D. Mayo & D. Hand: “Statistical significance and its critics: practicing damaging science, or damaging scientific practice?”



Prof. Deborah Mayo, Emerita
Department of Philosophy
Virginia Tech


Prof. David Hand
Department of Mathematics Statistics
Imperial College London

Statistical significance and its critics: practicing damaging science, or damaging scientific practice?  (Synthese)

[pdf of full paper.]

Abstract: While the common procedure of statistical significance testing and its accompanying concept of p-values have long been surrounded by controversy, renewed concern has been triggered by the replication crisis in science. Many blame statistical significance tests themselves, and some regard them as sufficiently damaging to scientific practice as to warrant being abandoned. We take a contrary position, arguing that the central criticisms arise from misunderstanding and misusing the statistical tools, and that in fact the purported remedies themselves risk damaging science. We argue that banning the use of p-value thresholds in interpreting data does not diminish but rather exacerbates data-dredging and biasing selection effects. If an account cannot specify outcomes that will not be allowed to count as evidence for a claim-if all thresholds outcomes that will not be allowed to count as evidence for a claim- if all thresholds are abandoned-then there is no test of that claim. The contributions of this paper are: To explain the rival statistical philosophies underlying the ongoing controversy; To elucidate and reinterpret statistical significance tests, and explain how this reinterpretation ameliorates common misuses and misinterpretations; To argue why recent recommendations to replace, abandon, or retire statistical significance undermine a central function of statistics in science: to test whether observed patterns in the data are genuine or due to background variability

Keywords: Data-dredging · Error probabilities · Fisher · Neyman and Pearson . P-values · Statistical significance tests

Introduction and background

While the common procedure of statistical significance testing and its accompanying concept of p-values have long been surrounded by controversy, renewed concern has been triggered by the so-called replication crisis in some scientific fields. In those fields, many results that had been found statistically significant are not found to be so (or have smaller effect sizes) when an independent group tries to replicate them. This has led many to blame the statistical significance tests themselves, and some view the use of p-value thresholds as sufficiently damaging to scientific practice as to warrant being abandoned. We take a contrary position, arguing that the central criticisms arise from misunderstanding and misusing the statistical tools, and that in fact the purported remedies themselves risk damaging science. In our view, if an account cannot specify remedies themselves risk damaging science. In our view, if an account cannot specify are abandoned-then there is no test of that claim.


The goals of our paper are:

  • To explain the key issues in the ongoing controversy surrounding statistical significance tests;
  • To reinterpret statistical significance tests, and the use of p-values, and explain how this reinterpretation ameliorates common misuses that underlie criticisms of these methods;
  • To show that underlying many criticisms of statistical significance tests, and especially proposed alternatives, are often controversial philosophical presuppositions about statistical evidence and inference;
  • To argue that recommendations to replace, abandon, or retire statistical significance tests are damaging to scientific practice.

Section 2 sets out the main features of statistical significance tests, emphasizing aspects that are routinely misunderstood, especially by their critics. In Sects. 3 and 4 we will flesh out, and respond to, what seem to be the strongest arguments in support of the view that current uses of statistical significance tests are damaging to science. Section 3 explores five key mistaken interpretations of p-values, how these can lead to damaging science, and how to avoid them. In Sect. 4 we discuss and respond to central criticisms of p-values that arise from presupposing alternative philosophies of evidence and inference. In Sect. 5 we argue that calls to replace, abandon, or retire statistical significance tests are damaging to scientific practice. We argue that the “no threshold” view does not diminish but rather exacerbates data-dredging and biasing selection effects (Sect. 5.1), and undermines a central function of statistics in science: to test whether observed patterns in the data can be explained by chance variation or not (Sect. 5.2). Section 5.3 shows why specific recommendations to retire, replace, or abandon statistical significance yield unsatisfactory tools for answering the significance tester’s question. Finally, in Sect. 6 we pull together the main threads of the discussion, and consider some implications for evaluating statistical methods with integrity.

You can read the rest on line.

Other papers in the Special Topic: Recent Issues in Philosophy of Statistics: Evidence, Testing, and Applications (so far), are here.

We welcome your constructive comments!

Categories: Error Statistics | Leave a comment

Paul Daniell & Yu-li Ko commentaries on Mayo’s ConBio Editorial

I had been posting commentaries daily from January 6, 2022 (on my editorial “The Statistics Wars and Intellectual conflicts of Interest”, Conservation Biology) until Sir David Cox died on January 18, at which point I switched to some memorial items. These two commentaries from what Daniell calls my ‘birthday festschrift’ were left out, and I put them up now. (Links to others are below.)



Paul Daniell 
Ph.D student
Department of Philosophy, Logic & Scientific Method
London School of Economics & Political Science


Conflict, Analogy, and Deprojection
In the spirit of a birthday Festschrift for Prof. Deborah G. Mayo

Since I am about to comment upon an editorial on statistical methods in Conservation Biology, I will begin at the natural point-of-departure: Virgil’s Aeneid. This comment is only half tongue-in-cheek. Ostensibly, the story of the Aeneid is the story of a man who flees Troy to become the ancestor to the earliest Romans. But what it is, really, is a meditation on the nature of conflict and war. Indeed, its most controversial phrase to translate are its three first words

Arma virumque cano.

Robert Fagles  came under fire when he chose to translate those three words

Wars and a man I sing

rather than its practically canonical English translation, made famous by the 17th century English poet, John Dryden

Of arms and the man I sing.

The meditation, especially starting in Book 7, concerns whether war is the inevitable consequence of human vanity or whether it is the result of the petty grievances of the gods. Either way, the conclusion appears to be that conflict is just part of human lives.

Of course, today, it is not scientifically respectable to wonder whether the gods are responsible for our conflicts concerning Bayesianism and frequentism (or even within frequentism which p-value constitutes a statistically significant figure). Prof. Mayo’s bold suggestion is that editors avoid this conflict by not taking sides. She argues that by taking sides, editors encourage the misuse of data analysis. When combined with the fact that scientists must publish in order to maintain and advance their careers, what results is experimental design which encourages the cherry picking of data and other selection malfeasance. Editors should remain islands, neutral Switzerlands landlocked in wartime.

