I am grateful for the chance to comment on the paper by Gelman and Robert. I welcome seeing statisticians raise philosophical issues about statistical methods, and I entirely agree that methods not only should be applicable but also capable of being defended at a foundational level. “It is doubtful that even the most rabid anti-Bayesian of 2010 would claim that Bayesian inference cannot apply” (Gelman and Robert 2012, p. 6). This is clearly correct; in fact, it is not far off the mark to say that the majority of statistical applications nowadays are placed under the Bayesian umbrella, even though the goals and interpretations found there are extremely varied. There are a plethora of international societies, journals, post-docs, and prizes with “Bayesian” in their name, and a wealth of impressive new Bayesian textbooks and software is available. Even before the latest technical advances and the rise of “objective” Bayesian methods, leading statisticians were calling for eclecticism (e.g., Cox 1978), and most will claim to use a smattering of Bayesian and non-Bayesian methods, as appropriate. George Casella (to whom their paper is dedicated) and Roger Berger in their superb textbook (2002) exemplify a balanced approach.
What about the issue of the foundational defense of Bayesianism? That is the main subject of these comments. Whereas many practitioners see the “rising use of Bayesian methods in applied statistical work” as being in support of a corresponding Bayesian philosophy, Gelman and Shalizi (2012) declare that “most of the standard philosophy of Bayes is wrong” (p. 2). The widespread use of Bayesian methods does not underwrite the classic subjective inductive philosophy that Gelman associates (correctly) with the description of Bayesianism found on Wikipedia: “Our key departure from the mainstream Bayesian view (as expressed, for example, [in Wikipedia]) is that we do not attempt to assign posterior probabilities to models or to select or average over them using posterior probabilities. Instead, we use predictive checks to compare models to data and use the information thus learned about anomalies to motivate model improvements.” (p. 71).
From the standpoint of this departure, Gelman and Robert defend their Bayesian approach against Feller’s view “that Bayesian methods are absurd—not merely misguided but obviously wrong in principle” (p. 2).
Given that Bayesian methods have inundated all teaching and applications, a reader might at first be puzzled by the authors’ choice to consider Feller’s 1950 introduction to probability, the text of which gives a page or two to “Bayes Rule.” Noting that “before the ascendance of the modern theory, the notion of equal probabilities was often used as synonymous for ‘no advance knowledge,’” Feller questions the “ ‘law of succession of Laplace’ connected with this” (Feller 1950, pp. 124-125 of the 1970 edition). The authors readily concede: “[I]t would be accurate, we believe, to refer to Bayesian inference as being an undeveloped subfield in statistics at that time, with Feller being one of the many academics who were aware of some of the weaker Bayesian ideas but not of the good stuff” (p. 4).
Yet the authors have a deeper reason to examine Feller. As they reiterate, what strikes them “about Feller’s statement was not so much his stance as his apparent certainty” (p. 3). They “doubt that Feller came to his own considered judgment about the relevance of Bayesian inference…. Rather, we suspect that it was from discussions with one or more statistician colleagues that he drew his strong opinions about the relative merits of different statistical philosophies” (p. 6).
Whether or not their suspicion of Feller is correct, they have identified a common tendency in foundational discussions of statistics simply to be swayed by colleagues and oft-repeated criticisms, rather than arriving at one’s own considered conclusion. Also to their credit, their defense is not “defensive.” Indeed, in some ways they raise stronger criticisms of Bayesian standpoints than Feller himself:
In the last half of the twentieth century, Bayesians had the reputation (perhaps deserved) of being philosophers who were all too willing to make broad claims about rationality, with optimality theorems that were ultimately built upon questionable assumptions of subjective probability, in a denial of the garbage-in-garbage-out principle, thus defying all common sense. In opposition to this nonsense, Feller (and others of his time) favored a mixture of Fisher’s rugged empiricism and the rigorous Neyman-Pearson theory, which “may be not only defended but also applied.” (p. 17)
Perhaps Bayesians have gotten over the reputation cited by the authors of “being philosophers who were all too willing to make broad claims about rationality,” but, by and large, philosophers have not. I regard the most important message of their paper as being a call for a change from all players (p. 15).
