# spurious p values

## Memory Lane (4 years ago): Why significance testers should reject the argument to “redefine statistical significance”, even if they want to lower the p-value*

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An argument that assumes the very thing that was to have been argued for is guilty of begging the question; signing on to an argument whose conclusion you favor even though you cannot defend its premises is to argue unsoundly, and in bad faith. When a whirlpool of “reforms” subliminally alter  the nature and goals of a method, falling into these sins can be quite inadvertent. Start with a simple point on defining the power of a statistical test.

I. Redefine Power?

Given that power is one of the most confused concepts from Neyman-Pearson (N-P) frequentist testing, it’s troubling that in “Redefine Statistical Significance”, power gets redefined too. “Power,” we’re told, is a Bayes Factor BF “obtained by defining H1 as putting ½ probability on μ = ± m for the value of m that gives 75% power for the test of size α = 0.05. This H1 represents an effect size typical of that which is implicitly assumed by researchers during experimental design.” (material under Figure 1).

The Bayes factor discussed is of H1 over H0, in two-sided Normal testing of H0: μ = 0 versus H1: μ ≠ 0.

“The variance of the observations is known. Without loss of generality, we assume that the variance is 1, and the sample size is also 1.” (p. 2 supplementary)

“This is achieved by assuming that μ under the alternative hypothesis is equal to ± (z0.025 + z0.75) = ± 2.63 [1.96. + .63]. That is, the alternative hypothesis places ½ its prior mass on 2.63 and ½ its mass on -2.63”. (p. 2 supplementary)

Putting to one side whether this is “without loss of generality”, the use of “power” is quite different from the correct definition. The power of a test T  (with type I error probability α) to detect a discrepancy μ’ is the probability T generates an observed difference that is statistically significant at level α, assuming μ = μ’. The value z = 2.63 comes from the fact that the alternative against which this test has power .75 is the value .63 SE in excess of the cut-off for rejection. (Since an SE is 1, they add .63 to 1.96.) I don’t really see why it’s advantageous to ride roughshod on the definition of power, and it’s not the main point of this blogpost, but it’s worth noting if you’re to avoid sinking into the quicksand.

Let’s distinguish the appropriateness of the test for a Bayesian, from its appropriateness as a criticism of significance tests. The latter is my sole focus. The criticism is that, at least if we accept these Bayesian assignments of priors, the posterior probability on H0 will be larger than the p-value. So if you were to interpret a p-value as a posterior on H0 (a fallacy) or if you felt intuitively that a .05 (2-sided) statistically significant result should correspond to something closer to a .05 posterior on H0, you should instead use a p-value of .005–or so it is argued. I’m not sure of the posterior on H0, but the BF is between around 14 and 26.[1] That is the argument. If you lower the required p-value, it won’t be so easy to get statistical significance, and irreplicable results won’t be as common. [2]

The alternative corresponding to the preferred p =.005 requirement

“corresponds to a classical, two-sided test of size α = 0.005. The alternative hypothesis for this Bayesian test places ½ mass at 2.81 and ½ mass at -2.81. The null hypothesis for this test is rejected if the Bayes factor exceeds 25.7. Note that this curve is nearly identical to the “power” curve if that curve had been defined using 80% power, rather than 75% power. The Power curve for 80% power would place ½ its mass at ±2.80”. (Supplementary, p. 2)

z = 2.8 comes from adding .84 SE to the cut-off: 1.96 SE +.84 SE = 2.8. This gets to the alternative vs which the α = 0.05 test has 80% power. (See my previous post on power.)

Is this a good form of inference from the Bayesian perspective? (Why are we comparing μ = 0 and μ = 2.8?). As is always the case with “p-values exaggerate” arguments, there’s the supposition that testing should be on a point null hypothesis, with a lump of prior probability given to H0 (or to a region around 0 so small that it’s indistinguishable from 0). I leave those concerns for Bayesians, and I’m curious to hear from you. More importantly, does it constitute a relevant and sound criticism of significance testing? Let’s be clear: a tester might well have her own reasons for preferring z = 2.8 rather than z = 1.96, but that’s not the question. The question is whether they’ve provided a good argument for the significance tester to do so?

II. What might the significance tester say?

For starters, when she sets .8 power to detect a discrepancy, she doesn’t “implicitly assume” it’s a plausible population discrepancy, but simply one she wants the test to detect by producing a statistically significant difference (with probability .8). And if the test does produce a difference that differs statistically significantly from H0, she does not infer the alternative against which the test had high power, call it μ’. (The supposition that she does grows out of fallaciously transposing “the conditional” involved in power.) Such a rule of interpreting data would have a high error probability of erroneously inferring a discrepancy μ’ (here 2.8).