Of course, this appears to conflict with Virgil’s apparent view that hostility and dispute are preordained as is taking sides, whether a Latin like Turnus or a Trojan like Aeneas. Let me provide some counterpoint to Professor Mayo’s contention that editors should not take sides.

The first point is perhaps partly anecdotal. My own experience has mostly been with molecular biologists, when I worked with my father in his lab as a teenager. I have learned over the years that biologists usually do not have deep training in statistics. In part, that is because much research in biology is qualitative. One might, for example, publish the sequence of a plasmid vector or make some qualitative judgments about the birdsong of North American woodpeckers. Certainly, I have never found a molecular biologist with whom I could talk at length about the Central Limit Theorem and how it figures into null hypothesis testing. In the absence of editorial guidance upon statistical standards, some scientists may find themselves at sea.

Second, editors are bound to enforce or encourage some epistemic norms. For example, in a serious epidemiological study, it will surely be insufficient if N=2 and the subjects are from the same nuclear family. Is the enforcement of other epistemic standards, such as the specification of an α-level or the requirement to use likelihood ratios really different in kind?

Third, and probably most importantly, what does avoiding conflict amount to? Even if editors do acquiesce to the request not to specify positions on probabilistic or statistical standard de jure in their official editorial guidelines, will they not inevitably take a position by choosing which articles to publish? That is, will they not inevitably engage in conflict by virtue of their role as editors, who separate the wheat from the chaff?

Admittedly, what these objections attack are something of a caricature of Mayo’s view, and there is no suggestion that any and all statistical guidance will generate scientific malpractice. However, the dividing line between prudent guidance and guidance which causes our baser instincts of ambition to overtake our better judgment is difficult to draw. Even the standard that editors should avoid  taking positions of strained philosophy controversy is difficult to interpret, since we all know almost any question is a hot button for some philosopher.

Let me now add a rejoinder to my own counterpoint. I am sympathetic with Prof. Mayo’s view more than the above objections may suggest. Like Hempel and Oppenheim, I contend that scientific explanations consist in deductions of sort. What sort of deductive standard is involved in statistical arguments? Though statistics itself makes use of the predicate calculus through its use of arithmetic, algebra, and analysis, statistical arguments employ analogical logic. In particular, in reasoning statistically, we analogize from a sample to a population.

The trouble here, as Paul Bartha writes in the Stanford Encyclopedia of Philosophy’s article on Analogical Reasoning is that though such reasoning abounds, no one has come close to even presenting a plausible sound and complete logic of analogy. It does not merely permeate scientific reasoning

I argue in a forthcoming work, The Foundations of Microeoconomic Analysis (a preview which can be seen here), the reason is that analogical reasoning is situationally-specific. The nature of the similarity between an analogical model and its target defines which sort of inferences or deprojections are warranted epistemically.

Take for example the case of the chassis of a car modeled out of clay to calculate its drag coefficient. Because its shape will be exactly like the chassis of the production model, we can experiment with the clay model in order to make inferences about the airflow. We cannot, however, try to set it on fire, and then conclude the car is impossible to set aflame. Of course this is a contrived example, but it is the burden of author’s to convince us that the deprojections (i.e. the statistical and probabilistic standards) they have made are warranted given the similarity between the sample space and the population. Let the authors be the Latins and Trojans and let the editors watch like cool-headed Jupiter from above.



Yu-Li Ko
(Ph.D in Ecological Economics
Rensselaer Polytechnic Institute)

Some Economics of No-Threshold View

In the recent editorial article in Conservation Biology, Mayo (2021) emphasizes how philosophical presuppositions in statistics can lead to conflicts over journal policies, along with her consistent defense for the proper use of p-value in error control. The particular focus in this article is the adverse consequences of what she calls “no-threshold view,” which demands the restraint of the phrase statistical significance. I will discuss some economics about the no-threshold view and Mayo’s argument.

The incentive problem regarding p-value is a complicated one, and a blog article cannot fully describe the whole extent of the problem for general readers. The core component of the problem is straightforward though: information is incomplete for the reader of a research article. (See Dasgupta and David (1994) for general discussions about the reward system of science and incomplete information.) P-value provides information on research behaviors to the reader, but the research behavior is not directly observable. Due to its information value, p-value can be exploited by the researchers who conduct fraudulent and questionable research practices.

In my view, the no-threshold view tries to solve the problem by weakening the information value of p-value. It intends to make p-value a less attractive tool to manipulate and hence discourage manipulations. As any researcher keen on policy implications would know, when a policy is evaluated the effect needs to be evaluated for unintended effects considering multiple factors. Mayo’s argument on the consequences of the no-threshold view shows how the no-threshold view weakens the effect of intended legitimate uses as well.

Mayo writes, “If the reward structure is seducing even researchers who are aware of the pitfalls of capitalizing on selection biases, then one is dealing with a highly susceptible group.” The target population of the no-threshold view is this “highly susceptible group,” and about this part we do not seem to have sufficient empirical knowledge regarding this particular heterogeneity of population in the science community.

As a policy, the justification of the no-threshold view also depends on the effectiveness of other means to control the susceptible population. Statistical techniques can be developed to solve the problem of incomplete information. If there is a way to statistically detect p-value manipulation it may suffice to discourage the susceptible population. There is a potential that the problem can be fixed with statistical tools rather than institutional interventions. The problem with the no-threshold view is that it can disincentivize the development of such statistical tools. Mayo’s comment, “For a journal or organization to take sides in these long-standing controversies—or even to appear to do so—encourages groupthink and discourages practitioners from arriving at their own reflective conclusions about methods.” seems to express the same concern.

When incomplete information is the problem, the solution is often more information not less. When properly used, p-value and the phrase statistical significance delivers useful information. Rather than giving up on this information, it seems to be a better idea to give it a chance to improve. For the susceptible population, p-value is not the only tool to maneuver, and it is impossible to ban all methods. It is a defeatist attitude to give up on a valid tool.


