimental difficulties. Burnet had begun with the simple form of the CST. In 1962 he

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characterized this form as follows: it is the simplest self-consistent theory, and because it is so inherently simple it is probably wrong. As yet, however, no decisive evidence against it has been produced and it is a good rule not to complicate assumptions until absolutely necessary. Occam's razor is still a useful tool ([25], p. 90). Simplicity, however, as has been argued above in connection with the thesis of generalized empiricism, is o f lesser import than experimental results, and as Bumet noted in 1967, experiments did begin to raise difficulties for the CST. In his 1967 address to the Cold Spring Harbor meeting, Burnet wrote: There is one aspect of the ten years I am talking about that has interested me enormously. Most of the crucial experiments designed to disprove clonal selection once and for all, came off. Attardi et al. [26] showed that the same cell could often produce two different antibodies if the rabbit providing it had been immunized with two unrelated bacteriophages. Nossal much more rarely found a double producer in his rats. Trentin and Fahlberg [27] showed that, by using the Till-McCulloch method, a mouse effectively repopulated from the progeny of a single clone of lymphoid cells could produce three [or four] different antibodies. Szenberg et al. [28] found too many foci on the chorioallantois to allow a reasonable number of clones amongst chicken leukocytes and so on ([5], p. 3). These experiments, such as the double producer and Trentin's quadruple producer and the Szenberg et al. work on the Simonsen phenomenon, for a time moved Burnet toward a considerably modified selection view known as subcellular selection. This temporary fall-back view was seen by instructionists such as Hanrowitz as a refutation of the CST, 12 though Burnet saw the modification as still consistent with a selection hypothesis of the 71 type. In a 1962 paper, Bumet wrote "Further study o f the [Simonsen or graft versus host] phenomena in Melbome has ... shown conclusively that the simple form o f the clonal selection theory is inadmissible. The first difficulty is that competent cells have a proportion of descendants whose specificity is different from their own ... the second difficulty is that too high a proportion of ceils can initiate loci" ([29], p. 13). Earlier, writing with his colleagues Szenberg, Warner and Lind, it was asserted that, "A selectionist approach (Lederberg, [10]) is still necessary but for the CAM-focus system it must be a sub-cellular selection" ([28], p. 136). The Simonsen phenomena continued to trouble the CST. 13 The mystery o f the double-producers was resolved, however, partly by discovering the artifact nature of those results by 1967 (see [30]). This was also Burnet's most recent view before his death. 14 In the quotation from Burnet's 1967 Cold Spring Harbor address, given above, he noted that "crucial experiments designed to disprove clonal selection once and for all, came off". In a later paragraph in that address he drew a distinction between these experiments and new heuristic advances. He wrote: But, on the other hand, every new heuristic advance in immunology in that decade - and

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it has been a veritable golden age of immunology - fitted as it appeared easily and conformably into the pattern of clonal selection. With each advance some minor ad hoc adjustment might be necessary, but no withdrawals or massive re-interpretations. Sometimes the new discovery was actually predicted. The statement (Burnet, [4], p. 119) that the lymphocyte 'is the only possible candidate for the responsive cell of clonal selection theory' was validated by Gowans' work in vivo and by Nowell [31] and many subsequent workers, especially Pearmain et al. [32], in vitro. The thymus as a producer of lymphocytes must have immunological importance and Miller's work in 1961 was the effective initiation of the immunological approach to the thymus (Miller, [33]). The origin of thymic cells from the bone marrow was the logical extension of this. In quite different directions, Jerne and Nordin's [34] development of the antibody plaque technique provided a precise demonstration of two very important presumptions of the theory that in a mouse a few cells capable of producing anti-rabbit or anti-sheep hemolysin are present before immunization and that on stimulation with sheep cells a wholly different population of plaque forming cells develops from what appears if rabbit cells are used as antigen. The findings by several authors in 1964-65 that pure line strains of guinea-pigs responded to some synthetic antigens but not others; the analysis of the classic Felton paralysis by pneumococcal polysaccharide which showed that in the paralyzed mice there was a specific absence of reactive ceils - these facts just don't fit any instructive theory. Finally, there is the immensely productive field that opened when the work of Putnam and his collaborators led to a progressive realization of the monoclonal character of myelomatosis and the uniformity of the immunoglobulin produced ... [G]iven the established facts of human myelomatosis you have almost a categorical demonstration of (a) clonal proliferation, 0a) phenotypic restriction and precise somatic inheritance, (c) the random quality of somatic mutation, and (d) the complete independence of specific pattern on the one hand and mutation to metabolic abnormality such as failure of maturation of the plasmablast, on the other. Almost all the essential features of clonal selection are explicitly displayed ([5], p. 3). This distinction between heuristic and experimental results, though suggestive, will not, I think, stand up under closer scrutiny. To an extent, some of the work Burnet reports under heuristic results are experimental findings. More important are the experiments on renaturation of antibody molecules which were considered in 1964 and 1965 by both Burnet and Haurowitz as most significant. In an article on "The Unfolding and Renaturation of a Specific Univalent Antibody", which appeared in the November 1963 number of the Proceedings of the National Academy of Sciences, Buckley, Whitney and Tanford noted that "the chemical basis for antibody specificity has not, so far, been determined" ([35], p, 827). They suggested that there were three possibilities: (1) the Burnet and Lederberg approach whereby specificity was encoded in the primary structure of amino acid sequence, (2) variability dependent on disulphide (covalent) bonds (this is the Karush [23] modification I noted above), and (3) variability dependent on non-covalent bonds where the specificity is directed by a complementary antigenic structure. (There the authors referred to Pauling's [22] work.) Buckley and his colleagues worked on a small fragment of antibodies, employing an important discovery by Porter made in 1959 that a digestive

