2.1. Mendeleev, Meyer, and the periodic table

Dimitri Mendeleev published his first version of the periodic table of chemical elements in 1869. Mendeleev’s insight was to order all known chemical elements primarily according to their atomic weight. It is well known that this resulted in several gaps in the table, which led to Mendeleev’s famous predictions of three new chemical elements, namely Scandium, Aluminum, and Germanium, which were all discovered in subsequent years. It is less well known that Mendeleev also made so-called contrapredictions, that is, predictions against what was assumed to be established knowledge at the time (Brush Reference Brush1996; Schindler Reference Schindler2014). For example, uranium was widely believed to have a chemical weight of 120. This would have put uranium between tin (weight of 118) and antimony (122). But chemically, uranium did not quite fit there; for example, uranium has a much higher density than these elements. Mendeleev therefore suggested in 1870 that the weight of uranium be doubled (by doubling its valence), moving it to a group with other heavy atomic elements. Mendeleev sought empirical evidence for his theoretical hunch in the form of specific heat experiments (carried out by an assistant of his), but they failed to deliver a favorable result. Still, Mendeleev had convinced himself of this change and retained U = 240 in his tables, even though it was not until several years later that Mendeleev’s prediction was experimentally confirmed (see Smith Reference Smith1976, 332–35).

Interestingly, Mendeleev highlighted counterpredictions such as his change of the weight of uranium in his later reflections on the periodic table: “Where, then, lies the secret of the special importance which has since been attached to the periodic law?” he asked. “In the first place,” his answer was, “we have the circumstance that, as soon as the law made its appearance, it demanded a revision of many facts which were considered by chemists as fully established by existing experience” (Mendeleev 1889, in Jensen Reference Jensen2005, 167; added emphasis). Here Mendeleev emphasized specifically the guidance provided by the periodic table in the assessment of empirical facts:

In another place, Mendeleev wrote similarly that before the periodic table, there “was only a grouping, a scheme, a subordination to a given fact; while the periodic law furnishes the facts” (Mendeleev 1879, in Jensen Reference Jensen2005, 138; added emphasis). Previous attempts to classify the chemical elements, Mendeleev explained, were hampered “because the facts, and not the law, stood foremost in all attempts” (Mendeleev 1889, in Jensen Reference Jensen2005, 166–67). Doubtlessly, then, Mendeleev attached great weight to counterpredictions.

Mendeleev’s approach contrasted with Lothar Meyer’s, who is often mentioned as the codiscoverer of the periodic table. Before the publication of Mendeleev’s first periodic table in 1869, Meyer published a table of elements in his book Die Modernen Theorien der Chemie (Meyer Reference Meyer1864). Here, Meyer classified the known elements in a main table consisting of 28 elements and two further, smaller tables, containing 16 + 6 elements, respectively. Only in the main table were the elements arranged so that their weight consistently increased from left to right and from top to bottom. Meyer strangely did not at all discuss this aspect of the table, but instead lay his main focus on the differences in atomic weights and did not maintain a consistent application of the weight criterion.Footnote ⁶ Later Meyer would acknowledge explicitly that it was Mendeleev who in 1869 had “emphasized more decisively than it had happened until that point” that the properties of the chemical elements are a periodic function of their atomic weight and that this was the case for all the elements, “including even those with highly uncertain atomic weights” (Meyer Reference Meyer1872, 298).

Only after Mendeleev’s first publication of his periodic table in 1969 did Meyer publish a note in which he sought to stake his claim as codiscoverer of the periodic table, stating that his table was “essentially identical to that given by Mendeleev” (Meyer Reference Meyer1870).Footnote ⁷ Even though Meyer considered the possibility of changes of atomic weights, he was—quite in contrast to Mendeleev—not ready to suggest any changes. As he put it, “It would be rash to change the accepted atomic weights on the basis of so uncertain a starting-point [as the weight ordering criterion of the periodic table]” (ibid.). In the ensuing priority dispute, Mendeleev later granted Meyer an understanding of the “outer meaning of the periodic law,” but did not think that Meyer had “penetrate[ed] its inner meaning” until after Mendeleev’s first publication in 1869 (Mendeleev 1880, in Jensen Reference Jensen2005, 146). This allegation Mendeleev justified by saying that Meyer had only repeated his table in another form and “left underdeveloped those aspects of the subject…which alone could have proven the correctness and universality of the law.” Those aspects included the prediction of the properties of unknown elements and the change in atomic weights of extant elements (ibid.).Footnote ⁸