Dasgupta, P., & David, P. A. (1994). Toward a new economics of science. Research policy, 23(5), 487-521.

Mayo D. G. (2021). The statistics wars and intellectual conflicts of interest. Conservation Biology, Published online December 6, 2021.


3 published commentaries and links to the Phil Stat Forum of January 11 are on my last blog post.

All of the initial blog commentaries on Mayo’s (2021) editorial (up through Jan 18, 2022) are below

Ionides and Ritov

I’m very grateful to all who wrote, and to Yoav Benjamini and David Hand for their presentations at the January 11 Phil Stat Forum on the topic: Statistical significance Test Anxiety.


Categories: Mayo editorial, stat wars and their casualties | 1 Comment

3 Commentaries on my Editorial are being published in Conservation Biology



There are 3 commentaries soon to be published in Conservation Biology on my editorial, “The statistics wars and intellectual conflicts of interest” also published in Conservation Biology. Continue reading

Categories: Mayo editorial, significance tests | Tags: , , , , | Leave a comment

A statistically significant result indicates H’ (μ > μ’) when POW(μ’) is low (not the other way round)–but don’t ignore the standard error


1. New monsters. One of the bizarre facts of life in the statistics wars is that a method from one school may be criticized on grounds that it conflicts with a conception that is the reverse of what that school intends. How is that even to be deciphered? That was the difficult task I set for myself in writing Statistical Inference as Severe Testing: How to Get Beyond the Statistics Wars (CUP, 2008) [SIST 2018]. I thought I was done, but new monsters keep appearing. In some cases, rather than see how the notion of severity gets us beyond fallacies, misconstruals are taken to criticize severity! So, for example, in the last couple of posts, here and here, I deciphered some of the better known power howlers (discussed in SIST Ex 5 Tour II) I’m linking to all of this tour (in proofs). Continue reading

Categories: power, reforming the reformers, SIST, Statistical Inference as Severe Testing | 16 Comments

Do “underpowered” tests “exaggerate” population effects? (iv)


You will often hear that if you reach a just statistically significant result “and the discovery study is underpowered, the observed effects are expected to be inflated” (Ioannidis 2008, p. 64), or “exaggerated” (Gelman and Carlin 2014). This connects to what I’m referring to as the second set of concerns about statistical significance tests, power and magnitude errors. Here, the problem does not revolve around erroneously interpreting power as a posterior probability, as we saw in the fallacy in this post. But there are other points of conflict with the error statistical tester, and much that cries out for clarification — else you will misunderstand the consequences of some of today’s reforms.. Continue reading

Categories: power, reforming the reformers, SIST, Statistical Inference as Severe Testing | 14 Comments

Join me in reforming the “reformers” of statistical significance tests


The most surprising discovery about today’s statistics wars is that some who set out shingles as “statistical reformers” themselves are guilty of misdefining some of the basic concepts of error statistical tests—notably power. (See my recent post on power howlers.) A major purpose of my Statistical Inference as Severe Testing: How to Get Beyond the Statistics Wars (2018, CUP) is to clarify basic notions to get beyond what I call “chestnuts” and “howlers” of tests. The only way that disputing tribes can get beyond the statistics wars is by (at least) understanding correctly the central concepts. But these misunderstandings are more common than ever, so I’m asking readers to help. Why are they more common (than before the “new reformers” of the last decade)? I suspect that at least one reason is the popularity of Bayesian variants on tests: if one is looking to find posterior probabilities of hypotheses, then error statistical ingredients may tend to look as if that’s what they supply. 

Run a little experiment if you come across a criticism based on the power of a test. Ask: are the critics interpreting the power of a test (with null hypothesis H) against an alternative H’ as if it were a posterior probability on H’? If they are, then it’s fallacious. But it will help understand why some people claim that high power against H’ warrants a stronger indication of a discrepancy H’, upon getting a just statistically significant result. But this is wrong. (See my recent post on power howlers.)

I had a blogpost on Ziliac and McCloskey (2008) (Z & M)on power (from Oct. 2011), following a review of their book by Aris Spanos (2008). They write:

“The error of the second kind is the error of accepting the null hypothesis of (say) zero effect when the null is in face false, that is, when (say) such and such a positive effect is true.”

So far so good, keeping in mind that “positive effect” refers to a parameter discrepancy, say δ, not an observed difference.

And the power of a test to detect that such and such a positive effect δ is true is equal to the probability of rejecting the null hypothesis of (say) zero effect when the null is in fact false, and a positive effect as large as δ is present.

Fine. Let this alternative be abbreviated H’(δ):

H’(δ): there is a positive (population) effect at least as large as δ.

Suppose the test rejects the null when it reaches a significance level of .01 (nothing turns on the small value chosen).

(1) The power of the test to detect H’(δ) =

Pr(test rejects null at the .01 level| H’(δ) is true).

Say it is 0.85.

According to Z & M:

“[If] the power of a test is high, say, 0.85 or higher, then the scientist can be reasonably confident that at minimum the null hypothesis (of, again, zero effect if that is the null chosen) is false and that therefore his rejection of it is highly probably correct.” (Z & M, 132-3)

But this is not so.  They are mistaking (1), defining power, as giving a posterior probability of .85 to H’(δ)! That is, (1) is being transformed to (1′):

(1’) Pr(H’(δ) is true| test rejects null at .01 level)=.85!

(I am using the symbol for conditional probability “|” all the way through for ease in following the argument, even though, strictly speaking, the error statistician would use “;”, abbreviating “under the assumption that”). Or to put this in other words, they argue:

1. Pr(test rejects the null | H’(δ) is true) = 0.85.

2. Test rejects the null hypothesis.

Therefore, the rejection is probably correct, e.g., the probability H’ is true is 0.85.

Oops. Premises 1 and 2 are true, but the conclusion fallaciously replaces premise 1 with 1′.

