NHST and Systematic Biases

Statistical background on p-value problems: Against null-hypothesis statistical-significance testing

The basic nature of ‘significance’ being usually defined as p < 0.05 means we should expect something like >5% of studies or experiments to be bogus (optimistically), but that only considers “false positives”; reducing “false negatives” requires statistical power (weakened by small samples), and the two combine with the base rate of true underlying effects into a total error rate. Ioannidis 2005 points out that considering the usual p values, the underpowered nature of many studies, the rarity of underlying effects, and a little bias, even large randomized trials may wind up with only an 85% chance of having yielded the truth. One survey of reported p-values in medicine yielding a lower bound of false positives of 17%.

Yet, there are too many positive results¹ (psychiatry⁠, neurobiology biomedicine⁠, biology⁠, ecology & evolution⁠, psychology 12 3 4 5⁠, economics’ top journals⁠, sociology⁠, gene-disease correlations) given effect sizes (and positive results correlate with per capita publishing rates in US states & vary by period & country—apparently chance is kind to scientists who must publish a lot and recently!); then there come the inadvertent errors which might cause retraction, which is rare, but the true retraction rate may be 0.1–1% (“How many scientific papers should be retracted?”), is increasing & seems to positively correlate with journal prestige metrics (modulo the confounding factor that famous papers/​journals get more scrutiny), not that anyone pays any attention to such things; then there are basic statistical errors in >11% of papers (based on the high-quality papers in Nature and the British Medical Journal; “Incongruence between test statistics and P values in medical papers”⁠, García-Berthou 2004) or 50% in neuroscience⁠.

And only then can we get into replicating at all. See for example The Atlantic article “Lies, Damned Lies, and Medical Science” on John P. A. Ioannidis’s research showing 41% of the most cited medical research failed to be replicated—were wrong. For details, you can see Ioannidis’s “Why Most Published Research Findings Are False”²⁠, or Begley’s failed attempts to replicate 47 of 53 articles on top cancer journals (leading to Booth’s “Begley’s Six Rules”⁠; see also the Nature Biotechnology editorial & note that full details have not been published because the researchers of the original studies demanded secrecy from Begley’s team), or Kumar & Nash 2011’s “Health Care Myth Busters: Is There a High Degree of Scientific Certainty in Modern Medicine?” who write ‘We could accurately say, “Half of what physicians do is wrong,” or “Less than 20% of what physicians do has solid research to support it.”’ Nutritional epidemiology is something of a fish in a barrel; after Ioannidis, is anyone surprised that when Young & Karr 2011 followed up on 52 correlations tested in 12 RCTs, 0⁄52 replicated and the RCTs found the opposite of 5?

Attempts to use animal models to infer anything about humans suffer from all the methodological problems previously mentioned⁠, and add in interesting new forms of error such as mice simply being irrelevant to humans, leading to cases like <150 sepsis clinical trials all failing—because the drugs worked in mice but humans have a completely different set of genetic reactions to inflammation.

‘Hot’ fields tend to be new fields, which brings problems of its own, see “Large-Scale Assessment of the Effect of Popularity on the Reliability of Research” & discussion⁠. (Failure to replicate in larger studies seems to be a hallmark of biological/​medical research. Ioannidis performs the same trick with biomarkers⁠, finding less than half of the most-cited biomarkers were even statistically-significant in the larger studies. 12 of the more prominent SNP-IQ correlations failed to replicate on a larger data.) As we know now, almost the entire candidate-gene literature, most things reported from 2000–2010 before large-scale GWASes started to be done (and completely failing to find the candidate-genes), is nothing but false positives! The replication rates of candidate-genes for things like intelligence, personality, gene-environment interactions, psychiatric disorders–the whole schmeer—are literally ~0%. On the plus side, the parlous state of affairs means that there are some cheap heuristics for detecting unreliable papers—simply asking for data & being refused /​ ​ignored correlates strongly with the original paper having errors in its statistics.