Meyer was certainly much more cautious than Mendeleev in changing atomic weights. Commenting on his first fragmentary periodic table, Meyer, on the one hand, was confident that “a certain lawfulness governs the numeric values of the atomic weights” but, on the other hand, he also thought it “quite unlikely that it would be as simple as it appears” (Meyer Reference Meyer1864, 139). Although Meyer believed that some of the empirically determined atomic weights would turn out to be wrong, he doubted that all discrepancies could be accounted for in this way. In particular, he criticized as unjustified “arbitrary” corrections and changes of atomic weights (made by Proutians) only “for the sake of a presumed regularity.” He insisted that only experiment could replace any current values (ibid.). In sum, he took it to be a “great danger” to assess and correct empirical results on the basis of any theoretical considerations (ibid.).

What can we learn from this case? As per point (1) of the aforementioned scheme, chemists who recognized atomic weight as a decent ordering criterion, faced a situation of evidential uncertainty in the mid-1860s. Although atomic weight clearly allowed a classification of the chemical elements into groups of similar chemical properties, a number of chemical elements did not want to fit this classification. For chemists like Meyer, who was keen to closely stick to the (apparent) facts, this meant that, for him and others, a coherent classification of all of the known chemical elements was not possible (by point 6). Mendeleev, however, saw in the periodic recurrence of chemical properties within the table more than just a description, namely a law of nature that transcended the apparent facts. The presupposition that this regularity was an exceptionless law then allowed Mendeleev to predict new elements and correct the values of already known ones.Footnote ⁹

Why was Mendeleev so adamant that he had discovered a law of nature, rather than just a regularity describing only a subset of the chemical elements? The answer, I think, has to be sought in the table’s explanatory power. In spite of the fact that Mendeleev believed that the “periodic law” required explanation and that he saw himself incapable of providing such an explanation (Smith Reference Smith1976, 300), there is indeed a sense in which the periodic table explained the properties of the chemical elements: If the chemical properties of elements are determined by their atomic weight and their position in the periodic table, then membership in a particular group in the table explains why an element must have the properties that it does have. To put it in terms of Lange’s recent account of explanation by constraint (Lange Reference Lange2017), one may say that Mendeleev’s table set necessary constraints on the elements, first and foremost the constraint of ascending atomic weights and group membership. On that take, the periodic table explains why element X has chemical properties Y because X could not possibly have had properties Y, had X’s weight been significantly different. Of course, strictly speaking the ascending weight constraint is not in fact necessary, as there are exceptions (see footnote 8), and because the more fundamental ordering criterion is atomic number. But Mendeleev certainly treated the criterion as if it was necessary.

That Mendeleev subscribed to such a minimal notion of explanation is indicated by him also speaking of the chemical elements being “fragmentary, incidental in Nature” prior to the periodic table and that there had been no “special reasons” to expect the discovery of new elements (Mendeleev 1889, in Jensen Reference Jensen2005, 178). The “special reasons” and the properties of chemical elements ceasing to appear “incidental,” I would argue, derived from this minimally explanatory power of the table. Compare: Had the table been merely a description of the facts, there would have been no good reason for Mendeleev to want to change any of the element weights. This is clearly illustrated by the tables produced by all those chemists who did not dare to go beyond the apparent facts and who remained content in finding regularities between those apparent facts. About his precursors Mendeleev complained that “they merely wanted the boldness necessary to place the whole question at such a height that its reflection on the facts could be seen clearly” (Mendeleev 1889, in Jensen Reference Jensen2005, 167). In other words, Mendeleev saw his contribution in elevating the periodicity of the elements to a “law” that had to be respected, even if that required revision of apparently established weights.