As Aris Spanos (2008) points out, “They have it backwards”. Extracting from a Spanos comment on this blog in 2011:

“When [Ziliak and McCloskey] claim that: ‘What is relevant here for the statistical case is that refutations of the null are trivially easy to achieve if power is low enough or the sample size is large enough.’ (Z & M, p. 152), they exhibit [confusion] about the notion of power and its relationship to the sample size; their two instances of ‘easy rejection’ separated by ‘or’ contradict each other! Rejections of the null are not easy to achieve when the power is ‘low enough’. They are more difficult exactly because the test does not have adequate power (generic capacity) to detect discrepancies from the null; that stems from the very definition of power and optimal tests. [Their second claim] is correct for the wrong reason. Rejections are easy to achieve when the sample size n is large enough due to high not low power. This is because the power of a ‘decent’ (consistent) frequentist test increases monotonically with n!” (Spanos 2011) 

However, their slippery slides are very illuminating for common misinterpretations behind the criticisms of statistical significance tests–assuming a reader can catch them, because they only make them some of the time. [i] According to Ziliak and McCloskey (2008): “It is the history of Fisher significance testing. One erects little significancehurdles, six inches tall, and makes a great show of leaping over them, . . . If a test does a good job of uncovering efficacy, then the test has high power and the hurdles are high not low.” (ibid., p. 133)

They construe little significanceas little hurdles! It explains how they wound up supposing high power translates into high hurdles. Its the opposite. The higher the hurdle required before rejecting the null, the more difficult it is to reject, and the lower the power. High hurdles correspond to insensitive tests, like insensitive fire alarms. It might be that using sensitivityrather than power would make this abundantly clear. We may coin: The high power = high hurdle (for rejection) fallacy. A powerful test does give the null hypothesis a harder time in the sense that its more probable that discrepancies from it are detected. That makes it easier to infer H1. Z & M have their hurdles in a twist.

For a fuller discussion, see this link to Excursion 5 Tour I of SIST (2018). [ii] [iii]

What power howlers have you found? Share them in the comments. 

Spanos, A. (2008), Review of S. Ziliak and D. McCloskey’s The Cult of Statistical SignificanceErasmus Journal for Philosophy and Economics, volume 1, issue 1: 154-164.

Ziliak, Z. and McCloskey, D. (2008), The Cult of Statistical Significance: How the Standard Error Costs Us Jobs, Justice and Lives, University of Michigan Press.

[i] When it comes to raising the power by increasing sample size, they often make true claims, so it’s odd when there’s a switch or mixture, as when they say “refutations of the null are trivially easy to achieve if power is low enough or the sample size is large enough”. (Z & M, p. 152) It is clear that “low” is not a typo here either (as I at first assumed), so it’s mysterious. 

[ii] Remember that a power computation is not the probability of data x under some alternative hypothesis, it’s the probability that data fall in the rejection region of a test under some alternative hypothesis. In terms of a test statistic d(X), it is Pr(test statistic d(X) is statistically significant | H’ true), at a given level of significance. So it’s the probability of getting any of the outcomes that would lead to statistical significance at the chosen level, under the assumption that alternative H’ is true. The alternative H’ used to compute power is a point in the alternative region. However, the inference that is made in tests is not to a point hypothesis but to an inequality, e.g., θ > θ’.

[iii] My rendering of their fallacy above sees it as a type of affirming the consequent.  To Z & M, “the so-called fallacy of affirming the consequent may not be a fallacy at all in a science that is serious about decisions and belief.”  It is, they think, how Bayesians reason. They are right that if inference is by way of a Bayes boost, then affirming the consequent is not a fallacy. A hypothesis H that entails data x will get a “B-boost” from x, unless its probability is already 1. The error statistician objects that the probability of finding an H that perfectly fits x is high, even if H is false–but the Bayesian need not object if she isn’t in the business of error probabilities. The trouble erupts when Z & M take an error statistical concept like power, and construe it Bayesianly. Even more confusing, they only do so some of the time.

Categories: power, SIST, statistical significance tests | Tags: , , | 1 Comment

Happy Birthday Neyman: What was Neyman opposing when he opposed the ‘Inferential’ Probabilists? Your weekend Phil Stat reading


Today is Jerzy Neyman’s birthday (April 16, 1894 – August 5, 1981). I’m reposting a link to a quirky, but fascinating, paper of his that explains one of the most misunderstood of his positions–what he was opposed to in opposing the “inferential theory”. The paper, fro 60 years ago,Neyman, J. (1962), ‘Two Breakthroughs in the Theory of Statistical Decision Making‘ [i] It’s chock full of ideas and arguments. “In the present paper” he tells us, “the term ‘inferential theory’…will be used to describe the attempts to solve the Bayes’ problem with a reference to confidence, beliefs, etc., through some supplementation …either a substitute a priori distribution [exemplified by the so called principle of insufficient reason] or a new measure of uncertainty” such as Fisher’s fiducial probability. It arises on p. 391 of Excursion 5 Tour III of Statistical Inference as Severe Testing: How to Get Beyond the Statistics Wars (2018, CUP). Here’s a link to the proofs of that entire tour. If you hear Neyman rejecting “inferential accounts,” you have to understand it in this very specific way: he’s rejecting “new measures of confidence or diffidence”. Here he alludes to them as “easy ways out”. He is not rejecting statistical inference in favor of behavioral performance as is typically thought. It’s amazing how an idiosyncratic use of a word 60 years ago can cause major rumblings decades later. Neyman always distinguished his error statistical performance conception from Bayesian and Fiducial probabilisms [ii]. The surprising twist here is semantical and the culprit is none other than…Allan Birnbaum. Yet Birnbaum gets short shrift, and no mention is made of our favorite “breakthrough” (or did I miss it?). You can find quite a lot on this blog searching Birnbaum. Continue reading

Categories: Bayesian/frequentist, Neyman | Leave a comment

Power howlers return as criticisms of severity

Mayo bangs head

Suppose you are reading about a statistically significant result x that just reaches a threshold p-value α from a test T+ of the mean of a Normal distribution

 H0: µ ≤  0 against H1: µ >  0

with n iid samples, and (for simplicity) known σ.  The test “rejects” H0 at this level & infers evidence of a discrepancy in the direction of H1.