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enzyme could cleave the antibody into fragments. They directed their attention to that smaller fragment which was equivalent to the larger (parent) molecule as regards antibody specificity and affinity for antigen (later called the Fab part). Buckley, Whitney, and Tanford forced the Fab part of the rabbit antibody specific to bovine serum albumin to unfold by adding a reagent to the antibody, testing their result by examining the optical rotation power of solutions of the antibody fragments. Reversal of the unfolding was brought about by slow removal of the reagent by dialysis. In analyzing their results they asserted that "these data provide very strong evidence that different antibody specificities cannot be generated by different arrangements of non-covalent bonds in molecules of identical covalent structure" ([35], p. 833), citing other investigators' related work on both covalent and non-covalent mechanisms. They summed up their position noting that "one must conclude from these considerations that antibody specificity is generated primarily by differences in amino acid sequence in some portion of the antibody molecule". Also cited in support of this notion was a then recent important discovery by Koshland and Engleberger [36, 37] that two different antibodies for the same animal had different amino acid sequences. Previously this had been masked by insufficiently sensitive experimental techniques. Burnet recognized these experiments in an article he wrote in 1964. In Bumet's view these experiments constituted "Evidence from several sources [that] seem to render [the instructive theory] untenable". He added: Koshland and Engleberger have shown differences in amino acid constitution of two antibodies from the same rabbit, Buckley, et al. have shown that completely denatured 7globulin fractions can regain immunological specificity on renaturation ([38], p. 452). Haurowitz also took note of both of these results in his 1965 review article, writing that the Pauling version "has lost much of its appeal by the discovery of different amino acid composition of two antibodies formed simultaneously in a single animal .... and by the observation that unfolded and denatured anti-BSA from rabbit serum refolds and regains its antibody activity after removal of the denaturing guanidine salt [the reagent] by dialysis" ([21], p. 36). It is important to realize that Haurowitz did not question these observations, though he did call into question some of the auxiliary assumptions made by these experimenters. For example, he expressed doubt whether in the work of Buckley, et al. discussed above, "the unfolding of the antibody fragments ... is indeed complete as concluded from the change in optical rotation" ([21], p. 16). Haurowitz also questioned whether the amino acid differences found by Koshland and Engleberger "involve the combining groups of these antibodies or whether they are merely a consequence of the heterogeneity of the two antibody populations" ([21], p. 40; my emphasis). Acceptance of a relatively stable observation language and many of the assumptions of these experiments did not

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result in Haurowitz's relinquishing his commitment to the instructive theory, however, for he wrote in his review article that "the reviewer would attribute the small changes in amino acid composition [discussed by Koshland and Engleberger] to a disturbance of the coding mechanism by serologically determinant fragments of the antigen molecule, resulting in a change in the cellular phenotype but not its genotype" ([21], p. 36). What we have here then is a modification of one of the central 8 level assumptions, namely the Panling hypothesis - stable since the early 1940's in this extended theory though questioned by Karush in 1958 - and its replacement by a new 8 assumption: the disturbance of the coding mechanisms of protein synthesis. (This approach is further developed in Haurowitz's [13] in the quote (and in Figure 2) given above, and will be reconsidered again in the next section as an instance of an ad hoc hypothesis.) The 1965 modification amounts to still another 8 4 in the instructive theory, after Breinl and Hanrowitz's [16], 841, Pauling's [22], 842, and Karush's [23], ~43, and underscores the kind of diachronic variation which exists at lower than "/levels of generalization in an extended theory.