In sum, we can conclude that Mendeleev’s periodic table had significant explanatory virtues, as in point (2) of the aforementioned scheme, and Mendeleev was keenly aware of these virtues. Mendeleev decreased his credences in those atomic weights that did not obey his “periodic law,” as in (3), and he took the congruent weights to confirm his “periodic law,” as in (4). This was a major reason for Mendeleev’s successful discovery of the periodic table and Meyer’s (and others’) failure (by point 5–7).

2.2. Watson and Crick’s model of the DNA structure and Franklin’s evidence

The second case I want to highlight is the discovery of the DNA structure. The case is of course well-known in popular culture, not least because of the sexism that Rosalind Franklin was potentially subjected to, by way of Watson and Crick downplaying her contribution to the discovery. I do not want to take any stance toward this controversial question here. Instead, our focus shall lie on the approach that these historical figures chose in deciphering the structure of DNA.

It is well known that Watson and Crick sought to discover the structure of DNA by constructing physical models representing all the relevant stereochemical constraints, such as interatomic distances and angles of the DNA molecules. It is also well known that they made a number of (sometimes embarrassing) mistakes on the way (Judson Reference Judson1996). However, the model-building approach was not the approach Franklin and her colleague Wilkins at King’s college in London chose. Instead, they tried to infer the structure from pictures that they took of the structure of DNA by using x-ray crystallography in which Franklin was an undisputed expert (Schindler Reference Schindler2008; Bolinska Reference Bolinska2018).Footnote ¹⁰ Using a mathematical technique known as Fourier transforms, Franklin sought to reconstruct the structure of the molecules. A massive hurdle to this approach, though, was that the phases of x-rays cannot be reconstructed from x-ray photographs. Franklin had to resort to so-called Patterson functions, which allowed the reconstruction only of intermolecular distances, but not molecule locations in space (see Klug Reference Klug2004; Schindler Reference Schindler2008). Retrospectively, relying on this approach looks rather haphazard, but Franklin made a conscious decision not to use model building. Her PhD student Gosling would later describe her attitude thus: “We are not going to speculate, we are going to wait, we are going to let the spots on this photograph [via the Patterson synthesis] tell us what the structure is” (Gosling, cited in Judson Reference Judson1996, 127).Footnote ¹¹ Similarly, Franklin’s colleague Wilkins relayed an episode in which he encouraged a student by the name of Bruce Fraser to engage in model building: “Rosalind dismissed our excitement [about model-building] by saying that model-building is what you do after you have found the structure” (Wilkins Reference Wilkins2003, 160; added emphasis).

Although Franklin was not keen on model building, she produced some very crucial evidence for the DNA structure with her x-ray crystallographic work. In 1952 she and her student Gosling had discovered that there were two forms of DNA: a “dry,” or “crystalline,” form and a “wet” form (with a water content of more than 75 percent). Before, x-ray photographs had contained mixtures between the two forms, making interpretation difficult. In particular, picture #51 of the B form, which would later also gain popular prominence, provided unequivocal evidence for the structure of DNA being helical. Unequivocal, because the basic X-shaped pattern could be deduced from helical diffraction theory, which Crick was involved in developing (Schindler Reference Schindler2008). Picture #51 also indicated, almost at a glance, the size of the axial repeat and the axial spacing of the helix (Klug Reference Klug1968, 810).Footnote ¹² Franklin accepted that much, but she could not convince herself that the same applied to the dry form as well. Quite the opposite, after she noticed “a very definite asymmetry” in the A form she came to firmly believe that the A form was irreconcilable with a helical structure (ibid., 843). With Gosling, she even wrote a little note announcing the “death of D.N.A helix (crystalline)” (Maddox Reference Maddox2002, 184–85). Even Wilkins, with whom Franklin had a difficult relationship, and their joint colleague Stokes “could see no way round the conclusion that Rosalind had reached after months of careful work” (Wilkins Reference Wilkins2003, 182).