2. Probabilism in contrast to sampling theory standpoints
Tellingly, the authors begin their article by observing that “[y]ounger readers of this journal may not be fully aware of the passionate battles over Bayesian inference among statisticians in the last half of the twentieth century” (p. 2). They are undoubtedly correct, and that alone attests to the predominance of Bayesian methods and pro-Bayesian arguments in statistics courses. By contrast, few readers are unaware of the litany of criticisms repeatedly raised regarding statistical significance tests, confidence intervals, and the frequentist sampling-theory justifications for these tools. We heartily share their sentiment:
At the very least, we hope Feller’s example will make us wary of relying on the advice of colleagues to criticize ideas we do not fully understand. New ideas by their nature are often expressed awkwardly and with mistakes—but finding such mistakes can be an occasion for modifying and improving these ideas rather than rejecting them. (p. 17)
The construal of Neyman-Pearson statistics that is so widely lampooned reflects Neyman and Pearson’s very early attempt to develop a formalism that would capture the Fisherian and other methods used at the time. As Pearson remarks in his response to Fisher’s (1955) criticisms: “Indeed, from the start we shared Professor Fisher’s view that in scientific enquiry, a statistical test is ‘a means of learning’” (Pearson 1955, 206).
Underlying one of the philosophers’ examples Gelman and Robert discuss (the doomsday argument) “is the ultimate triumph of the idea, beloved among Bayesian educators, that our students and clients don’t really understand Neyman-Pearson confidence intervals and inevitably give them the intuitive Bayesian interpretation.” The idea “beloved among Bayesian educators” does not merely assert that probability should enter to provide posterior probabilities—an assumption we may call probabilism– it assumes that the frequentist error statistician also shares this goal. Thus, whenever error probabilities, be they p-values or confidence levels, disagree with a favored Bayesian posterior, this is alleged to show that frequentist methods are self-contradictory, and thus unsound.
For example, the fact that a frequentist p-value can differ from a Bayesian posterior (in two-sided testing, assuming one or another prior) has been regarded as showing that p-values overestimate the evidence against a (point) null (e.g., Berger 2003). That a sufficiently large sample size can result in rejecting a null deemed plausible by a Bayesian is thought to show the logical unsoundness of significance testers (Howson 1997a, 1997b).[i] Assuming that confidence levels are to give posterior probabilities to the resulting interval estimate, Jose Bernardo declares that non-Bayesians “should be subject to some re-education using well known, standard counter-examples such as the fact that conventional 0.95-confidence regions may actually consist of the whole real line” (2008, 453). The situation with all of these alleged “counterexamples” looks very different when error probabilities associated with methods are employed in order to indicate the parameter values that are or are not well indicated by the data (e.g., Mayo 2003, 2005, 2010). Error probabilities are not posteriors, but refer to the distribution of a statistic d(X)—the so-called sampling distribution (hence the term sampling theory). Admittedly, this alone is often claimed to be at odds with mainstream (at least subjective) Bayesian methods where consideration of outcomes other than the one observed is disallowed (i.e., the likelihood principle [LP]), at least once the data are available. In Jay Kadane’s recent text: “Neyman-Pearson hypothesis testing violates the likelihood principle, because the event either happens or does not; and hence has probability one or zero” (Kadane 2011, 439).
It often goes unrecognized that criticisms of frequentist statistical methods assume a certain philosophy about statistical inference (probabilism), and often allege that error-statistical methods can achieve only radical behavioristic goals, wherein only long-run error rates matter. Feller, in declaring that “the modern method of statistical tests and estimation is less intuitive but more realistic,” also reveals the common tendency to assume a philosophy of probabilism (Feller 1950, pp. 124-125 of the 1970 edition). Our own intuitions go in a different direction: what is intuitively required are ways to quantify how well tested claims are, and how precisely and accurately they are indicated. Still, we admit that good error probabilities while necessary, do not automatically suffice to satisfy the goal of capturing the well-testedness of inferences.