3. TYPES OF FACTORS INVOLVED IN THE CST-INSTRUCTIVE THEORY DEBATE In section 3 of Part I of this article [1] I discussed three types of factors which influence theory 'acceptance' and 'rejection'. We have now examined a fairly detailed illustration of extended theory competition and can return with profit to the Bayesian logic of comparative theory evaluation outlined above both to relate that logic to the example and to elaborate further that logic. Since we are dealing both with a normative logic and a logic which permits some variation in this application, one must anticipate deviations from the logic in individual cases. 15 1 submit, though, that the individual assessments can in a sense be 'averaged' so as to demonstrate a change in consensus among scientists over time. Individual variation, as has been noted implicitly, is in part a function of what that individual knows - not all scientists hear of an experimental or theoretical innovation at the same time, nor do all scientists react to such news in the same way: an individual's own background knowledge and 'prior probabilities' will affect his or her interpretation of novel results. It is clear, however, at least in the example I have sketched in section 2 above, that in the 10 years from 1957 to 1967 the consensus of immunologists shifted from a commitment to the instructive theory to the clonal selection theory. 16 In the present section I investigate the dynamics - in the sense of the factors which forced that shift - of this change in consensus. I shall begin by discussing 'simplicity'. This, as has been noted several times,

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is generally the weakest of the types of dynamic factors involved in theory change, though in situations in which other stronger factors are individually or jointly indeterminate it can become significant.17 1 then progress to a discussion of the role of intertheoretic considerations (what I termed theoretical context sufficiency) which also affect the prior probability. I then turn to considering empirical adequacy. I will at that point also very briefly discuss how ad hoc modifications affect theory assessments. Some general comments on comparability of probability assessments will then close this section and also this essay. 1. Simplicity. Earlier I suggested that 'simplicity' determinations affect the prior probability of hypotheses and theories. We saw an instance of this in section 2 above in which Pauling's [22] modification of the instructive theory's assumption resulted in increased simplicity and, according to assessments in review articles, increased commitment by immunologists to the extended instructive theory. Other inductive logicians of a Bayesian persuasion have also located the effect of simplicity assessments in the prior probability component of Bayes' Theorem. Most notable are the suggestions of Sir Harold Jeffreys who first (with Dorothy Wrinch) proposed that simple laws have greater prior probability than more complex laws. Jeffreys and Wrinch [43] use a paucity of parameters criterion for simplicity, ordering laws from the simpler to the complex as one moves from y=ax, y=ax 2, y=ax 3 ... y=ax n, for example. Jeffreys and Wrinch realized that one would have an infinity of hypotheses whose prior probability must sum to unity, and provided a scheme for assigning that probability. Jeffreys later modified this approach in his Theory of Probability and the explication has been criticized from several different points of view by Popper ([44], ch. 7 and Appendices vii and viii) and others. 18 It is unclear that a paucity of parameters criterion is a suitable one, in any event, to apply in semiquantitative sciences such as biology and medicine, though insofar as this can be generalized to an Occam type of simplicity, Jeffreys' approach may be a good approximation. There is no consensus definition of the important notion of simplicity. As Einstein has noted: "an exact formulation of [what] 'logical simplicity of the premises (of the basic concepts and of the relations between these which are taken as a basis') [consists in] meets with great difficulties" ([46], p. 23). Logical simplicity has nonetheless "played an important role in the selection and evaluation since time immemorial" ([46], p. 23). Einstein also suggested that assessing logical simplicity or determining which formulation of a theory contained "the most definite claims" usually found agreement among scientists. Terming such factors as logical simplicity "inner perfection", he wrote that in spite of the difficulty of defining various senses of simplicity "it turns out that among the 'augurs' there usually is agreement in judging the inner

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perfection of the theories" ([46], pp. 23-25). A review of Hesse's ([42], ch. 10) discussion of simplicity will disclose the variety of senses the term has had for philosophers and scientists. As indicated above, I have suggested, along with Jeffreys, that simplicity is best conceived of as affecting the prior probability. 19 It is worth considering two points where simplicity enters in the above example of competition between the CST and the Instructive Theory. First, recall Burnet's 'complication' of the original simpler CST to account for double and triple or quadruple producers, and the later detected strong Simonsen effect (in the strong version of the effect, 1 out of every 40 lymphocytes would produce the effect). Now consider Pauling's 542 modification of the earlier, Breinl-Haurowitz instructive theory hypothesis Pauling proceeded by attempting to answer the following questions. He wrote:

541.