This epidemic of false positives is apparently deliberately and knowing accepted by epidemiology⁠; Young’s 2008 “Everything is Dangerous” remarks that 80–90% of epidemiology’s claims do not replicate (eg. the NIH ran 20 randomized-controlled-trials of claims, and only 1 replicated) and that lack of ‘multiple comparisons’ (either Bonferroni or Benjamin-Hochberg) is taught: “Rothman (1990) says no correction for multiple testing is necessary and Vandenbroucke, PLoS Med (2008) agrees” (see also Perneger 1998 who also explicitly understands that no correction increases type 2 errors and reduces type 1 errors). Multiple correction is necessary because its absence does, in fact, result in the overstatement of medical benefit (Godfrey 1985⁠, Pocock et al 1987⁠, Smith 1987). The average effect size for findings confirmed meta-analytically in psychology/​education is d = 0.5³ (well below several effect sizes from n-back/​IQ studies); when moving from laboratory to non-laboratory settings, meta-analyses replicate findings correlate ~0.7 of the time, but for social psychology the replication correlation falls to ~0.5 with >14% of findings actually turning out to be the opposite (see Anderson et al 1999 and Mitchell 2012⁠; for exaggeration due to non-blinding or poor randomization, Wood et al 2008). (Meta-analyses also give us a starting point for understanding how unusual medium or large effects sizes are⁴⁠.) Psychology does have many challenges, but practitioners also handicap themselves; an older overview is the entertaining “What’s Wrong With Psychology, Anyway?”⁠, which mentions the obvious point that statistics & experimental design are flexible enough to reach significance as desired. In an interesting example of how methodological reforms are no panacea in the presence of continued perverse incentives, an earlier methodological improvement in psychology (reporting multiple experiments in a single publication as a check against results not being generalizable) has merely demonstrated the widespread p-value hacking or manipulation or publication bias when one notes that given the low statistical power of each experiment, even if the underlying phenomena were real it would still be wildly improbable that all n experiments in a paper would turn up statistically-significant results, since power is usually extremely low in experiments (eg. in neuroscience, “between 20–30%”). These problems are pervasive enough that I believe they entirely explain any “decline effects”⁵⁠.

The failures to replicate “statistically significant” results has led one blogger to caustically remark (see also “Parapsychology: the control group for science”⁠, “Using degrees of freedom to change the past for fun and profit”⁠, “The Control Group is Out Of Control”):

Parapsychology, the control group for science, would seem to be a thriving field with “statistically significant” results aplenty…Parapsychologists are constantly protesting that they are playing by all the standard scientific rules, and yet their results are being ignored—that they are unfairly being held to higher standards than everyone else. I’m willing to believe that. It just means that the standard statistical methods of science are so weak and flawed as to permit a field of study to sustain itself in the complete absence of any subject matter. With two-thirds of medical studies in prestigious journals failing to replicate, getting rid of the entire actual subject matter would shrink the field by only 33%.

Cosma Shalizi:

…Let me draw the moral [about publication bias]. Even if the community of inquiry is both too clueless to make any contact with reality and too honest to nudge borderline findings into significance, so long as they can keep coming up with new phenomena to look for, the mechanism of the file-drawer problem alone will guarantee a steady stream of new results. There is, so far as I know, no Journal of Evidence-Based Haruspicy filled, issue after issue, with methodologically-faultless papers reporting the ability of sheep’s livers to predict the winners of sumo championships, the outcome of speed dates, or real estate trends in selected suburbs of Chicago. But the difficulty can only be that the evidence-based haruspices aren’t trying hard enough, and some friendly rivalry with the plastromancers is called for. It’s true that none of these findings will last forever, but this constant overturning of old ideas by new discoveries is just part of what makes this such a dynamic time in the field of haruspicy. Many scholars will even tell you that their favorite part of being a haruspex is the frequency with which a new sacrifice over-turns everything they thought they knew about reading the future from a sheep’s liver! We are very excited about the renewed interest on the part of policy-makers in the recommendations of the mantic arts…

And this is when there is enough information to replicate; open access to any data for a paper is rare (economics: <10%) the economics journal Journal of Money, Credit and Banking, which required researchers provide the data & software which could replicate their statistical analyses, discovered that <10% of the submitted materials were adequate for repeating the paper (see “Lessons from the JMCB Archive”). In one cute economics example, replication failed because the dataset had been heavily edited to make participants look better (for more economics-specific critique, see Ioannidis & Doucouliagos 2013). Availability of data, often low⁠, decreases with time⁠, and many studies never get published regardless of whether publication is legally mandated⁠.