The significance tester merely seeks evidence of some (genuine) discrepancy from 0, and eschews a comparative inference such as the ratio of the probability of the data under the points 0 and 2.63 (or 2.8). I don’t say there’s no role for a comparative inference, nor preclude someone arguing it is comparing how well μ = 2.8 “explains” the data compared to μ = 0 (given the assumptions), but the form of inference is so different from significance testing, it’s hard to compare them. She definitely wouldn’t ignore all the points in between 0 and 2.8. A one-sided test is preferable (unless the direction of discrepancy is of no interest). While one or two-sided doesn’t make that much difference for a significance tester, it makes a big difference for the type of Bayesian analyses that is appealed to in the “p-values exaggerate” literature. That’s because a lump prior, often .5 (but here .9!), is placed on the point 0 null. Without the lump, the p-value tends to be close to the posterior probability for H0, as Casella and Berger (1987a,b) show–even though p-values and posteriors are actually measuring very different things.

“In fact it is not the case that P-values are too small, but rather that Bayes point null posterior probabilities are much too big!….Our concern should not be to analyze these misspecified problems, but to educate the user so that the hypotheses are properly formulated,” (Casella and Berger 1987 b, p. 334, p. 335).

There is a long and old literature on all this (at least since Edwards, Lindman and Savage 1963–let me know if you’re aware of older sources).

Those who lodge the “p-values exaggerate” critique often say, we’re just showing what would happen even if we made the strongest case for the alternative. No they’re not. They wouldn’t be putting the lump prior on 0 were they concerned not to bias things in favor of the null, and they wouldn’t be looking to compare 0 with so far away an alternative as 2.8 either.

The only way a significance tester can appraise or calibrate a measure such as a BF (and these will differ depending on the alternative picked) is to view it as a statistic and consider the probability of an even larger BF under varying assumptions about the value of μ. This is an error probability associated with the method. Accounts that appraise inferences according to the error probability of the method used I call error statistical (which is less equivocal than frequentist or other terms.)

For example, rejecting H0 when z ≥ 1.96 (which is the .05 test, since they make it 2-sided), we said, had .8 power to detect μ = 2.8, but with the .005 test it has only 50% power to do so. If one insists on a fixed .005 cut-off, this is construed as no evidence against the null (or even evidence for it–for a Bayesian). The new test has only 30% probability of finding significance were the data generated by μ = 2.3. So the significance tester is rightly troubled by the raised type II error [3], although the members of an imaginary Toxic Co. (having the risks of their technology probed) might be happy as clams.[4]

Suppose we do attain statistical significance at the recommended .005 level, say z = 2.8. The BF advocate assures us we can infer μ = 2.8, which is now 25 times as likely as μ = 0, (if all the various Bayesian assignments hold). The trouble is, the significance tester doesn’t want to claim good evidence for μ = 2.8. The significance tester merely infers an indication of a discrepancy (an isolated low p-value doesn’t suffice, and the assumptions also must be checked). She’d never ignore all the points other than 0 and ± 2.8. Suppose we were testing μ ≤ 2.7 vs. μ > 2.7, and observed z = 2.8. What is the p-value associated with this observed difference? The answer is ~.46. (Her inferences are not in terms of points but of discrepancies from the null, but I’m trying to relate the criticism to significance tests. ) To obtain μ ≥ 2.7 using one-sided confidence intervals would require a confidence level of .46 .54. An absurdly low confidence level/high error probability.

The one-sided lower .975 bound with z = 2.8 would only entitle inferring μ > .84 (2.8 – 1.96)–quite a bit smaller than inferring μ = 2.8. If confidence levels are altered as well (and I don’t see why they wouldn’t be), the one-sided lower .995 bound would only be μ > 0. Thus, while the lump prior on  Hresults in a bias in favor of a null–increasing the type II error probability– it’s of interest to note that achieving the recommended p-value licenses an inference much larger than what the significance tester would allow.

Note, their inferences remain comparative in the sense of “H1 over H0” on a given measure, it doesn’t actually say there’s evidence against (or for) either (unless it goes on to compute a posterior, not just odds ratios or BFs), nor does it falsify either hypothesis. This just underscores the fact that the BF comparative inference is importantly different from significance tests which seek to falsify a null hypothesis, with a view toward learning if there are genuine discrepancies, and if so, their magnitude.

Significance tests do not assign probabilities to these parametric hypotheses, but even if one wanted to, the spiked priors needed for the criticism are questioned by Bayesians and frequentists alike. Casella and Berger (1987a) say that “concentrating mass on the point null hypothesis is biasing the prior in favor of H0 as much as possible” (p. 111) whether in one or two-sided tests. According to them “The testing of a point null hypothesis is one of the most misused statistical procedures.” (ibid., p. 106)

III. Why significance testers should reject the “redefine statistical significance” argument:

(i) If you endorse this particular Bayesian way of attaining the BF, fine, but then your argument begs the central question against the significance tester (or of the confidence interval estimator, for that matter). The significance tester is free to turn the situation around, as Fisher does, as refuting the assumptions:

Even if one were to imagine that H0  had an extremely high prior probability, says Fisher—never minding “what such a statement of probability a priori could possibly mean”(Fisher, 1973, p.42)—the resulting high posteriori probability to H0 , he thinks, would only show that “reluctance to accept a hypothesis strongly contradicted by a test of significance” (ibid., p. 44) … “…is not capable of finding expression in any calculation of probability a posteriori” (ibid., p. 43). Indeed, if one were to consider the claim about the priori probability to be itself a hypothesis, Fisher says, “it would be rejected at once by the observations at a level of significance almost as great [as reached by H0 ]. …Were such a conflict of evidence, as has here been imagined under discussion… in a scientific laboratory, it would, I suggest, be some prior assumption…that would certainly be impugned.” (p. 44)