What is the simplest structure which can be suggested, on the basis of the extensive information now available about intra-molecular and intermolecular forces, for a molecule with the properties observed for antibodies and what is the simplest reasonable process of formation of such a molecule? ([22], p. 2643) There are several ways in which Pauling was guided by simplicity, e.g., in his assumption that antibodies had a common primary structure. 2° Pauling also noted that antibody-antigen complexes precipitate, and that in forming such a precipitate lattice or framework, "an antibody molecule must have two or more distinct regions with surface configuration complementary to that of the antigens" ([22], p. 2643). Pauling added: The role of parsimony (the use of minimum effort to achieve the result) suggests that there are only two such regions, that is that the antibody molecules are at most bivalent. The proposed theory is based on this reasonable assumption. It would, of course, be possible to expand the theory in such a way as to provide a mechanism for the formation of antibody molecules with valence higher than two, but this would make the theory considerably more complex, and it is likely that antibodies with valence higher than two occur rarely if at all ([22], p. 2643; my emphasis). The sense of simplicity here appears closer to Occam's: presuppose the minimum number of entities required. It would seem then that the desideratum of simplicity interpreted in a generalized Occam's razor manner is best located as a factor affecting prior probability. The determination of what specific weight to attach to simplicity, and a detailed explication of simplicity, are at least partially empirical questions, and the answers may vary from historical case to historical case. Here we can only give rough comparative indications as in the above quotations. Further elaboration of a detailed partially empirical theory of simplicity will require extensive additional research. 2. Theoretical Context Sufficiency. Issues involving conformity with wellconfirmed theories of protein synthesis significantly affected the acceptability of the CST and the Instructive Theory in the early to middle 1960's. Burnet's and

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Haurowitz's comments in the proceeding sections dearly support this point, and Haurowitz felt constrained to keep his views in approximate conformity with the increasingly detailed mechanism of protein synthesis emerging from the work of geneticists and molecular biologists. How this was done and the decreasing flexibility protein synthesis theory offered proponents of the instructive theory was noted above. In the simple Bayesian schema outlined earlier, recall that I proposed to accommodate this intertheoretic effect on acceptability by locating it in the prior probability. For any hypothesis h at any level of specificity (~,, c, or 5) a scientist assesses the P(hlb), where b, the background knowledge, includes other wellconfirmed theories. Each hypothesis can be assessed alone as well as jointly (for details see my [11], ch. 5). Thus far we have assumed a stable background b. This, however, is only good to the first approximation in limited contexts, and in point of fact in our historical example the b changed as regards a theory of protein synthesis and the primary structure determination of tertiary structure (known as the sequence hypothesis). In representing the dynamics of theory change, then, one must do what the Bayesian terms a 'reconditionalization' with a modified b in a number of cases. The exact procedure is not well understood, 21 but as long as the shift from b at time 1 to b at time 2 is applied consistently to any given case of theory competition, i.e., it would be inappropriate to compare P(Tli[bl) with P(T2ilb2), special problems regarding this background change should not arise. Since both theoretical context sufficiency and simplicity judgments affect prior probability in the view being urged here, some consideration as to how these operate jointly is needed. Above, in treating simplicity, I alluded to the possibility that both the simplicity determination and the weight a scientist might attribute to that determination might vary from individual to individual. This point can be accommodated together with a theoretical context sufficiency assessment in the prior probability expression by taking a weighted product: P(TIb) = OtPTes (Tlb) • ~Psim (Ylb) where o~ + 13 = 1, and in general ~ > 13, since theoretical context sufficiency judgments usually figure more prominently than simplicity assessments in global comparative theory evaluation. The exact values of the prior probabilities, or the weights given the theoretic context or simplicity will in general not matter too much if the experimental situation becomes clear (and certain other fairly general conditions hold), since Bayesians have shown that likelihood effects can 'swamp' the effects of divergent priors (see [51]), but also see Earman's criticisms of this claim [52]. 3. Empirical Adequacy. The Bayesian approach suggests that we revise our probability by condifionalization as new evidence becomes available. This

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means, as noted earlier, that as new experimental evidence (e 1) becomes available, we update our probability by Bayes' Theorem: P(Tlbl&e) o~ P(TIb 1) . p(ellbl&T) where b refers to 'background knowledge'. We can construct a new b 2 = b 1 & e 1 and assess the effect of a later new e 2 by rewriting P(TIb2& e) ~: P(T[b 2) • p(e21b2 & T) where o~ is the symbol for 'is proportional to'. In providing a global evaluation of two competing theories, say the CST and IT (for the Instructive Theory), we compute P(TITIbi & e i)

P(TiTIbi).p(eilbi & TIT)

P(TcsTIbi & e i)

P(TcsTIbi).p(eilbi & TCST)