I have heard some people say:

A. If the test’s power to detect alternative µ’ is very low, then the just statistically significant x is poor evidence of a discrepancy (from the null) corresponding to µ’.  (i.e., there’s poor evidence that  µ > µ’ ). See point* on language in notes.

They will generally also hold that if POW(µ’) is reasonably high (at least .5), then the inference to µ > µ’ is warranted, or at least not problematic.

I have heard other people say:

B. If the test’s power to detect alternative µ’ is very low, then the just statistically significant x is good evidence of a discrepancy (from the null) corresponding to µ’ (i.e., there’s good evidence that  µ > µ’).

They will generally also hold that if POW(µ’) is reasonably high (at least .5), then the inference to µ > µ’ is unwarranted.

Which is correct, from the perspective of the frequentist error statistical philosophy? Continue reading

Categories: Statistical power, statistical tests | Tags: , , , , | 7 Comments

Insevere Tests of Severe Testing (iv)


One does not have evidence for a claim if little if anything has been done to rule out ways the claim may be false. The claim may be said to “pass” the test, but it’s one that utterly lacks stringency or severity. On the basis of this very simple principle, I build a notion of evidence that applies to any error prone inference. In this account, data x are evidence for a claim C only if (and only to the extent that) C has passed a severe test with x.[1] How to apply this simple idea, however, and how to use it to solve central problems of induction and statistical inference requires careful consideration of how it is to be fleshed out. (See this post on strong vs weak severity.)

Consider a fairly egregious, yet all-too familiar, example of a poorly tested claim to the effect that a given drug improves lung function on people with a given fatal lung disease. Say the CEO of the drug company, confronted with disappointing results from an RCT — they are no better than would be expected by the background variability alone — orders his data analysts to “slice and dice” the data until they get some positive results. They might try and try again to find a benefit among various subgroups (e.g., males, females, employment history, etc.). Failing yet again they might vary how “lung benefit” is measured using different proxy variables. This way of proceeding has a high probability of issuing in a report of drug benefit H1 (in some subgroup or other), even if no benefit exists (i.e., even if the null or test hypothesis H0 is true). (For a real case, see my “p-values on trial” in Harvard Data Science Review.)

The method has a high error probability in relation to what it infers, H1. H1 passes a test with low or even minimal severity. The gambit leading to low severity here is referred to with a variety of names, multiple testing, significance seeking, data-dredging, subgroup analysis, outcome switching, and data torturing and others besides. Experimental design principles endorsed by hundreds of medical journals, best-practice statistical manuals, and replication researchers reflect the need to block cavalier attitudes towards inferring data-dredged hypotheses. A variety of ways to avoid, adjust or otherwise compensate for “post data selection,” as some now call it, are well-known.

Some central features of the severity assessment:

  1. The severity assessment attaches to the method of inferring a claim C with a given test T and data x. The resulting assessment for a given hypothesis H1– in this case low — remains even if H1 is known or believed to be true (plausible, probable, or the like). Perhaps there are other data out there, y, or a different type of test, T’, that provide a warrant for H1, but that doesn’t change the low severity afforded by x from test T. In other words, asserting H1 might be right, but if it’s based on the post-data multiple searching method, it is right for the wrong reason. The method, as I described it, failed to distinguish cases where mere random variation throws up a interesting pattern in the particular subgroup which the researchers seize on.
  2. It is incorrect to speak of the severity of a test, in and of itself. Severity, as used and developed by me and by Spanos, refers to an assessment of how well-tested a particular claim of interest is. (It is post-data.) It is analogous to Popper’s term “corroboration” (a claim is corroborated if it passes severely)–never mind that he never adequately cashed it out. The severity associated with C measures how well-corroborated C is, with the data x and the test T under consideration.
  3. In assessing the severity associated with a method, we have to consider how it behaves in general, with other possible outcomes–not just the one you happen to observe–and under various alternatives. That is, we consider the method’s error probabilities–its capabilities to avoid (or commit) erroneous interpretations of the data. Methods that use probability (in inference) to assess and control error probabilities I call error statistical accounts. My account of evidence is one of severe testing based on error statistics.
  4. It is rarely the hypotheses or claims themselves that determine the severity with which they pass tests. Hypotheses pass poor tests when they happen to contain sufficiently vague terms, lending themselves to “just so” stories. An example from Popper is the concept of an “inferiority complex” in Adler’s psychological theory. Whatever behavior is observed, Popper charges, can be ‘explained’ as in sync with Adler (same for concepts in Freud). The theory may be logically falsifiable, but it is immunized from being found false. The theory is easily saved by ad hoc means, even if it’s false. The data-dredger can pull off the same stunt, but–as is more typical– the flexibility is in the data and hypothesis generation and analysis.On the flip side, theories with high content and “corroborative tendrils” that give it more chances of failing enjoy high severity provided that they pass a test that probably would have found flaws. (Sometimes philosophers talk of a large scale theory, paradigm, or research program that is understood to include overall testing methods as well as particular hypothesis.) [Updated 4/5 to include the flip side. For a discussion see SIST (2018) pp. 237-8.]

If someone is interested in appraising the value of our account of severity, and especially if they purport to refute it, they should be sure they are talking about an account with these essential features. Otherwise, their assessment will have no bearing on this account of severity.

Severe testing considers alternative hypotheses but is not a comparative account–there’s a big difference!

A comparative account of evidence merely reports that one hypothesis (model or claim) is favored over another in some sense: It might be said to be more likely, better supported, fit the data better or the like. Comparative accounts do not test, provide evidence for, or falsify hypotheses. They are limited to claiming one fits data better than another in some sense — even though they do not exhaust the possibilities, and even though both might be quite lousy. The better of two poorly warranted hypothesis is still a poorly warranted hypothesis.(See Mayo 2018, Mayo and Spanos 2011).