(ii) Suppose, on the other hand, you don’t endorse these priors or the Bayesian computation on which the “redefine significance” argument turns. Since lowering the p-value cut-off doesn’t seem too harmful, you might tend to look the other way as to the argument on which it is based. Isn’t that OK? Not unless you’re prepared to have your students compute these BFs and/or posteriors in just the manner upon which the critique of significance tests rests. Will you say, “oh that was just for criticism, not for actual use”? Unless you’re prepared to defend the statistical analysis, you shouldn’t support it. Lowering the p-value that you require for evidence of a discrepancy, or getting more data (should you wish to do so) doesn’t require it.

Moreover, your student might point out that you still haven’t matched p-values and BFs (or posteriors on H0 ): They still differ, with the p-value being smaller. If you wanted to match the p-value and the posterior, you could do so very easily: use the frequency matching priors (which doesn’t use the spike). You could still lower the p-value to .005, and obtain a rejection region precisely identical to the Bayesian. Why isn’t that a better solution than one based on a conflicting account of statistical inference?

Of course, even that is to grant the problem as put before us by the Bayesian argument. If you’re following good error statistical practice you might instead shirk all cut-offs. You’d report attained p-values, and wouldn’t infer a genuine effect until you’ve satisfied Fisher’s requirements: (a) Replicate yourself, show you can bring about results that “rarely fail to give us a statistically significant result” (1947, p. 14) and that you’re getting better at understanding the causal phenomenon involved. (b) Check your assumptions: both the statistical model, the measurements, and the links between statistical measurements and research claims. (c) Make sure you adjust your error probabilities to take account of, or at least report, biasing selection effects (from cherry-picking, trying and trying again, multiple testing, flexible determinations, post-data subgroups)–according to the context. That’s what prespecified reports are to inform you of. The suggestion that these are somehow taken care of by adjusting the pool of hypotheses on which you base a prior will not do. (It’s their plausibility that often makes them so seductive, and anyway, the injury is to how well-tested claims are, not to their prior believability.) The appeal to diagnostic testing computations of “false positive rates” in this paper opens up a whole new urn of worms. Don’t get me started. (see related posts.)

A final word is from a guest post by Senn.  Harold Jeffreys, he says, held that if you use the spike (which he introduced), you are to infer the hypothesis that achieves greater than .5 posterior probability.

Within the Bayesian framework, in abandoning smooth priors for lump priors, it is also necessary to change the probability standard. (In fact I speculate that the 1 in 20 standard seemed reasonable partly because of the smooth prior.) … A parsimony principle is used on the prior distribution. You can’t use it again on the posterior distribution. Once that is calculated, you should simply prefer the more probable model. The error that is made is not only to assume that P-values should be what they are not but that when one tries to interpret them in the way that one should not, the previous calibration survives.

It is as if in giving recommendations in dosing children one abandoned a formula based on age and adopted one based on weight but insisted on using the same number of kg one had used for years.

Error probabilities are not posterior probabilities. Certainly, there is much more to statistical analysis than P-values but they should be left alone rather than being deformed in some way to become second class Bayesian posterior probabilities. (Senn)

Please share your views, and alert me to errors. I will likely update this. Stay tuned for asterisks.
12/17 * I’ve already corrected a few typos.

[1] I do not mean the “false positive rate” defined in terms of α and (1 – β)–a problematic animal I put to one side here (Mayo 2003). Richard Morey notes that using their prior odds of 1:10, even the recommended BF of 26 gives us an unimpressive  posterior odds ratio of 2.6 (email correspondence).

[2] Note what I call the “fallacy of replication”. It’s said to be too easy to get low p-values, but at the same time it’s too hard to get low p-values in replication. Is it too easy or too hard? That just shows it’s not the p-value at fault but cherry-picking and other biasing selection effects. Replicating a p-value is hard–when you’ve cheated or been sloppy  the first time.

[3] They suggest increasing the sample size to get the power where it was with rejection at z = 1.96, and, while this is possible in some cases, increasing the sample size changes what counts as one sample. As n increases the discrepancy indicated by any level of significance decreases.

[4] The severe tester would report attained levels and,in this case, would indicate the the discrepancies indicated and ruled out with reasonable severity. (Mayo and Spanos 2011). Keep in mind that statistical testing inferences are  in the form of µ > µ’ =µ+ δ,  or µ ≤ µ’ =µ+ δ  or the like. They are not to point values. As for the imaginary Toxic Co., I’d put the existence of a risk of interest in the null hypothesis of a one-sided test.

Related Posts

Elements of this post are from Mayo 2018.

References

Benjamin, D. J., Berger, J., Johannesson, M., Nosek, B. A., Wagenmakers, E.-J., Berk, R., 3 … Johnson, V. (2017, July 22), “Redefine statistical significance“, Nature Human Behavior.