Unfortunately for Franklin, she decided to focus her efforts on the A form, which gave rise to sharper spots on the x-ray photographs and was thus much more amenable to her Patterson synthesis. Franklin’s notebooks show that she was considering various kinds of structures for the A form, such as “sheets, rods made of two chains running in opposite directions…and also a pseudohelical structure…which looked like a figure of eight in projection” (Klug Reference Klug1968, 844). Franklin then tried to accommodate both her antihelical A form and helical B form. Klug comments, “In her notebooks we see her shuttling backwards and forwards between the data for the two forms, applying helical diffraction theory to the B form and trying to fit the Patterson function of the A form” (ibid.). Klug sympathizes with the dilemma Franklin in which found herself: “The stage reached by Franklin at the time is a stage recognizable to many scientific workers, when there are apparently contradictory, or discordant, observations jostling for one’s attention and one does not know which are the clues to select for solving the puzzle” (1968, 844).

Watson and Crick were quite aware of Franklin’s apparently antihelical evidence. But Crick was confident that the apparent asymmetry visible in pictures of the A form resulted from “a small perturbation” in the molecular structure due their close packing in the crystal lattice (Klug Reference Klug1968, 810). Crick later remarked that he had learned from another episode that “it was important not to place too much reliance on any single piece of experimental evidence” and relayed Watson’s “brasher” conclusion according to which “no good model ever accounted for all the facts, since some data was bound to be misleading if not plain wrong. A theory that did fit all the data would have been ‘carpentered’ to do this and would thus be open to suspicion” (Crick Reference Crick1988, 59–60; original emphasis). This sentiment was not only shared by Crick and Watson. Wilkins later admitted that he and Franklin should not have been so perturbed by the antihelical evidence and they instead should have followed admiral Nelson who “won the battle of Copenhagen [in 1801] by putting his blind eye to the telescope so that he did not see the signal to stop fighting” (Wilkins Reference Wilkins2003, 166).

To sum up this case, the DNA researchers in the early 1950s faced a situation of conflicting evidence: Some of the x-ray diffraction pictures spoke for and some against the structure of DNA being helical, as in (1) in the aforementioned scheme. The model developed by Watson and Crick had a number of explanatory virtues (point 2 in the scheme): Most importantly, perhaps, it was internally consistent, as it successfully accommodated all stereochemical constraints, and it was also externally consistent because it accommodated important crystallographic information (such as the repeat and rise of the helix). The model also offered a possible mechanism of how genetic replication might work and set off an incredibly successful research program. In other words, the model was theoretically fertile, and Crick and Watson correctly guessed already in their discovery paper that it might be. Upon seeing the X-shaped picture #51 Watson and Crick knew that the DNA had to be helical. In contrast to their colleagues in London, though, who convinced themselves that the A form could not be helical (by points 5 and 6), Watson and Crick disregarded the apparently antihelical evidence and took their helical model to be confirmed by the B form (by point 3 and 4). This was a crucial factor in Watson and Crick’s success and Franklin’s unsuccessful attempts at reconstructing the structure of DNA (by point 7).

4.1. Direct and indirect strategies

Standard Bayesianism is seemingly blind to explanatory concerns. At the core of Bayesianism lies Bayesian conditionalization (BC), according to which one’s degrees of belief in a proposition h upon learning evidence e is equal to one’s original degrees of belief in h conditional on e. In short, ${P_n}\left( h \right) = {P_o}\left( {h{\rm{|}}e} \right)$ , i.e., the new probability is equivalent to the old probability conditional on the evidence, whereby the conditional probability is determined by Bayes’s theorem: ${P_o}\left( {h{\rm{|}}e} \right) = {{{P_o}(e|h) \times {P_o}\left( h \right)} \over {{P_o}\left( e \right)}}$ . ${P_o}\left( h \right)$ is also known as the “prior,” ${P_o}\left( {h{\rm{|}}e} \right)$ as the “posterior,” and ${P_o}(e|h)$ as the “likelihood” of e on h. Whether h is explanatorily virtuous or not, BC works just the same. However, recently there is what one might call a “new wave” of Bayesian measures of confirmation that have sought to incorporate explanatory concerns. More specifically, Bayesians have sought to reconcile BC with the inference to the best explanation (IBE). There are basically two strategies for achieving reconciliation, which I will refer to as direct and indirect.