The classic example of a comparative account is based on the likelihood ratio of the hypothesis H1 over H0 compares the probability (or density) of x under H1which we may write as Pr(x;H1) — to the probability of x under H0, Pr(x;H0).

The likelihood ratio is Pr(x;H1)/Pr(x;H0).

With likelihoods, the data x are fixed while the hypotheses vary. Given the data x, it easy to find a hypothesis H1 that perfectly agrees with the data so that H1 is a better fit to the data than is hypothesis H0. However, as statistician George Barnard puts it, “there always is such a rival hypothesis viz., that things just had to turn out the way they actually did” (Barnard 1972, 129). So the probability of finding some better fitting alternative or other is high (if not guaranteed) even when H0 correctly describes the data generation.

Suppose someone proposes that H1 passes a severe test so long as the data are more probable under H1 than under some H0. Such an account will fail to meet even minimal requirements of severe tests in the error statistical account. Since the data dredging and other biasing selection effects do not alter the likelihood ratio or the Bayes Factor, basing severity on such comparative accounts will be at odds with the one we intend. This does not seem to bother the authors of a recent paper, van Dongen, Sprenger and Wagenmakers (2022), hereafter, VSW (2022). They say straight out:

the Bayes factor only depends on the probability of the data in light of the two competing hypotheses. As Mayo emphasizes (e.g., Mayo and Kruse, 2001; Mayo, 2018), the Bayes factor is insensitive to variations the sampling protocol that affect the error rates, i.e., optional stopping of the experiment.[2] The Bayes factor only depends on the actually observed data, and not on whether they have been collected from an experiment with fixed or variable sample size, and so on. In other words, the Bayesian ex-post evaluation of the evidence stays the same regardless of whether the test has been conducted in a severe or less severe fashion. (VSW 2022)

Stopping at this point and acknowledging the difference in statistical philosophies would be my recommendation. We’re not always in a context of severe testing in our sense. But these authors desire (or appear to desire) an error-statistical severity omelet without breaking the error statistical eggs (to allude to a famous analogous quote by Savage).

In the next paragraph they assure us that they too can capture severity, if not in my sense, then in a (subjective Bayesian) sense they find superior:

We agree with this observation [in the above quote], but we believe that the proper place for severity in statistical inference is the choice of the tested hypotheses (VSW 2022).

But the example they give that is supposed to convince me that I ought to define severity comparatively is not promising. According to them:

a stringent scrutiny of the claim C: “90% of all swans are white” requires only a single swan if the alternative claim is “all swans are black”.

But H1: 90% swans are white, does not pass a stringent scrutiny by dint of finding a single white swan x, although x falsifies H0: all swans are black. (It doesn’t matter for my point how we label the two hypotheses.) While I don’t know the precise distribution of white and black swans (nor how the sample was collected, nor whether the hypotheses are specified post hoc), it would be silly to suppose that a single white swan is good evidence that 90% of the population of swans are white.

A more familiar example of the same form as theirs would be to take a single case where a treatment works as grounds to stringently pass a hypothesis H1: that it works in at least 90% of the population. For these authors, as I understand them, what does the work that enables the alleged stringent inference to H1 is setting H0 as a hypothesis that x falsifies. Of course these two hypotheses scarcely exhaust the space of hypotheses — but this is a standard move (and a standard problem) in comparativist accounts [3]. To my ears, the example illustrated the problem with a comparative appraisal: Pr(x;H1) is surely greater than Pr(x;H0) which is 0, but H1 has not thereby been subjected to a scrutiny that it probably would have failed, if false.

In statistical significance tests, say, concerning the mean μ of a Normal distribution: H0: μ < μ0 versus H1: μ > μ0, we have an alternative hypothesis, but it is not a comparative account. (We could equally well have H0: μ = μ0) VSW question how such an alternative can pass with severity because it is composite (p. 6)–H1: μ > μ0 includes a range of values, e.g., the mean survival is higher in the treated vs the control group. Here’s how it does: A small p-value can warrant H1 with severity because with high probability, 1 – p, we would have obtained a larger p-value were we in a world where H0 is adequate. It is rather the comparative appraisal of point hypotheses that cannot falsify a hypothesis.


I will study the rest of VSW’s paper at a later date. The subjective Bayesian account is sufficiently flexible to redefine terms and goals so that the newly defined severity passes the test. But since the authors already conceded “the Bayesian ex-post evaluation of the evidence stays the same regardless of whether the test has been conducted in a severe or less severe fashion,” it’s hard to see how their view is being put to a severe test.

I may come back to this in a later post. For a detailed development of severe testing, see proofs of the first three excursions from SIST.[4]

Share you constructive remarks in the comments.


[1] Merely blocking an inference to a claim that passes with low severity is what I call weak severity. A fuller, strong severity principle says: We have evidence for a claim C just to the extent it survives a stringent scrutiny. If C passes a test that was highly capable of findings flaws or discrepancies from C, were they to be present, and yet none or few are found, the passing result, x, is evidence for C.

[2] Optional stopping is another gambit that can wreck error probability guarantees, violating what Cox and Hinkley (1974) call weak repeated sampling. (For details, see SIST pp 44-5; Mayo and Kruse 2001 below).

[3] Some Bayesians object to Bayes factors for similar reasons. Gelman (2011) says: “To me, Bayes factors correspond to a discrete view of the world, in which we must choose between models A, B, or C” (p. 74) or a weighted average of them.

[4] I have finally pulled together the pieces from the page proofs of the first three “excursions” of my Statistical Inference as Severe Testing: how to Get Beyond the Statistics Wars (2018, CUP) [SIST]. Here they are, beginning with the Preface: Excursions 1-3 from SIST. I would have hoped that scholars discussing severity and Popper would have looked at what I say about Popper in Excursion 2 (especially Tour II). To depict Popper as endorsing the naive or dogmatic variants called out by Lakatos in 1970 is highly problematic e.g., that old view of falsification by “basic statements”.
The best treatment of Bayes and Popper, I recalled when writing this, is in a book by the non-subjective Bayesian, Roger Rosenkrantz (1977), chapter 6. I looked it up today, and yes I think it is an excellent discussion that at least takes a reader up to Popper 1977. (updated on 4/6/22)



Barnard, G. (1972). The logic of statistical inference (Review of “The Logic of Statistical Inference” by Ian Hacking). British Journal for the Philosophy of Science, 23(2), 123–32.