Berger, J. O. and Delampady, M. (1987). “Testing Precise Hypotheses” and “Rejoinder“, Statistical Science 2(3), 317-335.

Berger, J. O. and Sellke, T.  (1987). “Testing a point null hypothesis: The irreconcilability of p values and evidence,” (with discussion). J. Amer. Statist. Assoc. 82: 112–139.

Cassella G. and Berger, R. (1987a). “Reconciling Bayesian and Frequentist Evidence in the One-sided Testing Problem,” (with discussion). J. Amer. Statist. Assoc. 82 106–111, 123–139.

Cassella, G. and Berger, R. (1987b). “Comment on Testing Precise Hypotheses by J. O. Berger and M. Delampady”, Statistical Science 2(3), 344–347.

Edwards, W., Lindman, H. and Savage, L. (1963). “Bayesian Statistical Inference for Psychological Research”, Psychological Review 70(3): 193-242.

Fisher, R. A. (1947). The Design of Experiments (4th ed.). Edinburgh: Oliver and Boyd. (First published 1935).

Fisher, R. A. (1973). Statistical Methods and Scientific Inference, 3rd ed,  New York: Hafner Press.

Ghosh, J. Delampady, M., and Samanta, T. (2006). An Introduction to Bayesian Analysis: Theory and Methods. New York: Springer.

Mayo, D. G. (2003). “Could Fisher, Jeffreys and Neyman have Agreed on Testing? Commentary on J. Berger’s Fisher Address,” Statistical Science 18: 19-24.

Mayo (2018), Statistical Inference as Severe Testing: How to Get Beyond the Statistics Wars. Cambridge (June 2018)

Mayo, D. G. and Spanos, A. (2011) “Error Statistics” in Philosophy of Statistics , Handbook of Philosophy of Science Volume 7 Philosophy of Statistics, (General editors: Dov M. Gabbay, Paul Thagard and John Woods; Volume eds. Prasanta S. Bandyopadhyay and Malcolm R. Forster.) Elsevier: 1-46.

## Why significance testers should reject the argument to “redefine statistical significance”, even if they want to lower the p-value*

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An argument that assumes the very thing that was to have been argued for is guilty of begging the question; signing on to an argument whose conclusion you favor even though you cannot defend its premises is to argue unsoundly, and in bad faith. When a whirlpool of “reforms” subliminally alter  the nature and goals of a method, falling into these sins can be quite inadvertent. Start with a simple point on defining the power of a statistical test.

I. Redefine Power?

Given that power is one of the most confused concepts from Neyman-Pearson (N-P) frequentist testing, it’s troubling that in “Redefine Statistical Significance”, power gets redefined too. “Power,” we’re told, is a Bayes Factor BF “obtained by defining H1 as putting ½ probability on μ = ± m for the value of m that gives 75% power for the test of size α = 0.05. This H1 represents an effect size typical of that which is implicitly assumed by researchers during experimental design.” (material under Figure 1). Continue reading

## Statistical skepticism: How to use significance tests effectively: 7 challenges & how to respond to them

Here are my slides from the ASA Symposium on Statistical Inference : “A World Beyond p < .05”  in the session, “What are the best uses for P-values?”. (Aside from me,our session included Yoav Benjamini and David Robinson, with chair: Nalini Ravishanker.)

7 QUESTIONS

• Why use a tool that infers from a single (arbitrary) P-value that pertains to a statistical hypothesis H0 to a research claim H*?
• Why use an incompatible hybrid (of Fisher and N-P)?
• Why apply a method that uses error probabilities, the sampling distribution, researcher “intentions” and violates the likelihood principle (LP)? You should condition on the data.
• Why use methods that overstate evidence against a null hypothesis?
• Why do you use a method that presupposes the underlying statistical model?
• Why use a measure that doesn’t report effect sizes?
• Why do you use a method that doesn’t provide posterior probabilities (in hypotheses)?

## Thieme on the theme of lowering p-value thresholds (for Slate)

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Here’s an article by Nick Thieme on the same theme as my last blogpost. Thieme, who is Slate’s 2017 AAAS Mass Media Fellow, is the first person to interview me on p-values who (a) was prepared to think through the issue for himself (or herself), and (b) included more than a tiny fragment of my side of the exchange.[i]. Please share your comments.

## Will Lowering P-Value Thresholds Help Fix Science? P-values are already all over the map, and they’re also not exactly the problem.

Last week a team of 72 scientists released the preprint of an article attempting to address one aspect of the reproducibility crisis, the crisis of conscience in which scientists are increasingly skeptical about the rigor of our current methods of conducting scientific research.

