Costa, T. (2026). The Bayesian audit: Evaluating the proportionality of scientific claims to evidence—a case study on social priming and walking speed. Frontiers in Psychology, 17, 1799078. DOI: 10.3389/fpsyg.2026.1799078


This article applies Bayes’ theorem to one conveniently selected t value and calls the result a ‘Bayesian audit.’ Most readers may simply ignore it because it appeared in Frontiers in Psychology. Those who want a more substantive reason can point to this review.

Costa (2026) introduces a “Bayesian audit,” a six-step framework intended to evaluate whether the strength of scientific claims is proportional to the evidence supporting them. The idea is sensible. Statistical significance does not tell us how strongly we should believe a scientific claim, and surprising claims based on weak evidence deserve particularly careful scrutiny. Costa illustrates the proposed method with one of social psychology’s most famous findings: Bargh, Chen, and Burrows’s (1996) claim that priming college students with words related to old age caused them to walk more slowly afterward.

Unfortunately, the audit itself is problematic. It misrepresents important features of the original study, considers only a fraction of the available evidence, and reduces a question about the magnitude and robustness of an effect to a comparison between a null and an inadequately specified alternative hypothesis.

The first problem is surprisingly basic. Costa describes the original finding as based on a study with approximately t(28) = 2.0 and p ≈ .05. But Bargh et al. actually reported two elderly-priming experiments. In Experiment 2a, the comparison was t(28) = 2.86, p < .01. They then conducted Experiment 2b as a replication and again reported slower walking, t(28) = 2.16, p < .05. Costa appears to approximate the weaker second result while failing to mention the stronger first result or even that the original article contained two studies.

That is an odd starting point for an audit. If the purpose is to reconstruct how much evidence supported the claim in 1996, both original studies should be included.

Costa also incorrectly describes participants as being “subliminally exposed to words related to old age.” They were not. Participants consciously read words while completing a scrambled-sentence task. The claimed unconscious component was that participants supposedly did not realize that the elderly-related words subsequently affected their walking. Bargh et al. themselves explicitly distinguished this procedure from subliminal priming; Experiment 3 of their paper used genuinely subliminal presentation of faces.

This distinction matters because Costa uses the apparent implausibility of unconscious effects on motor behavior to motivate skeptical prior probabilities. One should at least characterize the causal claim correctly before assigning a prior to it.

The treatment of replication evidence is even more problematic.

Costa cites Doyen et al. (2012) and Harris et al. (2013) as subsequent replication attempts. Doyen et al. did replicate the elderly-walking paradigm. In a substantially larger study using automated measurement, they found essentially no priming effect. Their second experiment further suggested that experimenter expectations could influence the result.

Harris et al. (2013), however, did not replicate elderly priming at all. They attempted to replicate Bargh et al.’s 2001 high-performance goal-priming experiments, in which achievement words were supposed to improve performance on a cognitive task. Calling Harris et al. a replication of the elderly-walking finding is simply an error.

More importantly, why is a Bayesian audit conducted in 2026 based primarily on one t statistic from 1996?

There is now a substantial literature on behavioral priming. Dai et al. (2023), for example, meta-analyzed 351 studies and 862 effect sizes and concluded that behavioral priming effects could be detected across a large literature. Conversely, Mac Giolla et al. (2024) examined 70 close replication attempts of 49 social-priming findings. Ninety-four percent produced smaller effects than the originals, only 17% were significant in the predicted direction, and among 52 replications conducted without an original author, none was significant in the original direction; the pooled effect for those independent replications was essentially zero.

These sources do not necessarily settle the question. Meta-analyses themselves can be distorted by publication bias and other forms of selection. But that is precisely why an audit should examine them critically. An audit of a 30-year-old scientific claim should evaluate the accumulated evidence, not simply convert one selected original result into a Bayes factor.

There is an even more fundamental problem with the statistical question Costa asks.

Costa assigns prior probabilities of .05, .10, and .20 to the alternative hypothesis and combines these with an estimated Bayes factor of approximately 3. This yields posterior probabilities of .14, .25, and .43, respectively. The arithmetic is straightforward. The interpretation is not.

Why should the prior probability that the effect exists be .05 or .10?

Costa acknowledges that these values are illustrative rather than derived from an elicitation procedure. But these priors largely determine the conclusion that posterior belief remains low. Starting with a 5% probability and multiplying the prior odds by a Bayes factor of 3 inevitably produces a low posterior probability.

More importantly, what exactly is the hypothesis whose prior probability is 5%?