Transcription errors in papers seem to be common (possibly due to constantly changing analyses & p-hacking?), and as software and large datasets becomes more inherent to research, the need and the problem of it being possible to replicate will get worse because even mature commercial software libraries can disagree majorly on their computed results to the same mathematical specification (see also Anda et al 2009). And spreadsheets are especially bad, with error rates in the 88% range (“What we know about spreadsheet errors”⁠, Panko 1998); spreadsheets are used in all areas of science, including biology and medicine (see “Error! What biomedical computing can learn from its mistakes”⁠; famous examples of coding errors include Donohue-Levitt & Reinhart-Rogoff), not to mention regular business (eg the London Whale).

Psychology is far from being perfect either; look at the examples in The New Yorker’s “The Truth Wears Off” article (or look at some excerpts from that article). Computer scientist Peter Norvig has written a must-read essay on interpreting statistics, “Warning Signs in Experimental Design and Interpretation”⁠; a number of warning signs apply to many psychological studies. There may be incentive problems: a transplant researcher discovered the only way to publish in Nature his inability to replicate his earlier Nature paper was to officially retract it⁠; another interesting example is when, after Daryl Bem got a paper published in the top journal JPSP demonstrating precognition, the journal refused to publish any replications (failed or successful) because… “‘We don’t want to be the Journal of Bem Replication’, he says, pointing out that other high-profile journals have similar policies of publishing only the best original research.” (Quoted in New Scientist) One doesn’t need to be a genius to understand why psychologist Andrew D. Wilson might snarkily remark “…think about the message JPSP is sending to authors. That message is ‘we will publish your crazy story if it’s new, but not your sensible story if it’s merely a replication’.” (You get what you pay for.) In one large test of the most famous psychology results, 10 of 13 (77%) replicated. The replication rate is under 1⁄3 in one area of psychology touching on genetics. This despite the simple point that replications reduce the risk of publication bias, and increase statistical power, so that a replicated result is more likely to be true⁠. And the small samples of n-back studies and nootropic chemicals are especially problematic. Quoting from Nick Bostrom & Anders Sandberg’s 2006 “Converging Cognitive Enhancements”:

The reliability of research is also an issue. Many of the cognition-enhancing interventions show small effect sizes, which may necessitate very large epidemiological studies possibly exposing large groups to unforeseen risks.

Particularly troubling is the slowdown in drug discovery & medical technology during the 2000s, even as genetics in particular was expected to produce earth-shaking new treatments. One biotech venture capitalist writes:

The company spent $7^$5₂₀₁₁M or so trying to validate a platform that didn’t exist. When they tried to directly repeat the academic founder’s data, it never worked. Upon re-examination of the lab notebooks, it was clear the founder’s lab had at the very least massaged the data and shaped it to fit their hypothesis. Essentially, they systematically ignored every piece of negative data. Sadly this “failure to repeat” happens more often than we’d like to believe. It has happened to us at Atlas [Venture] several times in the past decade…The unspoken rule is that at least 50% of the studies published even in top tier academic journals—Science, Nature, Cell, PNAS, etc…—can’t be repeated with the same conclusions by an industrial lab. In particular, key animal models often don’t reproduce. This 50% failure rate isn’t a data free assertion: it’s backed up by dozens of experienced R&D professionals who’ve participated in the (re)testing of academic findings. This is a huge problem for translational research and one that won’t go away until we address it head on.

Half the respondents to a 2012 survey at one cancer research center reported 1 or more incidents where they could not reproduce published research; two-thirds of those were unable to “ever able to explain or resolve their discrepant findings”, half had trouble publishing results contradicting previous publications, and two-thirds failed to publish contradictory results. An internal Bayer survey of 67 projects (commentary) found that “only in ~20–25% of the projects were the relevant published data completely in line with our in-house findings”, and as far as assessing the projects went:

…despite the low numbers, there was no apparent difference between the different research fields. Surprisingly, even publications in prestigious journals or from several independent groups did not ensure reproducibility. Indeed, our analysis revealed that the reproducibility of published data did not significantly correlate with journal impact factors, the number of publications on the respective target or the number of independent groups that authored the publications. Our findings are mirrored by ‘gut feelings’ expressed in personal communications with scientists from academia or other companies, as well as published observations. [apropos of above] An unspoken rule among early-stage venture capital firms that “at least 50% of published studies, even those in top-tier academic journals, can’t be repeated with the same conclusions by an industrial lab” has been recently reported (see Further information) and discussed 4⁠.