The direct strategy awards bonus points to the posteriors of the most explanatory hypothesis. Unfortunately, this turns out to be inconsistent with BC and the axioms of probability, generating “Dutch Book” situations, where agents are bound to accept a series of bets, which individually seem reasonable, but that jointly are guaranteed to result in losses (van Fraassen Reference van Fraassen1989). This seems to be the least appealing strategy, even though there are a handful of philosophers who have argued not only that betting behavior is a wrong model for BC but also that—in computer simulations—explanatory models of belief updating can outperform BC models (Douven and Schupbach Reference Douven and Schupbach2015; Douven Reference Douven, McCain and Poston2017). I will here not further comment on this strategy (see e.g., Pettigrew Reference Pettigrew2021), but if this strategy were successful, it would be quite similar to IBE, and therefore very much in line with ITTA: First check whether the hypotheses are likely conditional on the evidence and then award extra points for explanation.

By far the most popular strategy of reconciling BC with IBE is the indirect strategy. The indirect strategy tries to reconcile IBE with BC by arguing that the posteriors are affected by explanatory concerns boosting the priors and/or the likelihoods in BC (Salmon Reference Salmon1990; Lipton Reference Lipton1991/2004; Okasha Reference Okasha2000; Salmon Reference Salmon2001; Henderson Reference Henderson2013).Footnote ¹⁶ Two varieties of this strategy should be distinguished: Sometimes IBE is viewed as complementing or as “filling holes” left open by BC (Lipton Reference Lipton1991/2004; Okasha Reference Okasha2000). Other times, BC and IBE are presented as fully aligned, and BC as simply explicating IBE in probabilistic terms (Salmon Reference Salmon2001; Henderson Reference Henderson2013). One may refer to this version of the indirect strategy as “reductive.”Footnote ¹⁷ But the outcome of each of the two versions of the indirect strategy is the same. As Henderson puts it succinctly, “If the theory is more plausible, it gets a higher prior; if it is lovelier [i.e., more explanatory], it gets a higher likelihood” (Henderson Reference Henderson2013, 712).

To illustrate the basic idea of the indirect strategy: When assessing whether a patient has COVID-19 or just the flu, a doctor will have certain priors, for example, COVID-19 sometimes involves the loss of smell, whereas influenza does not. Upon hearing about the patient’s symptoms (i.e., the evidence), which involve an increased temperature but also a loss of smell (meaning that the COVID-19 hypothesis is much more likely than the influenza hypothesis), the doctor concludes (calculating her posteriors) that the patient’s symptoms are better explained by COVID-19 than by influenza. Bayesian updating and explanation, so it would seem, go hand in hand.

Even though the indirect strategy of reconciling Bayesianism with explanation at first sight may succeed, there are some general problems. Let us first focus on the priors and then proceed to the likelihoods.