Cox, D. R. & Hinkley, D. (1974). Theoretical Statistics. London: Chapman and Hall LTD.

Gelman, A. (2011). Induction and Deduction in Bayesian Data Analysis, Rationality, Markets and Morals 2:67-78.

Mayo D. (2018). Statistical inference as severe testing: How to get beyond the statistics wars. Cambridge: Cambridge University Press.

Mayo D. & Kruse, M. (2001). Principles of inference and their consequences. In D. Corfield and J. Williamson (eds.) Foundations of Bayesianism, pp. 381-403. The Netherlands: Kluwer Academic Publishers.

Mayo, D. and Spanos, A. (2011). Error Statistics.

Savage, L. J. (1961). The Foundations of Statistics Reconsidered. Proceedings of the Fourth Berkeley Symposium on Mathematical Statistics and Probability 1. Berkeley: University of California Press, 57586.

van Dongen, N. N. N., Wagenmakers, E., & Sprenger, J. (2020, December 16). A Bayesian perspective on severity: Risky predictions and specific hypotheses. PsyArXiv preprints. (To appear in Psychonomic Bulletin and Review 2022.)

Categories: Error Statistics | 2 Comments

No fooling: The Statistics Wars and Their Casualties Workshop is Postponed to 22-23 September, 2022

The Statistics Wars
and Their Casualties

Postponed to
22-23 September 2022


London School of Economics (CPNSS)

Yoav Benjamini (Tel Aviv University), Alexander Bird (University of Cambridge), Mark Burgman (Imperial College London),
Daniele Fanelli (London School of Economics and Political Science), Roman Frigg (London School of Economics and Political Science), Stephen Guettinger (London School of Economics and Political Science), David Hand (Imperial College London), Margherita Harris (London School of Economics and Political Science), Christian Hennig (University of Bologna), Katrin Hohl *(City University London),
Daniël Lakens (Eindhoven University of Technology), Deborah Mayo (Virginia Tech), Richard Morey (Cardiff University), Stephen Senn (Edinburgh, Scotland), Jon Williamson (University of Kent)

Panel Leaders: TBA

While the field of statistics has a long history of passionate foundational controversy the last decade has, in many ways, been the most dramatic. Misuses of statistics, biasing selection effects, and high powered methods of Big-Data analysis, have helped to make it easy to find impressive-looking but spurious, results that fail to replicate. As the crisis of replication has spread beyond psychology and social sciences to biomedicine, genomics and other fields, people are getting serious about reforms.  Many are welcome (preregistration, transparency about data, eschewing mechanical uses of statistics); some are quite radical. The experts do not agree on how to restore scientific integrity, and these disagreements reflect philosophical battles–old and new– about the nature of inductive-statistical inference and the roles of probability in statistical inference and modeling. These philosophical issues simmer below the surface in competing views about the causes of problems and potential remedies. If statistical consumers are unaware of assumptions behind rival evidence-policy reforms, they cannot scrutinize the consequences that affect them (in personalized medicine, psychology, law, and so on). Critically reflecting on proposed reforms and changing standards requires insights from statisticians, philosophers of science, psychologists, journal editors, economists and practitioners from across the natural and social sciences. This workshop will bring together these interdisciplinary insights–from speakers as well as attendees.

Organizers: D. Mayo and R. Frigg

Logistician (chief logistics and contact person): Jean Miller 

*We have had numerous postponements due to Covid and LSE regulations. Hohl’s attendance is uncertain.

Categories: Error Statistics | Leave a comment

The AI/ML Wars: “explain” or test black box models?


I’ve been reading about the artificial intelligence/machine learning (AI/ML) wars revolving around the use of so-called “black-box” algorithms–too complex for humans, even their inventors, to understand. Such algorithms are increasingly used to make decisions that affect you, but if you can’t understand, or aren’t told, why a machine predicted your graduate-school readiness, or which drug a doctor should prescribe for you, etc, you’d likely be dissatisfied and want some kind of explanation. Being told the machine is highly accurate (in some predictive sense) wouldn’t suffice. A new AI field has grown up around the goal of developing (secondary) “white box” models to “explain” the workings of the (primary) black box model. Some call this explainable AI, or XAI. The black box is still used to reach predictions or decisions, but the explainable model is supposed to help explain why the output was reached. (The EU and DARPA in the U.S. have instituted broad requirements and programs for XAI.) Continue reading

Categories: machine learning, XAI/ML | 15 Comments

Philosophy of Science Association (PSA) 22 Call for Contributed Papers

PSA2022: Call for Contributed Papers


Twenty-Eighth Biennial Meeting of the Philosophy of Science Association
November 10 – November 13, 2022
Pittsburgh, Pennsylvania


Submissions open on March 9, 2022 for contributed papers to be presented at the PSA2022 meeting in Pittsburgh, Pennsylvania, on November 10-13, 2022. The deadline for submitting a paper is 11:59 PM Pacific Standard Time on April 6, 2022. 

Contributed papers may be on any topic in the philosophy of science. The PSA2022 Program Committee is committed to assembling a program with high-quality papers on a variety of topics and diverse presenters that reflects the full range of current work in the philosophy of science. Continue reading

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January 11 Forum: “Statistical Significance Test Anxiety” : Benjamini, Mayo, Hand

Here are all the slides along with the video from the 11 January Phil Stat Forum with speakers: Deborah G. Mayo, Yoav Benjamini and moderator/discussant David Hand.