Physics has relatively small sins; “Assessing uncertainty in physical constants” (Henrion & Fischoff 1985); Hanson’s summary:

Looking at 306 estimates for particle properties, 7% were outside of a 98% confidence interval (where only 2% should be). In seven other cases, each with 14 to 40 estimates, the fraction outside the 98% confidence interval ranged from 7% to 57%, with a median of 14%.

Nor is peer review reliable or robust against even low levels of collusion⁠. Scientists who win the Nobel Prize find their other work suddenly being heavily cited⁠, suggesting either that the community either badly failed in recognizing the work’s true value or that they are now sucking up & attempting to look better by association⁠. (A mathematician once told me that often, to boost a paper’s acceptance chance, they would add citations to papers by the journal’s editors—a practice that will surprise none familiar with Goodhart’s law and the use of citations in tenure & grants.)

The former editor Richard Smith amusingly recounts his doubts about the merits of peer review as practiced, and physicist Michael Nielsen points out that peer review is historically rare (just one of Einstein’s 300 papers was peer reviewed; the famous Nature did not institute peer review until 1967), has been poorly studied & not shown to be effective, is nationally biased⁠, erroneously rejects many historic discoveries (one study lists “34 Nobel Laureates whose awarded work was rejected by peer review”⁠; Horrobin 1990 lists other), and catches only a small fraction of errors. And questionable choices or fraud? Forget about it:

A pooled weighted average of 1.97% (N = 7, 95%CI: 0.86–4.45) of scientists admitted to have fabricated, falsified or modified data or results at least once—a serious form of misconduct by any standard—and up to 33.7% admitted other questionable research practices. In surveys asking about the behaviour of colleagues, admission rates were 14.12% (N = 12, 95% CI: 9.91–19.72) for falsification, and up to 72% for other questionable research practices…When these factors were controlled for, misconduct was reported more frequently by medical/​​pharmacological researchers than others.

And psychologists:

We surveyed over 2,000 psychologists about their involvement in questionable research practices, using an anonymous elicitation format supplemented by incentives for honest reporting. The impact of incentives on admission rates was positive, and greater for practices that respondents judge to be less defensible. Using three different estimation methods, we find that the proportion of respondents that have engaged in these practices is surprisingly high relative to respondents’ own estimates of these proportions. Some questionable practices may constitute the prevailing research norm.

In short, the secret sauce of science is not ‘peer review’. It is replication!

Systemic Error Doesn’t Go Away

Why isn’t the solution as simple as eliminating datamining by methods like larger n or pre-registered analyses? Because once we have eliminated the random error in our analysis, we are still left with a (potentially arbitrarily large) systematic error, leaving us with a large total error.

None of these systematic problems should be considered minor or methodological quibbling or foolish idealism: they are systematic biases and as such, they force an upper bound on how accurate a corpus of studies can be even if there were thousands upon thousands of studies, because the total error in the results is made up of random error and systematic error⁠, but while random error shrinks as more studies are done, systematic error remains the same.

A thousand biased studies merely result in an extremely precise estimate of the wrong number.

This is a point appreciated by statisticians and experimental physicists, but it doesn’t seem to be frequently discussed. Andrew Gelman has a fun demonstration of selection bias involving candy⁠, or from pg812–1020 of Chapter 8 “Sufficiency, Ancillarity, And All That” of Probability Theory: The Logic of Science by E.T. Jaynes:

The classical example showing the error of this kind of reasoning is the fable about the height of the Emperor of China. Supposing that each person in China surely knows the height of the Emperor to an accuracy of at least ±1 meter, if there are N = 1,000,000,000 inhabitants, then it seems that we could determine his height to an accuracy at least as good as

$$\frac{1}{\sqrt{1,000,000,000}}m=0.003cm$$ (8-49)

merely by asking each person’s opinion and averaging the results.