each time as i=l, i=2, etc., reincorporating the 'old' e i into the new b i+l and assessing the effect of the 'new' e i+l. Let us call this the reiterative odds form of Bayes' Theorem. As shown by Savage and his colleagues, this reiterative process will result in a convergence, even if the priors are divergent, if the conditions of the principle of stable estimation are met. 22 There is a difficulty which arises in connection with deterministic hypotheses and theories which has received scant attention in the Bayesian literature, and which must be commented on at this point. In the testing of statistical hypotheses of the type discussed extensively in the statistical literature, the likelihood expression P(elh) has been generally thought to be well-defined. Savage in fact used to contrast the more subjective judgment involved in the prior probability P(h) with the more 'public' calculaton of the likelihood term in Bayes' Theorem. 23 This may be the case for hypotheses which suggest welldefined distributions, such as the binomial or beta distributions illustrated in the standard examples, though recently some Bayesian statisticians have questioned even this assumption (see [53]). When the hypothesis under test is deterministic and entails the evidence, as is usually the assumption in such a context, philosophers have suggested setting P(elh) = 1 (see [38], p. 82). Some statisticians have suggested, though, that since any measurement involves uncertainty, one could use the uncertainty inherent in the measuring apparatus to obtain a likelihood of < 1 (see [54], p. 15). 24 If, however, there is a (conditional) probability < 1 for the likelihood, and the likelihood expression is viewed as a Bayesian probability measuring how well the hypothesis accounts for or explains the evidence e, the likelihood expression takes on characteristics more similar to a 'prior' probability: it measures the

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'belief' of the individual scientist that h accounts for or explains e. This view would apparently not trouble some Bayesian statisticians, who have urged that the likelihood cannot legitimately be separated from the prior (see [53]), but it does introduce an additional explicit subjective element into the Bayesian approach. If, on the other hand, one views subjectivity masquerading as objectivity as worse than a frank acknowledgement of the subjective aspects of judgments, as Savage frequently suggested, 25 the Bayesian position may represent as much objectivity as can be obtained. In point of fact, the recognition of a subjective element in likelihood determinations does not eliminate the ability of the Bayesian approach to enforce a consistency of belief on an individual's judgments, but it may open the door to additional (though rationalized) disagreement among proponents of competing hypotheses. There is a way in which the odds form of Bayes' Theorem introduced several times above may offer some assistance in understanding how considerations of empirical adequacy affect theory acceptance. As noted above in the reiterative odds form, one is comparing the explanatory abilities of TCST with TIT in comparing likelihood ratios. If Tcs w gives a more precise explanation and e is more in accord with CST than TIT, then the likelihood ratio of CST to IT will be greater and favor the former over the latter. This is a sequential process, and the reiterative form of Bayes' Theorem can represent this process of competition over time. Suppose, however, a y-level hypothesis of CST were falsified, as would occur if a proponent of the CST were unable to provide a new unfalsified or ~-level hypothesis consistent with CST. Then its (CST's) likelihood becomes arbitrarily close to zero, and the alternative triumphs. 26 Thus the theorem will also incorporate an analogue of Popperean falsification. 27 Though 'falsification' is important, the procedure of being able to successfully save a prima facie refuted theory was encountered many times in the course of the historical example developed in section 2. We saw two types of outflanking moves in such rescues. One type was to assign provisionally the force of the refutation to one or more auxiliary hypotheses (as in Haurowitz's initial assessment of the Buckley et al. experiment). The other type of move made to outflank falsification is to change one or more of the hypotheses (exemplified, for example, by the sequence of ~54 changes in the instructive theory above). Both of these moves are often associated with the name of Pierre Duhem [57] who first clearly identified and described them. In more recent years, similar theses have been associated with the name of W.V. Quine, who argued persuasively in an influential article [58] that there was no sharp separation between analytic and synthetic statements, and later developed this thesis into a view that all assertions and theories about the world are underdetermined by the evidence [59]. This later more general thesis of Quine explains to an extent why the two

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outflanking strategies can work. This Quinean point of view also, I think, satisfactorily accounts for any 'incommensurability' discernible in the historical case examined in section 2. Quinean underdetermination, however, is not all that persuasive: in point of fact, as experimental evidence increases, the flexibility a proponent has in outflanking falsification decreases. It is in these circumstances, moreover, that extraempirical considerations such as simplicity and theoretical context sufficiency can exercise considerable constraint on hypothesis modification. These considerations also suggest a deeper Bayesian explanation for the force scientists attribute to the notion of 'direct evidence', a term that often appears in the scientific literature and which is discussed in my [11], ch. 4 (also see Shapere on 'direct observation' in his [60]). The power of 'direct evidence' arises from the very low probability of any competing explanation of that evidence; again the odds form of Bayes' Theorem indicates quite clearly why this is the case. I believe that the Bayesian perspective as outlined thus far can illuminate how these increasing constraints on rescuing options arise. I also think that such a Bayesian analysis will be closely connected to an account of what are termed ad hoc hypotheses, in the pejorative sense of that term, and have elsewhere [11, 48] give/a a detailed account as to how to do this (also see [39], pp. 110-112). In the space allotted for the present paper I will not be able to present that account here. Something like the analysis of ad hoc given in the references above, however, is necessary to understand fully the changes in scientific consensus regarding the merits of the instructive and clonal selection theories of the immune response. In the historical account earlier we saw several moves in which seriously ad ,hoc hypotheses were proposed that strongly and negatively affected belief commitments of scientists, such as Burnet's sub-cellular selection hypothesis (Haurowitz thought this tantamount to a refutation of the CST) and Haurowitz's attempt to save the instructive theory by his 1965 modification of the 84 hypothesis. By 1967, as already mentioned, most immunologists had been convinced of the correctness of the clonal selection theory and had abandoned the instructive theory. Haurowitz, then (and even ten years post-1967 [61]) still its ablest elaborator and defender, was not convinced an instructive approach had to be abandoned. Recall he proposed in his article in the 1967 Cold Spring Harbor volume that the presence of antigen in protein synthesis might reject some fragments of t-RNA bearing amino acids and favor other t-RNA-amino acid complexes. (See Figure 2 above and accompanying text.) This would preserve a positive quasi-instructive role for antigen and represent still another return in a sense, (now a 845) to the original 1930 Breinl-Hanrowitz analysis. The modification is ad hoc in the sense that it is meant to outflank the falsifying experiments