D. Mayo                 Y. Benjamini.           D. Hand


Y. Benjamini’s slides: “The ASA president Task Force Statement on Statistical Significance and Replicability



Mayo slides are from the Editorial* in Conservation Biology: “The Statistics Wars and Intellectual Conflicts of Interest” Mayo (2021)  




Video of presentations with D. Hand as moderator/discussant:


Categories: ASA Guide to P-values, ASA Task Force on Significance and Replicability, P-values, statistical significance | Leave a comment

Can’t Take the Fiducial Out of Fisher (if you want to understand the N-P performance philosophy) [i]


R.A. Fisher: February 17, 1890 – July 29, 1962

Continuing with posts in recognition of R.A. Fisher’s birthday, I reblog (with a few new comments) one from a few years ago on a topic that had previously not been discussed on this blog: Fisher’s fiducial probability

[Neyman and Pearson] “began an influential collaboration initially designed primarily, it would seem to clarify Fisher’s writing. This led to their theory of testing hypotheses and to Neyman’s development of confidence intervals, aiming to clarify Fisher’s idea of fiducial intervals (D.R.Cox, 2006, p. 195).

Continue reading

Categories: fiducial probability, Fisher, Phil6334/ Econ 6614, Statistics | Leave a comment

R.A. Fisher: “Statistical methods and Scientific Induction” with replies by Neyman and E.S. Pearson

17 Feb 1890-29 July 1962

In recognition of Fisher’s birthday (Feb 17), I reblog what I call the “Triad”–an exchange between  Fisher, Neyman and Pearson (N-P) a full 20 years after the Fisher-Neyman break-up–adding a few new introductory remarks here. While my favorite is still the reply by E.S. Pearson, which alone should have shattered Fisher’s allegations that N-P “reinterpret” tests of significance as “some kind of acceptance procedure”, they are all chock full of gems for different reasons. They are short and worth rereading. Neyman’s article pulls back the cover on what is really behind Fisher’s over-the-top polemics, what with Russian 5-year plans and commercialism in the U.S. Not only is Fisher jealous that N-P tests came to overshadow “his” tests, he is furious at Neyman for driving home the fact that Fisher’s fiducial approach had been shown to be inconsistent (by others). The flaw is glaring and is illustrated very simply by Neyman in his portion of the triad. Further details may be found in my book, SIST (2018) especially pp 388-392 linked to here. It speaks to a common fallacy seen every day in interpreting confidence intervals. As for Neyman’s “behaviorism”, Pearson’s last sentence is revealing. Continue reading

Categories: E.S. Pearson, Fisher, Neyman, phil/history of stat | Leave a comment

Happy Birthday R.A. Fisher: ‘Two New Properties of Mathematical Likelihood’

17 February 1890–29 July 1962

Today is R.A. Fisher’s birthday. I’ll reblog some Fisherian items this week with a few new remarks. This paper comes just before the conflicts with Neyman and Pearson (N-P) erupted.  Fisher links his tests and sufficiency, to the Neyman and Pearson lemma in terms of power. It’s as if we may see Fisher and N-P as ending up in a similar place while starting from different origins, as David Cox might say [1]. Unfortunately, the blow-up that occurred soon after is behind today’s misdirected war vs statistical significance tests.* I quote just the most relevant portions…the full article is linked below.** Happy Birthday Fisher! Continue reading

Categories: Fisher, phil/history of stat | Tags: , , , | Leave a comment

“Should Science Abandon Statistical Significance?” Session at AAAS Annual Meeting, Feb 18

Karen Kafadar, Yoav Benjamini, and Donald Macnaughton will be in a session:

Should Science Abandon Statistical Significance?

Friday, Feb 18 from 2-2:45 PM (EST) at the AAAS 2022 annual meeting.

The general program is here. To register*, go to this page.


The concept of statistical significance is central in scientific research. However, the concept is often poorly understood and thus is often unfairly criticized. This presentation includes three independent but overlapping arguments about the usefulness of the concept of statistical significance to reliably detect “effects” in frontline scientific research data. We illustrate the arguments with examples of scientific importance from genomics, physics, and medicine. We explain how the concept of statistical significance provides a cost-efficient objective way to empower scientific research with evidence.

Papers Continue reading

Categories: AAAS, Announcement, statistical significance | Tags: | Leave a comment

January 11 PhilStat Forum: Mayo: “The Stat Wars and Intellectual Conflicts of Interest”

Here are my slides on my Editorial in Conservation Biology: “The Statistics Wars and Intellectual Conflicts of Interest” Mayo (2021)  presented at  the 11 January Phil Stat Forum with speakers: Deborah G. Mayo and Yoav Benjamini and moderator David Hand. (Benjamini’s slides & full Video to come shortly)

D. Mayo                 Y. Benjamini.           D. Hand



For more details on the focus and background readings see this post on the Phil Stat Forum blog or this post January 10 post.

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ENBIS Webinar: Statistical Significance and p-values

Yesterday’s event video recording is available at:

European Network for Business and Industrial Statistics (ENBIS) Webinar:
Statistical Significance and p-values
Europe/Amsterdam (CET); 08:00-09:30 am (EST)

ENBIS will dedicate this webinar to the memory of Sir David Cox, who sadly passed away in January 2022.

Continue reading

Categories: Announcement, significance tests, Sir David Cox | Tags: , | 2 Comments

“A [very informal] Conversation Between Sir David Cox & D.G. Mayo”

In June 2011, Sir David Cox agreed to a very informal ‘interview’ on the topics of the 2010 workshop that I co-ran at the London School of Economics (CPNSS), Statistical Science and Philosophy of Science, where he was a speaker. Soon after I began taping, Cox stopped me in order to show me how to do a proper interview. He proceeded to ask me questions, beginning with:

COX: Deborah, in some fields foundations do not seem very important, but we both think foundations of statistical inference are important; why do you think that is?

MAYO: I think because they ask about fundamental questions of evidence, inference, and probability. I don’t think that foundations of different fields are all alike; because in statistics we’re so intimately connected to the scientific interest in learning about the world, we invariably cross into philosophical questions about empirical knowledge and inductive inference.

Continue reading

Categories: Birnbaum, Likelihood Principle, Sir David Cox, StatSci meets PhilSci | Tags: , | Leave a comment

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