Their suggestion? Change the threshold for what is considered statistically significant. The team, led by Daniel Benjamin, a behavioral economist from the University of Southern California, is advocating that the “probability value” (p-value) threshold for statistical significance be lowered from the current standard of 0.05 to a much stricter threshold of 0.005. Continue reading

Categories: P-values, reforming the reformers, spurious p values | 14 Comments

## Gigerenzer at the PSA: “How Fisher, Neyman-Pearson, & Bayes Were Transformed into the Null Ritual”: Comments and Queries (ii)

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Gerd Gigerenzer, Andrew Gelman, Clark Glymour and I took part in a very interesting symposium on Philosophy of Statistics at the Philosophy of Science Association last Friday. I jotted down lots of notes, but I’ll limit myself to brief reflections and queries on a small portion of each presentation in turn, starting with Gigerenzer’s “Surrogate Science: How Fisher, Neyman-Pearson, & Bayes Were Transformed into the Null Ritual.” His complete slides are below my comments. I may write this in stages, this being (i).

SLIDE #19

1. Good scientific practice–bold theories, double-blind experiments, minimizing measurement error, replication, etc.–became reduced in the social science to a surrogate: statistical significance.

I agree that “good scientific practice” isn’t some great big mystery, and that “bold theories, double-blind experiments, minimizing measurement error, replication, etc.” are central and interconnected keys to finding things out in error prone inquiry. Do the social sciences really teach that inquiry can be reduced to cookbook statistics? Or is it simply that, in some fields, carrying out surrogate science suffices to be a “success”? Continue reading

## Some statistical dirty laundry: have the stains become permanent?

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Right after our session at the SPSP meeting last Friday, I chaired a symposium on replication that included Brian Earp–an active player in replication research in psychology (Replication and Evidence: A tenuous relationship p. 80). One of the first things he said, according to my notes, is that gambits such as cherry picking, p-hacking, hunting for significance, selective reporting, and other QRPs, had been taught as acceptable become standard practice in psychology, without any special need to adjust p-values or alert the reader to their spuriousness [i]. (He will correct me if I’m wrong[2].) It shocked me to hear it, even though it shouldn’t have, given what I’ve learned about statistical practice in social science. It was the Report on Stapel that really pulled back the curtain on this attitude toward QRPs in social psychology–as discussed in this blogpost 3 years ago. (If you haven’t read Section 5 of the report on flawed science, you should.) Many of us assumed that QRPs, even if still committed, were at least recognized to be bad statistical practices since the time of Morrison and Henkel’s (1970) Significance Test Controversy. A question now is this: have all the confessions of dirty laundry, the fraudbusting of prominent researchers, the pledges to straighten up and fly right, the years of replication research, done anything to remove the stains? I leave the question open for now. Here’s my “statistical dirty laundry” post from 2013: Continue reading

Categories: junk science, reproducibility, spurious p values, Statistics | 4 Comments

## The Paradox of Replication, and the vindication of the P-value (but she can go deeper) 9/2/15 update (ii)

The unpopular P-value is invited to dance.

Critic 1: It’s much too easy to get small P-values.

Critic 2: We find it very difficult to get small P-values; only 36 of 100 psychology experiments were found to yield small P-values in the recent Open Science collaboration on replication (in psychology).

Is it easy or is it hard?

You might say, there’s no paradox, the problem is that the significance levels in the original studies are often due to cherry-picking, multiple testing, optional stopping and other biasing selection effects. The mechanism by which biasing selection effects blow up P-values is very well understood, and we can demonstrate exactly how it occurs. In short, many of the initially significant results merely report “nominal” P-values not “actual” ones, and there’s nothing inconsistent between the complaints of critic 1 and critic 2.

The resolution of the paradox attests to what many have long been saying: the problem is not with the statistical methods but with their abuse. Even the P-value, the most unpopular girl in the class, gets to show a little bit of what she’s capable of. She will give you a hard time when it comes to replicating nominally significant results, if they were largely due to biasing selection effects. That is just what is wanted; it is an asset that she feels the strain, and lets you know. It is statistical accounts that can’t pick up on biasing selection effects that should worry us (especially those that deny they are relevant). That is one of the most positive things to emerge from the recent, impressive, replication project in psychology. From an article in the Smithsonian magazine “Scientists Replicated 100 Psychology Studies, and Fewer Than Half Got the Same Results”:

The findings also offered some support for the oft-criticized statistical tool known as the P value, which measures whether a result is significant or due to chance. …

The project analysis showed that a low P value was fairly predictive of which psychology studies could be replicated. Twenty of the 32 original studies with a P value of less than 0.001 could be replicated, for example, while just 2 of the 11 papers with a value greater than 0.04 were successfully replicated. (Link is here.)

## Some statistical dirty laundry: The Tilberg (Stapel) Report on “Flawed Science”

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I had a chance to reread the 2012 Tilberg Report* on “Flawed Science” last night. The full report is now here. The discussion of the statistics is around pp. 17-21 (of course there was so little actual data in this case!) You might find it interesting. Here are some stray thoughts reblogged from 2 years ago…

1. Slipping into pseudoscience.
The authors of the Report say they never anticipated giving a laundry list of “undesirable conduct” by which researchers can flout pretty obvious requirements for the responsible practice of science. It was an accidental byproduct of the investigation of one case (Diederik Stapel, social psychology) that they walked into a culture of “verification bias”[1]. Maybe that’s why I find it so telling. It’s as if they could scarcely believe their ears when people they interviewed “defended the serious and less serious violations of proper scientific method with the words: that is what I have learned in practice; everyone in my research environment does the same, and so does everyone we talk to at international conferences” (Report 48). So they trot out some obvious rules, and it seems to me that they do a rather good job.