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that eliminated the instructive modification of Pauling, but preserve the T instructive hypothesis as well as one other even (3 level hypothesis - e.g., entrance of antigen into the cell. In my analysis sketched in [11] which largely follows my [48], I show why this move is objectionable. (Briefly what this amounts to is showing that the hypothesis under consideration p(H21b) = P(~IT5 Ib1967) is very low since the hypothesis finds no support from the then extant theory of protein synthesis, and is antagonistic to selective processes found in all other areas of biology.)

4. Hypothesis Centrality, ad hoc Theory Modifications, and Theory Integrity. At several points in my discussion above I have employed the odds form of Bayes' Theorem to explicate extended theory global evaluation. I would like to argue now that this form of the Theorem can also be used in clarifying one of the senses of centrality discussed earlier, namely extrinsic centrality. This notion was defined as a property of an hypothesis which served to distinguish the extended theory of which it is a part from a competitive extended theory. An hypothesis obtains this property, which is relative to competitors, by being able to explain an item(s) in the theories' domain on the basis of itself and a common complement 0. The Bayesian factor in this case is the likelihood ratio, for recall that: P(TIIe)

P(eIT 1)

P(elH l& 01)

P(T2Ie)

P(elT2)

P(elH2& 02)

Now it often happens as a science progresses that initially quite disparate extended theories begin to converge. This occurs because modifications of the non- T central hypotheses in the light of increased experimental and intertheoretical constraints lead toward overlap of hypotheses. In the extreme case 01 = 02 and then H 1 and H 2 are the only distinguishing characteristics. H 1 and H 2 may or may not be intrinsically central (see [1], p. 179) but by convergence of 01 and 02, the hypotheses H 1 and H 2 become the extrinsically central or 'essential' differentiating characteristics. Now if the likelihood ratio is much different from unity, which will be the case in the above situation if either H 1 or H 2 (but not both) explains e much better than its competitor, we have in the situation which produces e an (almost) crucial experiment. If H 1 or H 2 represents a T level hypothesis, and if the only possible more detailed realizations of the T level hypothesis are ad hoc in the pejorative sense (because of very low prior probability), then a massive shift of relative support between T 1 and T 2 will occur because of e. When this happens we encounter a major consensus shift, as happened in the years 1964-1967 as regards the clonal selection theory - instructive theory competition. A theory which has evolved to the point of major overlap with its competitors has major

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attention focussed on the differentiating hypothesis. This hypothesis cannot be yielded without the theory becoming identical with its competitor, and this type of change represents the limit of modifiability of the extended theory. Notice that it may only be a relative or comparative limit, but then, on the basis of the view expressed in this paper, that is the nature of global theory evaluation in most situations.

4. CONCLUSION In this two part paper I have sketched the outlines of a logic of comparative theory evaluation and embedded it in a Bayesian framework, as well as applied it to a recent illustration in the biomedical sciences. Before concluding, however, we should consider the extent to which such an inductive logic comports with the manner in which scientists actually reason. As Davidson, Suppes, and Siegel [62] and subsequently Tversky and Kahnemann [63] noted, people do not in general behave in a Bayesian manner. This raises the question of how a normative analysis such as that sketched above can be defended as a reasonable explication of scientific practice. Howson and Urbach ([39], pp. 292-295) address this question and cite other research on human problem solving indicating that in a number of circumstances people make clear mistakes in reasoning. Additional support for this point can be obtained from the work of Stich and Nisbett [64]. Just as we do not require that the measure of logical reasoning be based on all-too-human informal fallacies of deductive reasoning, it is inappropriate to reject a Bayesian perspective because many individuals do not reason in a Bayesian manner. But more can be said, I think, namely that we have in the Bayesian framework not only a powerful apparatus for comprehending the testing (in the evaluational sense) of statistical hypotheses (see [39]), but we also have a plausible application of extensions of that analysis in the examples presented above, and in the extensive and burgeoning Bayesian literature cited throughout this article. Whatever the ultimate form the foundations of statistics may take, it is reasonably certain it will be different from contemporary views. Savage himself wrote toward the end of his career that: "Whatever we may look for in a theory of statistics, it seems prudent to take the position that the quest is for a better one, not for the perfect one" ([55], p. 7). It is a recurring thesis of this article that the Bayesian approach is currently the best and most general foundation from which to search for such a theory. In sum, then, we seem to have a defensible notion of global evaluation that is a generalization of the Bayesian approach to statistical hypothesis testing. The account sketched is clearly a framework, and at a number of points I have

