Monthly Archives: April 2022

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

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