4.1. Explanation and priors

If the priors were the only place in which explanatory concerns could figure in BC, the role of explanation in BC would be rather feeble. This is so because BC usually is sold in tandem with the idea that the priors “wash out” with repeated updating. In fact, the washing out of priors almost seems a prerequisite on any reasonable version of the widely preferred subjectivist version of Bayesianism: Without washing out, the fact that different subjects will set their priors differently would inadvertently result in diverging posteriors for the same evidence. But with the same kind of evidence, we want subjects to converge on similar posteriors, even when they start out in different places. Abandoning the idea that the priors wash out would also make the “problem of priors,” that is the problem how the priors are to be determined, much more pressing, especially for the dominant view of subjective Bayesianism (see e.g., Titelbaum Reference Titelbaum2022).Footnote ¹⁸ So either there is washing out of priors and explanatory concerns are negligible on Bayesianism, or there is no washing out of priors and the Bayesian approach would lose a great deal of its plausibility.Footnote ¹⁹ With regards to ITTA, we can conclude that, if explanatory concerns were to enter the Bayesian calculus via the priors only, their role for confirmation would be negligible indeed. ITTA would seem to remain untouched.

4.2. Explanation and likelihoods

While the idea that explanatorily more appealing theories should result in higher priors seem intuitively plausible (but ultimately problematic), things get more involved with the likelihoods. In its simplest incarnation, though, the idea is intuitive enough: If ${h_1}$ is explanatorily more virtuous than ${h_2}$ , the corresponding likelihoods stand in the following inequality $P\left( {e{\rm{|}}{h_1}} \right) \gt P\left( {e{\rm{|}}{h_2}} \right)$ , mutatis mutandis (see e.g., Okasha Reference Okasha2000). In other words, if ${h_1}$ is explanatorily more appealing than ${h_2}$ , then e is more likely, or less “surprising” on ${h_1}$ than it is on ${h_2}$ . The basic idea has been widely endorsed (Salmon Reference Salmon1990; Lipton Reference Lipton1991/2004; Okasha Reference Okasha2000; Henderson Reference Henderson2013).

The measures proposed for explanatory power can be fairly complex. For example, Schupbach and Sprenger (Reference Schupbach and Sprenger2011) define explanatory power as the degree of expectedness of e given h and, adding some conditions, propose the following measure: $\varepsilon \left( {h,e} \right) = {{P\left( {h{\rm{|}}e} \right) - P(h|\neg e)} \over {P\left( {h{\rm{|}}e} \right) + (h|\neg e)}}$ .Footnote ²⁰ There are several other measures (e.g., McGrew Reference McGrew2003; Myrvold Reference Myrvold2003; Crupi and Tentori Reference Crupi and Tentori2012), but many of them boil down to the aforementioned inequality when used to compare two explanatory hypotheses (Schupbach Reference Schupbach2005, Reference Schupbach, McCain and Poston2017).

Bayesian measures of explanatory power in terms of likelihoods have been critiqued by Glymour (Reference Glymour2015) and Lange (Reference Lange2022a, Reference Lange2022b). The upshot of their criticism is that higher explanatory power is not necessarily reflected in higher likelihoods or priors.Footnote ²¹ For example, Newtonian mechanics is strictly speaking false, its prior accordingly zero, and its likelihood therefore undefined, despite its unquestionably high explanatory power (Glymour Reference Glymour2015), and different explanations may have the same likelihood because they all deductively entail the evidence (Lange Reference Lange2022a). What is more, there seems nothing in the New Wave Bayesian measures of explanation that would prevent any nonexplanatory theory to have as high a likelihood as an explanatorily highly virtuous theory. But that would mean that Bayesian measures of explanation are rather limited indeed for modeling real theory choice scenarios.

4.3. Bayesianism and cases of evidential uncertainty

Regardless of the aforementioned general concerns about Bayesians’ attempts to incorporate explanatory power into their measures, let us see whether Bayesians can accommodate the cases that I discussed in section 2.

Standard Bayesianism implies a strongly foundationalist epistemology, in which we are certain about the evidence (see e.g., Weisberg Reference Weisberg2009a). This is of course incompatible with cases such the ones discussed here are cases in which there was considerable uncertainty about the evidence. But Bayesians have found a straightforward way for modeling evidential uncertainty, also known as Jeffrey conditionalization:

$${P_n}\left( h \right) = {P_o}\left( {h{\rm{|}}e} \right) \times {P_n}\left( e \right) + {P_o}(h|\neg e) \times {P_n}\left( {\neg e} \right),$$

where ${P_o}\left( h \right)$ represents the prior of h before new information about the evidence is received and ${P_n}\left( h \right)$ the new probability of h after this information has been received. ${P_n}\left( h \right)$ is then the sum of the old conditional probabilities ${P_o}\left( {h{\rm{|}}e} \right)$ and ${P_o}(h|\neg e)$ , each weighted with the degrees of belief in $e$ occurring or not occurring, namely ${P_n}\left( e \right)$ and ${P_n}\left( {\neg e} \right)$ , respectively.