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indicated that further research, both of a logical and an empirical nature, will be required to determine the ultimate adequacy of this account. I think, however, because of its considerable internal structure and its fidelity to the historical case considered, and its conformity to other historical cases both in biology and physics (see my [48]), it represents one of the more promising analyses of global theory competition and scientific rationality.

Acknowledgements - I would like to gratefully acknowledge comments on an earlier version of this two-part essay by Arthur M. Silverstein, as well as those of three anonymous reviewers for this journal. APPENDIX

Where Might the Numbers Come from in a Bayesian Approach to Global Evaluation? In both classical and Bayesian statistics, both prior probabilities and likelihoods are often obtained using various theoretical models that statisticians term distributions (see almost any statistics textbook or my [11], ch. 5). For classical statisticians, these function in likelihood determinations, and for Bayesians they can function in both likelihood and prior probability assessments. The selection of a distribution is based on a judgment that the experimental and theoretical information available warrants the choice of that distribution. For well defined and typically local forms of evaluation good reasons can be offered for the selection of a particular distribution. For the more controversial and largely unexplored territory of global theory evaluation such distributions may not be easily available, and some of the existing alternatives to such a strategy will need to be explored. One alternative strategy that offers some promise is to utilize relative frequencies. Holloway writes that "Many data-generation processes can be characterized as tests devised to determine some particular property. For example . . . . medical tests are aimed at diagnosing particular problems. Often the tests are calibrated by trying them on particular populations and obtaining relative frequency information. In some cases these data can be used to calculate likelihoods" ([65], p. 327). This approach might involve an historical-sociological data gathering project, wherein investigators would seek to determine the frequency with which laboratory reports and review articles appearing in recognized scientific literature defending a particular theory reported experiments as confirming or disconfirming. This tack has not to my knowledge been tried even by Bayesian-oriented commentators on experimentation, such as Franklin [66], and it may be difficult to determine how to ask the right ques-

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tions. It has the attraction of being more 'objective' than the third alternative to which I turn in the next paragraph, but may be much more difficult to implement. A standard third alternative to obtain the likelihoods needed in a Bayesian application is to ask the scientists involved to provide 'subjective' assessments, or to do this for them in a speculative manner as I do below. The same approach can be taken for determination of the prior probabilities of hypotheses. This strategy has been worked out in considerable detail along with applications to examples in science in the Bayesian literature, for example in McGee [67]. The scientist is first asked to provide prior probabilities for the hypotheses that are being tested. There is no reason that a conjoined set of hypotheses such as constitute the CST and the IT examples above cannot be employed (but neither is there any reason why more focussed assessments could not be obtained; for suggestions as to how to accomplish this see my (Ill], ch. 5)). Thus Burnet might have been asked for such a determination and offered P(CSTIb) = 0.8 and P(ITIb) = 0.2, whereas Haurowitz might have proposed the reverse or even a more extreme difference, such as 0.01 and 0.99. In addition to the prior probabilities, subjective assessments can be obtained for the likelihood of different experimental results on the assumption of the competing theories. These numbers will also differ between proponents and opponents of a particular theory but will have to cover the range of possibilities, and then experience in the laboratory chooses which of the likelihoods actually is employed in Bayes' Theorem to update the probability of the competing theories. Thus we might speculate that for Burnet P(recovery of structure outcome of Buckley et al. experimentlCST) = 0.9, whereas Haurowitz might temper his judgment and offer a 0.7. It is likely that a less biased assessor would provide a fairly high likelihood for this assessment, say 0.85, and a correspondingly low likelihood for the actual outcome on the assumption of the IT. Similar likelihoods could be obtained from scientists for additional experiments, such as the Koshland and Engleberger [36] results. This permits the use of the reiterative form of Bayes' Theorem to operate and drive the successive posterior probabilities towards high probability for the CST. The actual calculations for determining either posterior odds or posterior probability are facilitated in the general case by using the 'evidence form' of Bayes' Theorem, which is stated in the Bayesian literature as: ev (Tie&b) = ev (TIb) +

10 logl0 [P(elT&b)/P(el~T&b)]

posterior evidence

increment or decrement in evidence

prior evidence

(This is obtained from the odds form by taking the logarithm of both sides of the equation and rearranging terms - see [67], p. 298 for proof.) Tables have

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been calculated to obtain posterior probabilities, odds, and evidence values (e.g,, [67], Appendix I, p. 366 was used for this calculation). Application o f this form to the unbiased assessor who might choose priors of 0.5 and 0.5 for the competing theories yields a posterior probability o f 0.85, which would have been anticipated on intuitive grounds. The more complex calculations for our hypothetical Burnet and Haurowitz examples are left to the reader. They will converge towards increased probability for the CST, but for Haurowitz very slowly because o f his strong prior against the CST theory.