One of the most fundamental rules of scientific research is that an investigation must be designed in such a way that facts that might refute the research hypotheses are given at least an equal chance of emerging as do facts that confirm the research hypotheses. Violations of this fundamental rule, such as continuing an experiment until it works as desired, or excluding unwelcome experimental subjects or results, inevitably tends to confirm the researcher’s research hypotheses, and essentially render the hypotheses immune to the facts…. [T]he use of research procedures in such a way as to ‘repress’ negative results by some means” may be called verification bias. [my emphasis] (Report, 48).

I would place techniques for ‘verification bias’ under the general umbrella of techniques for squelching stringent criticism and repressing severe tests. These gambits make it so easy to find apparent support for one’s pet theory or hypotheses, as to count as no evidence at all (see some from their list ). Any field that regularly proceeds this way I would call a pseudoscience, or non-science, following Popper. “Observations or experiments can be accepted as supporting a theory (or a hypothesis, or a scientific assertion) only if these observations or experiments are severe tests of the theory” (Popper 1994, p. 89). [2] It is unclear at what point a field slips into the pseudoscience realm.

2. A role for philosophy of science?
I am intrigued that one of the final recommendations in the Report is this: Continue reading

Categories: junk science, spurious p values | 14 Comments

## Some statistical dirty laundry

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It’s an apt time to reblog the “statistical dirty laundry” post from 2013 here. I hope we can take up the recommendations from Simmons, Nelson and Simonsohn at the end (Note [5]), which we didn’t last time around.

^^^^^^^^^^^^^^^^^^^^^^^^^^^^^^

I finally had a chance to fully read the 2012 Tilberg Report* on “Flawed Science” last night. Here are some stray thoughts…

1. Slipping into pseudoscience.
The authors of the Report say they never anticipated giving a laundry list of “undesirable conduct” by which researchers can flout pretty obvious requirements for the responsible practice of science. It was an accidental byproduct of the investigation of one case (Diederik Stapel, social psychology) that they walked into a culture of “verification bias”[1]. Maybe that’s why I find it so telling. It’s as if they could scarcely believe their ears when people they interviewed “defended the serious and less serious violations of proper scientific method with the words: that is what I have learned in practice; everyone in my research environment does the same, and so does everyone we talk to at international conferences” (Report 48). So they trot out some obvious rules, and it seems to me that they do a rather good job:

One of the most fundamental rules of scientific research is that an investigation must be designed in such a way that facts that might refute the research hypotheses are given at least an equal chance of emerging as do facts that confirm the research hypotheses. Violations of this fundamental rule, such as continuing an experiment until it works as desired, or excluding unwelcome experimental subjects or results, inevitably tends to confirm the researcher’s research hypotheses, and essentially render the hypotheses immune to the facts…. [T]he use of research procedures in such a way as to ‘repress’ negative results by some means” may be called verification bias. [my emphasis] (Report, 48).

I would place techniques for ‘verification bias’ under the general umbrella of techniques for squelching stringent criticism and repressing severe tests. These gambits make it so easy to find apparent support for one’s pet theory or hypotheses, as to count as no evidence at all (see some from their list ). Any field that regularly proceeds this way I would call a pseudoscience, or non-science, following Popper. “Observations or experiments can be accepted as supporting a theory (or a hypothesis, or a scientific assertion) only if these observations or experiments are severe tests of the theory” (Popper 1994, p. 89). [2] It is unclear at what point a field slips into the pseudoscience realm.

2. A role for philosophy of science?
I am intrigued that one of the final recommendations in the Report is this: Continue reading

Categories: junk science, reproducibility, spurious p values, Statistics | 27 Comments

## A biased report of the probability of a statistical fluke: Is it cheating?

One year ago I reblogged a post from Matt Strassler, “Nature is Full of Surprises” (2011). In it he claims that

[Statistical debate] “often boils down to this: is the question that you have asked in applying your statistical method the most even-handed, the most open-minded, the most unbiased question that you could possibly ask?

It’s not asking whether someone made a mathematical mistake. It is asking whether they cheated — whether they adjusted the rules unfairly — and biased the answer through the question they chose…”

(Nov. 2014):I am impressed (i.e., struck by the fact) that he goes so far as to call it “cheating”. Anyway, here is the rest of the reblog from Strassler which bears on a number of recent discussions:

“…If there are 23 people in a room, the chance that two of them have the same birthday is 50 percent, while the chance that two of them were born on a particular day, say, January 1st, is quite low, a small fraction of a percent. The more you specify the coincidence, the rarer it is; the broader the range of coincidences at which you are ready to express surprise, the more likely it is that one will turn up.