There is a major difference between these propositions:

elderly-related words have exactly zero effect on walking speed;

elderly-related words have some nonzero effect;

elderly-related words have a psychologically meaningful effect;

elderly priming produces effects of the magnitude originally reported;

automatic stereotype activation reliably produces consequential behavioral changes.

These are not the same hypothesis.

The scientifically interesting issue today is probably not whether the population effect is exactly zero. The effect could be d = .05 or d = .10. Such an effect would make the point null hypothesis technically false while providing little support for the dramatic theoretical interpretation of the original experiments.

This is why effect sizes matter. Bargh et al.’s original studies implied very large effects. Subsequent evidence raises the possibility that the true effect, if it exists at all, is much smaller. A useful audit therefore needs to ask how large the effect is and how precisely it has been estimated—not merely whether H0 or H1 receives the larger Bayes factor.

Costa’s procedure also conflates two different kinds of priors. One is the prior model probability: how likely H1 is relative to H0 before seeing the data. The other is the prior distribution over possible effect sizes within H1. A Bayes factor for a composite alternative necessarily depends on the latter. Yet the article emphasizes sensitivity to prior model probabilities while giving much less attention to the effect-size assumptions used to obtain BF₁₀ ≈ 3.

This creates another problem with Costa’s distinction between “evidence” and “belief.” He describes the Bayes factor as quantifying evidence supplied by the data and posterior probability as combining this evidence with prior belief. But a Bayes factor is not simply a property of the observed data. It depends on the statistical models being compared, including the distribution of effect sizes assumed under the alternative hypothesis.

There is also an internal inconsistency in the treatment of the replication evidence. Costa states that the later replication attempts yielded Bayes factors close to 1 and therefore had little evidential impact. That makes sense: a Bayes factor of 1 leaves prior odds unchanged. Yet the subsequent synthesis says that posterior belief “collapses under replication.” It cannot do both. Replications with BF ≈ 1 cannot cause posterior belief to collapse. To demonstrate such a decline, one would need Bayes factors favoring the null or another competing model and then accumulate this evidence formally.

Publication bias is another conspicuous omission. The article is motivated by the replication crisis and explicitly acknowledges that biased data limit the usefulness of evidential measures. Yet the actual Bayesian calculation treats the published Bargh result as though it were an observation selected independently of statistical significance.

That is unrealistic. A BF of 3 obtained from a randomly selected study and a BF of 3 obtained from a literature in which statistically significant and theoretically exciting findings were preferentially published do not have the same evidential implications. If selection contributed to the replication crisis, an audit of the original published evidence needs to take selection seriously.

Costa also describes the original study’s low statistical power as an additional reason for skepticism. Low power certainly matters because significant results from low-powered studies tend to exaggerate effect sizes, particularly in a selected literature. But sample size has already entered the likelihood used to compute the Bayes factor. Low power is therefore not independent evidence against the hypothesis. The additional concern arises from selection, analytic flexibility, measurement error, and effect-size inflation.

The deeper problem is that Costa reduces a scientific question to H0 versus H1 when several competing explanations exist. Doyen et al.’s work raised experimenter expectancy as one possible explanation. Other possibilities include a genuinely small priming effect, effects restricted to particular conditions or individuals, procedural artifacts, or some combination of these mechanisms. A Bayes factor contrasting an exact-zero model with a generic nonzero-effect model cannot determine which causal explanation is correct.

This is especially important because rejecting H0 would not establish Bargh’s theory. Even convincing evidence for a tiny difference in walking speed would not demonstrate that automatic stereotype activation generally controls overt behavior.

The Bayesian audit is therefore based on a reasonable principle but a poor demonstration. Scientific claims should indeed be proportional to evidence. The problem is that assessing proportionality requires accurately identifying the original evidence, considering the accumulated replication literature, evaluating publication bias, distinguishing statistical from substantive hypotheses, and estimating plausible effect sizes and their uncertainty.

Ironically, the elderly-priming case illustrates the weakness of Costa’s audit more effectively than it illustrates its strengths. A proper audit should not ask merely whether one selected t statistic changes the odds that an effect is exactly zero. It should ask what three decades of evidence tell us about the magnitude, robustness, boundary conditions, and causal interpretation of the phenomenon.

On those questions, uncertainty remains. There may be a small elderly-priming effect. The evidence does not establish that the effect is exactly zero. But neither does the accumulated evidence support taking the spectacular effects reported in 1996 at face value. The important scientific task is to estimate what effect remains after accounting for uncertainty and bias. That requires more than Bayes’ theorem applied to one conveniently chosen t value.