Now, in situations of evidential conflict, where both ${P_n}\left( {\neg e} \right)$ and ${P_n}\left( e \right)$ are $ \gt 0$ , it is not at all clear whether the posterior ${P_n}\left( {h{\rm{|}}e} \right)\;$ should be $ \lt $ or $ \gt .5$ . Bayesians should therefore recommend the suspension of judgment—independently of whether they believe that explanatory power be manifested in a theory’s likelihood or not. Although scientist group F seemed to follow this recommendation, group G decided to decrease their credence in ${P_n}\left( {\neg e} \right)$ . According to MuSTA, group G was justified in doing so: Theories that explain at least some of the evidence in a highly satisfying and revelatory way may cast doubt on evidence that is in apparent conflict with the theory. In Bayesian terms, explanatory theories may decrease credence in the data inconsistent with the theory, namely ${P_n}\left( {\neg e} \right)$ .

Suppose now that you are a confirmational holist and you think my historical cases can easily be accommodated by allowing beliefs about theories to affect beliefs about the evidence (but see my reply to objection 4 in the previous section). Could you give us a convincing Bayesian rendering of my cases? Strevens (Reference Strevens2001) has argued that the Duhem-Quine problem—which has it that hypotheses are never confirmed or disconfirmed in isolation, but only in conjunction with other assumptions—can be solved within the Bayesian framework. In particular, Strevens derives the conclusion that the higher one’s prior probability of a hypothesis h, the less h will be blamed when the conjunction of h and an auxiliary a is refuted by experiment, and that the magnitude of the impact of e on h is greater the higher the prior probability of a. True, scientists in my cases had high priors in their theories when dismissing apparent counterevidence, for which they had low priors, but Strevens gives no guidance as to when and why such scenarios arise and when it would be justified for scientists to have high priors for their theories and low priors for their auxiliaries. I have argued that the reason why group G scientists opted for the giving more weight to their theories than to the auxiliaries supporting the negative evidence is that they were guided by the explanatory power of their theories, whereas group F scientists were not. The Duhemian Bayesian à la Strevens could of course try to accommodate our cases by modeling explanatory power in terms of higher priors, but, as we have seen, this will not be a satisfactory solution either, at least not in a fully coherent Bayesian account.

Bayesianism may in fact be altogether incompatible with confirmational holism. In a seminal paper, Weisberg (Reference Weisberg2009a) has shown that Bayesianism cannot simultaneously satisfy both holism and commutativity, where the former is understood as belief revision in the light of changing background beliefs.Footnote ²² This characterization of confirmational holism in fact fits the bill very well in my cases: Mendeleev’s periodic law and Crick and Watson’s DNA model had scientists change their background beliefs about the relevant experiments, so that beliefs about the evidence changed. What is more, Weisberg has even argued that holism is incompatible with the two standard forms of Bayesian conditionalization (“strict” and Jeffrey), as both require “rigidity” of conditional probabilities on the evidence, namely that ${P_n}\left( {h{\rm{|}}e} \right) = {P_o}\left( {h{\rm{|}}e} \right)$ . Attempts to address Weisberg’s challenge have resulted in the abandonment of both of these standard forms of conditionalization (Gallow Reference Gallow2014). Even if Bayesianism was reconcilable with holism in some way, nothing would as yet have been said about the role of explanation in guiding researchers in cases of evidential uncertainty. It is thus not clear whether Bayesians can model MuSTA at all.