However, when we try to block the unintuitive inferences, for example, by conditioning on error properties that are relevant for assessing well-testedness, “there is a catch” (Ghosh, Delampady, and Semanta 2006, 38): we seem to be led toward violating other familiar frequentist principles (sufficiency, weak conditionality), at least according to a famous argument (by Allan Birnbaum in 1962). Once again, critics place us in a self-contradictory position, but we argue that the frequentist is simply presented with a false dilemma, and that “the ‘dilemma’ argument is therefore an illusion” (Cox and Mayo 2010).
While the text by Gelman et al. (2003) is a noteworthy exception, it is standard for texts to list, in addition to the above “counterexamples,” an assortment of classic fallacies (conflating statistical and substantive significance, fallacies of insignificant results, fallacies of rejection), which, to echo the authors’ point about Feller, stem from often-heard strong opinions of frequentist methods, overlooking how frequentists have responded. The current situation in statistical foundations may present an opportunity to reconsider them, free of the traditional frameworks both of Bayesian and frequentist statistics. The appeal to a testing notion may also be relevant to justify the Bayesian account that Gelman and Robert advance.
3. A Testing Defense for Bayesianism?
The authors correctly suspect that what has bothered mathematicians such as Feller comes from assuming “that Bayesians actually seem to believe their assumptions rather than merely treating them as counters in a mathematical game. . . . [T]his interpretation may be common among probabilists, whereas we see applied statisticians as considering both prior and data models as assumptions to be valued for their use in the construction of effective statistical inferences” (p. 8).
Rather than believing their assumptions, the authors suggest that they test them:
[W]e make strong assumptions and use subjective knowledge in order to make inferences and predictions that can be tested by comparing to observed and new data (see Gelman and Shalizi, 2012, or Mayo, 1996 for a similar attitude coming from a non-Bayesian direction). (p. 9)
So perhaps some kind of a “non-Bayesian checking of Bayesian models” (Gelman and Shalizi 2012, 11) would offer more promise than attempts at a reconciliation of Bayesian and frequentist ideas by way of long-run performance properties.
To pursue such an avenue, one still must reckon with a fundamental issue at the foundations of Bayesian method: the interpretation of and justification for the prior probability distribution, the use of which is arguably what distinguishes it from frequentist error statistics. To their credit, the authors concede “that many Bayesians over the years have muddied the waters by describing parameters as random rather than fixed. Once again, for Bayesians as much as for any other statistician, parameters are (typically) fixed but unknown. It is the knowledge about these unknowns that Bayesians model as random” (pp. 15-16).
Although many illustrations enable an intuitive grasp of what they seem to have in mind, viewing the knowledge of fixed unknowns as random, if it is to sit at the foundations, calls for explication. The authors are right to observe that most statisticians are comfortable with probability models:
Bayesians will go the next step and assign a probability distribution to a parameter that one could not possibly imagine to have been generated by a random process, parameters such as the coefficient of party identification in a regression on vote choice, or the overdispersion in a network model, or Hubble’s constant in cosmology. There is no inconsistency in this opposition once one realizes that priors are not reflections of a hidden “truth” but rather evaluations of the modeler’s uncertainty about the parameter. (pp. 9-10; emphasis mine)
But it is precisely the introduction of “the modeler’s uncertainty about the parameter” that is so much at the heart of questions involving the understanding and justification of Bayesian methods. It would be illuminating to hear the authors’ take on the different conceptions of and debates about this “modeler’s uncertainty” about a parameter. Arguably, the predominant uses of Bayesian methods come from those who advocate “objective” or “default” or “reference” priors (we use the neutral term “conventional” Bayesians, but any preferred term will do). Yet contemporary conventional Bayesians have worked assiduously to develop priors that are not supposed to be considered expressions of uncertainty, ignorance, or degree of belief; they are “mathematical concepts” of some sort used to obtain posterior probabilities. While subjective Bayesians urge us to incorporate background information into the analysis of a given set of data by means of a prior probability on alternative hypotheses (perhaps attained through elicitations of degrees of belief), some of the most influential Bayesian methods in practice invite us to employ conventional priors that have the most minimal influence on resulting inferences, letting the data dominate. Conventional priors, unlike what might be expected from measures of initial uncertainty in parameters, are model-dependent, leading to Bayesian incoherence, “leading to violations of basic principles, such as the likelihood principle and the stopping rule principle” (Berger 2006, 394). Even within the conventional Bayesian school, there are many from which to choose: priors based on the asymptotic model-averaged information differences (between the prior and the posterior); matching priors that yield optimal frequentist methods, and others besides (Berger 2006; Kass and Wasserman 1996). Cox (2006) summarizes some of the concerns he has often articulated:
[T]he prior distribution for a particular parameter may well depend on which is the parameter of primary interest or even on the order in which a set of nuisance parameters is considered. Further, the simple dependence of the posterior on the data only via the likelihood regardless of the probability model is lost. If the prior is only a formal device and not to be interpreted as a probability, what interpretation is justified for the posterior as an adequate summary of information. (p.77).