Categories: Higgs, spurious p values, Statistics | 7 Comments

## Reliability and Reproducibility: Fraudulent p-values through multiple testing (and other biases): S. Stanley Young (Phil 6334: Day#13)

S. Stanley Young, PhD
Assistant Director for Bioinformatics
National Institute of Statistical Sciences
Research Triangle Park, NC

Here are Dr. Stanley Young’s slides from our April 25 seminar. They contain several tips for unearthing deception by fraudulent p-value reports. Since it’s Saturday night, you might wish to perform an experiment with three 10-sided dice*,recording the results of 100 rolls (3 at a time) on the form on slide 13. An entry, e.g., (0,1,3) becomes an imaginary p-value of .013 associated with the type of tumor, male-female, old-young. You report only hypotheses whose null is rejected at a “p-value” less than .05. Forward your results to me for publication in a peer-reviewed journal.

*Sets of 10-sided dice will be offered as a palindrome prize beginning in May.

## capitalizing on chance (ii)

DGM playing the slots

I may have been exaggerating one year ago when I started this post with “Hardly a day goes by”, but now it is literally the case*. (This  also pertains to reading for Phil6334 for Thurs. March 6):

Hardly a day goes by where I do not come across an article on the problems for statistical inference based on fallaciously capitalizing on chance: high-powered computer searches and “big” data trolling offer rich hunting grounds out of which apparently impressive results may be “cherry-picked”:

When the hypotheses are tested on the same data that suggested them and when tests of significance are based on such data, then a spurious impression of validity may result. The computed level of significance may have almost no relation to the true level. . . . Suppose that twenty sets of differences have been examined, that one difference seems large enough to test and that this difference turns out to be “significant at the 5 percent level.” Does this mean that differences as large as the one tested would occur by chance only 5 percent of the time when the true difference is zero? The answer is no, because the difference tested has been selected from the twenty differences that were examined. The actual level of significance is not 5 percent, but 64 percent! (Selvin 1970, 104)[1]

…Oh wait -this is from a contributor to Morrison and Henkel way back in 1970! But there is one big contrast, I find, that makes current day reports so much more worrisome: critics of the Morrison and Henkel ilk clearly report that to ignore a variety of “selection effects” results in a fallacious computation of the actual significance level associated with a given inference; clear terminology is used to distinguish the “computed” or “nominal” significance level on the one hand, and the actual or warranted significance level on the other. Continue reading

## Probability that it is a statistical fluke [i]

From another blog:
“…If there are 23 people in a room, the chance that two of them have the same birthday is 50 percent, while the chance that two of them were born on a particular day, say, January 1st, is quite low, a small fraction of a percent. The more you specify the coincidence, the rarer it is; the broader the range of coincidences at which you are ready to express surprise, the more likely it is that one will turn up.

Humans are notoriously incompetent at estimating these types of probabilities… which is why scientists (including particle physicists), when they see something unusual in their data, always try to quantify the probability that it is a statistical fluke — a pure chance event. You would not want to be wrong, and celebrate your future Nobel prize only to receive instead a booby prize. (And nature gives out lots and lots of booby prizes.) So scientists, grabbing their statistics textbooks and appealing to the latest advances in statistical techniques, compute these probabilities as best they can. Armed with these numbers, they then try to infer whether it is likely that they have actually discovered something new or not.

And on the whole, it doesn’t work. Unless the answer is so obvious that no statistical argument is needed, the numbers typically do not settle the question.

Despite this remark, you mustn’t think I am arguing against doing statistics. One has to do something better than guessing. But there is a reason for the old saw: “There are three types of falsehoods: lies, damned lies, and statistics.” It’s not that statistics themselves lie, but that to some extent, unless the case is virtually airtight, you can almost always choose to ask a question in such a way as to get any answer you want. … [For instance, in 1991 the volcano Pinatubo in the Philippines had its titanic eruption while a hurricane (or `typhoon’ as it is called in that region) happened to be underway. Oh, and the collapse of Lehman Brothers on Sept 15, 2008 was followed within three days by the breakdown of the Large Hadron Collider (LHC) during its first week of running… Coincidence?  I-think-so.] One can draw completely different conclusions, both of them statistically sensible, by looking at the same data from two different points of view, and asking for the statistical answer to two different questions.

To a certain extent, this is just why Republicans and Democrats almost never agree, even if they are discussing the same basic data. The point of a spin-doctor is to figure out which question to ask in order to get the political answer that you wanted in advance. Obviously this kind of manipulation is unacceptable in science. Unfortunately it is also unavoidable. Continue reading

## Phil/Stat/Law: 50 Shades of gray between error and fraud

An update on the Diederik Stapel case: July 2, 2013, The Scientist, “Dutch Fraudster Scientist Avoids Jail”.

Two years after being exposed by colleagues for making up data in at least 30 published journal articles, former Tilburg University professor Diederik Stapel will avoid a trial for fraud. Once one of the Netherlands’ leading social psychologists, Stapel has agreed to a pre-trial settlement with Dutch prosecutors to perform 120 hours of community service.