NOTES 1 Falsification, as Lakatos was fond of remarking, often takes on different senses and must be looked at over the long term [2]. In connection with the 'clonal selection theory', Burnet himself wrote in his 1967 essay that "most of the crucial experiments designed to disprove clonal selection once and for all, came off" ([5], p. 3). See full quotation below on page 198. 2 See the 1967 proceedings of the Cold Spring Harbor meeting on 'Antibodies', with opening remarks by Burner and concluding comments by Jerne in [6]. 3 See for example Watson, ed. [7], Vol. 2, p. 838. 4 It should be pointed out that Joshua Lederberg made early and important contributions both to testing the clonal selection theory (see [9]) and to clarifying the essential and molecular aspects of the theory [10]. In its early years, the theory was frequently referred to as the Bumet-Lederberg theory of clonal selection (see [11], chs. 4 and 5 and also [12]). 5 This hypothesis does not specify the number of types; it embodies the sequence hypothesis. Hypothesis '~7 limits this type number to one (probably) or two (possibly). I thank Dr Arthur Silverstein for bringing the distinction between hypotheses 5 and 7 to my attention. 6 Dr Silverstein (personal communication) suggests that this hypothesis may reflect an expansion of the original clonal selection theory. 7 For example, ~5 is probably derivable from the central dogma of protein synthesis together with the other hypotheses. 8 For a good introductory account of these theories see Burnet [4], ch. 4 of my [11], and also Talmage's earlier [ 15] review. 9 Silverstein in his recent [19] history of immunology also cites Topley's [20] work. Also see Silverstein's interesting report of a personal communication with Haurowitz in [19], p. 84-85, n. 39. to See Haurowitz [21] for an excellent review of the instructive theory vis-~t-vis the CST. 11 Landsteiner's work is summarized in his classic monograph The Specificity of Serological Reactions [24]. 12 Haurowitz [21], pp. 32-33. t3 The resolution of the problem with the Simonsen phenomenon is somewhat murky, and will be discussed in my forthcoming [ 11 ]. 14 Personal communication, March 16, 1978. 15 See Howson and Urbach [39] for additional comments on the normative character of Bayesian inference and the extent to which scientists may be Bayesians. 16 How to combine different individuals' probabilistic judgments into a summary assessment is a complex undertaking and though some progress has been made in this area there is as yet no consensus on how to model consensus. See Genest and Zidek [40].

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(I thank Jay Kadane for this reference.) 17 See my [41] and also Hesse ([42], ch. 10) for a general discussion of simplicity in connection with comparative theory evaluation. Readers should also note Howson and Urbach's ([39], pp. 290--292) suggestion that simplicity is such a difficult notion to analyze that perhaps one should not do anything other than allow it to function in various individuals' priors. 18 See Glymour ([45], pp. 78-79) and also the discussions in Hesse ([42], pp. 226-228) and Howson and Urbach ([39], p. 292). 19 In his [47] Roger Rosenkrantz proposed a quite different but still Bayesian explication of simplicity, but has located the notion in the likelihood term of Bayes' Theorem. In my [11] I offer arguments against this view. 20 I suspect this 'guiding' took place in both discovery and justification phases of Pauling's work. For comments on the use of identical factors in both phases see my [48]. 21 Shimony (personal communication, but also see his [49]) suggests that when b changes, we do not use Bayesian conditionalization but rather start over again. This has similarities to Levi's [50] and Howson and Urbach's [39] suggestions, but leaves the kinematics ill-defined. 22 See [51 ], for a discussion of this principle. 23 See the discussion in [51], pp. 199-201. 24 Box and Tiao discuss the measurement of a physical constant and provide a standardized likelihood function represented by a 'Normal curve'. Shimony (personal communication) also seems to favor something like this approach. 25 See his comment ([55], pp. 15-16) that Bayesians, by recognizing subjectivity, are more objective in the sense of more constrained than those who are typically characterized as 'objectivist'. 26 See Salmon ([56], p. 117) for this suggestion, and also the comment by Howson and Urbach ([39], p. 81). 27 1 say "analogue" since if we accept Shimony's [49] "tempering" suggestion, we do not obtain a 0 probability.

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