Bayesian testing seems to be in a state of flux. The authors’ invitation to test Bayesian models, including priors, is welcome; but the results of testing are clearly going to depend on explicating the intended interpretation of whatever is being tested.
Elsewhere it is suggested that there need not be a uniquely correct conventional nor subjective prior, it may be a “combination of the prior distribution and the likelihood, each of which represents some compromise among scientific knowledge, mathematical convenience, and computational tractability” (Gelman and Shalizi 13). (Without presuming Robert concurs, we assume the authors endorse some latitude in interpreting priors.) There is no problem with the prior serving many functions, so long as its particular role is pinned down for the case at hand (Mayo 2013). These authors correctly argue that the assumptions of the likelihood are also just that—assumptions–but we still need to understand what is being represented. If the prior and likelihood is regarded as a holistic model, it is still possible to test for adequacy; but to pinpoint the source of any misfits would seem to require more.
Finally, if we agree with these authors that they key goal is “to make inferences and predictions that can be tested by comparing to observed and new data,” we need a notion of adequate/inadequate tests. A basic intuition is that a test have a good capacity, or at least some capability, of detecting inadequacies and flaws in whatever is being tested. The philosophy of statistics we favor employs frequentist error probabilities to appraise and ensure the probative capacity, or severity, of tests, being sensitive to the actual data and claim to be inferred. Admittedly, in developing this statistical philosophy, mistakes and shortcomings in the typical behavioristic construal of frequentist methods were used as “an occasion for modifying and improving these ideas rather than rejecting them”, to echo these authors. Possibly this can offer a non-traditional avenue for a philosophical defense of the Bayesian testing these authors advance.
4. Concluding remarks
Bayesian methods are widely applied, but when the discussion turns to foundations there is some question as to whether the success stories are properly credited to mainstream philosophical subjective Bayesianism. Gelman and Robert, if we understand them, deny this. Failure to consider an alternative defense for widely used Bayesian methods is at the heart of criticisms that continue. Stephen Senn (2011, p.58) calls attention to: “A very standard form of argument … frequently encountered in many applied Bayesian papers where the first paragraphs laud the Bayesian approach on various grounds, in particular its ability to synthesize all sources of information”, and in the rest of the paper the authors engage in non-Bayesian inexplicit reasoning. The objection loses its force, if some non-standard or even non-Bayesian defense is involved, but that is something that requires development. We do not deny there is an epistemological foundation for the authors’ Bayesian approach, only that the foundations for Bayesian testing is in some flux and deserves attention.
Our take-home message in a nutshell is this: contemporary Bayesianism is in need of new foundations; whether they are to be found in non-Bayesian testing, or elsewhere. Hopefully philosophers of probability will turn their attention to these tantalizing problems of statistics. In contrast to the heady golden era of philosophy of statistics of 25 or 40 years ago, contemporary philosophers of science are far more focused on probability than statistics. While some of the issues have trickled down to the philosophers, by and large we see ‘formal epistemology’ assuming the traditional justifications for probabilism that are being questioned by contemporary statisticians, Bayesian and non-Bayesian. Gelman and Robert are among the philosophically-minded statisticians who are taking the lead[ii]. As practitioners, it suffices that their methods are useful and widely applied; we philosophical under laborers should be helping to make explicit underlying philosophical defenses.
*Some very small editorial corrections are missing from what was first posted (e.g., it’s their paper, and not the whole issue that is dedicated to Cassella). Elbians will correct and update this.
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