According to Dutch newspaper NRC Handeslblad, the Dutch Organization for Scientific Research awarded Stapel \$2.8 million in grants for research that was ultimately tarnished by misconduct. However, the Dutch Public Prosecution Service and the Fiscal Information and Investigation Service said on Friday (June 28) that because Stapel used the grant money for student and staff salaries to perform research, he had not misused public funds. …

In addition to the community service he will perform, Stapel has agreed not to make a claim on 18 months’ worth of illness and disability compensation that he was due under his terms of employment with Tilburg University. Stapel also voluntarily returned his doctorate from the University of Amsterdam and, according to Retraction Watch, retracted 53 of the more than 150 papers he has co-authored.

“I very much regret the mistakes I have made,” Stapel told ScienceInsider. “I am happy for my colleagues as well as for my family that with this settlement, a court case has been avoided.”

No surprise he’s not doing jail time, but 120 hours of community service?  After over a decade of fraud, and tainting 14 of 21 of the PhD theses he supervised?  Perhaps the “community service” should be to actually run the experiments he had designed?  What about his innocence of misusing public funds? Continue reading

Categories: PhilStatLaw, spurious p values, Statistics | 13 Comments

## Some statistical dirty laundry

I finally had a chance to fully read the 2012 Tilberg Report* on “Flawed Science” last night. The full report is now here. Here are some stray thoughts…

1. Slipping into pseudoscience.
The authors of the Report say they never anticipated giving a laundry list of “undesirable conduct” by which researchers can flout pretty obvious requirements for the responsible practice of science. It was an accidental byproduct of the investigation of one case (Diederik Stapel, social psychology) that they walked into a culture of “verification bias”[1]. Maybe that’s why I find it so telling. It’s as if they could scarcely believe their ears when people they interviewed “defended the serious and less serious violations of proper scientific method with the words: that is what I have learned in practice; everyone in my research environment does the same, and so does everyone we talk to at international conferences” (Report 48). So they trot out some obvious rules, and it seems to me that they do a rather good job.

One of the most fundamental rules of scientific research is that an investigation must be designed in such a way that facts that might refute the research hypotheses are given at least an equal chance of emerging as do facts that confirm the research hypotheses. Violations of this fundamental rule, such as continuing an experiment until it works as desired, or excluding unwelcome experimental subjects or results, inevitably tends to confirm the researcher’s research hypotheses, and essentially render the hypotheses immune to the facts…. [T]he use of research procedures in such a way as to ‘repress’ negative results by some means” may be called verification bias. [my emphasis] (Report, 48).

I would place techniques for ‘verification bias’ under the general umbrella of techniques for squelching stringent criticism and repressing severe tests. These gambits make it so easy to find apparent support for one’s pet theory or hypotheses, as to count as no evidence at all (see some from their list ). Any field that regularly proceeds this way I would call a pseudoscience, or non-science, following Popper. “Observations or experiments can be accepted as supporting a theory (or a hypothesis, or a scientific assertion) only if these observations or experiments are severe tests of the theory” (Popper 1994, p. 89). [2] It is unclear at what point a field slips into the pseudoscience realm.

2. A role for philosophy of science?
I am intrigued that one of the final recommendations in the Report is this:

In the training program for PhD students, the relevant basic principles of philosophy of science, methodology, ethics and statistics that enable the responsible practice of science must be covered. Based on these insights, research Master’s students and PhD students must receive practical training from their supervisors in the application of the rules governing proper and honest scientific research, which should include examples of such undesirable conduct as data massage. The Graduate School must explicitly ensure that this is implemented.

A philosophy department could well create an entire core specialization that revolved around “the relevant basic principles of philosophy of science, methodology, ethics and statistics that enable the responsible practice of science” (ideally linked with one or more other departments).  That would be both innovative and fill an important gap, it seems to me. Is anyone doing this?

3. Hanging out some statistical dirty laundry.
Items in their laundry list include:

• An experiment fails to yield the expected statistically significant results. The experiment is repeated, often with minor changes in the manipulation or other conditions, and the only experiment subsequently reported is the one that did yield the expected results. The article makes no mention of this exploratory method… It should be clear, certainly with the usually modest numbers of experimental subjects, that using experiments in this way can easily lead to an accumulation of chance findings…. Continue reading
Categories: junk science, spurious p values, Statistics | 6 Comments

## “Bad statistics”: crime or free speech?

Hunting for “nominally” significant differences, trying different subgroups and multiple endpoints, can result in a much higher probability of erroneously inferring evidence of a risk or benefit than the nominal p-value, even in randomized controlled trials. This was an issue that arose in looking at RCTs in development economics (an area introduced to me by Nancy Cartwright), as at our symposium at the Philosophy of Science Association last month[i][ii]. Reporting the results of hunting and dredging in just the same way as if the relevant claims were predesignated can lead to misleading reports of actual significance levels.[iii]

Still, even if reporting spurious statistical results is considered “bad statistics,” is it criminal behavior? I noticed this issue in Nathan Schachtman’s blog over the past couple of days. The case concerns a biotech company, InterMune, and its previous CEO, Dr. Harkonen. Here’s an excerpt from Schachtman’s discussion (part 1). Continue reading

Categories: PhilStatLaw, significance tests, spurious p values, Statistics | 27 Comments