The absurdity of the conclusion tells us rather forcefully that the √N rule is not always valid, even when the separate data values are causally independent; it requires them to be logically independent. In this case, we know that the vast majority of the inhabitants of China have never seen the Emperor; yet they have been discussing the Emperor among themselves and some kind of mental image of him has evolved as folklore. Then knowledge of the answer given by one does tell us something about the answer likely to be given by another, so they are not logically independent. Indeed, folklore has almost surely generated a systematic error, which survives the averaging; thus the above estimate would tell us something about the folklore, but almost nothing about the Emperor.

We could put it roughly as follows:

error in estimate = $S\pm \frac{R}{\sqrt{N}}$ (8-50)

where S is the common systematic error in each datum, R is the RMS ‘random’ error in the individual data values. Uninformed opinions, even though they may agree well among themselves, are nearly worthless as evidence. Therefore sound scientific inference demands that, when this is a possibility, we use a form of probability theory (i.e. a probabilistic model) which is sophisticated enough to detect this situation and make allowances for it.

As a start on this, equation (8-50) gives us a crude but useful rule of thumb; it shows that, unless we know that the systematic error is less than about 1⁄3 of the random error, we cannot be sure that the average of a million data values is any more accurate or reliable than the average of ten⁶⁠. As Henri Poincare put it: “The physicist is persuaded that one good measurement is worth many bad ones.” This has been well recognized by experimental physicists for generations; but warnings about it are conspicuously missing in the “soft” sciences whose practitioners are educated from those textbooks.

Or pg1019–1020 Chapter 10 “Physics of ‘Random Experiments’”:

…Nevertheless, the existence of such a strong connection is clearly only an ideal limiting case unlikely to be realized in any real application. For this reason, the law of large numbers and limit theorems of probability theory can be grossly misleading to a scientist or engineer who naively supposes them to be experimental facts, and tries to interpret them literally in his problems. Here are two simple examples:

1. Suppose there is some random experiment in which you assign a probability p for some particular outcome A. It is important to estimate accurately the fraction f of times A will be true in the next million trials. If you try to use the laws of large numbers, it will tell you various things about f; for example, that it is quite likely to differ from p by less than a tenth of one percent, and enormously unlikely to differ from p by more than one percent. But now, imagine that in the first hundred trials, the observed frequency of A turned out to be entirely different from p. Would this lead you to suspect that something was wrong, and revise your probability assignment for the 101’st trial? If it would, then your state of knowledge is different from that required for the validity of the law of large numbers. You are not sure of the independence of different trials, and/​​​or you are not sure of the correctness of the numerical value of p. Your prediction of f for a million trials is probably no more reliable than for a hundred.
2. The common sense of a good experimental scientist tells him the same thing without any probability theory. Suppose someone is measuring the velocity of light. After making allowances for the known systematic errors, he could calculate a probability distribution for the various other errors, based on the noise level in his electronics, vibration amplitudes, etc. At this point, a naive application of the law of large numbers might lead him to think that he can add three significant figures to his measurement merely by repeating it a million times and averaging the results. But, of course, what he would actually do is to repeat some unknown systematic error a million times. It is idle to repeat a physical measurement an enormous number of times in the hope that “good statistics” will average out your errors, because we cannot know the full systematic error. This is the old “Emperor of China” fallacy…

Indeed, unless we know that all sources of systematic error—recognized or unrecognized—contribute less than about one-third the total error, we cannot be sure that the average of a million measurements is any more reliable than the average of ten. Our time is much better spent in designing a new experiment which will give a lower probable error per trial. As Poincare put it, “The physicist is persuaded that one good measurement is worth many bad ones.”⁷ In other words, the common sense of a scientist tells him that the probabilities he assigns to various errors do not have a strong connection with frequencies, and that methods of inference which presuppose such a connection could be disastrously misleading in his problems.

Schlaifer much earlier made the same point in Probability and Statistics for Business Decisions: an Introduction to Managerial Economics Under Uncertainty, Schlaifer 1959⁠, pg488–489 (see also Meng 2018⁠/​Shirani-Mehr et al 2018):

31.4.3 Bias and Sample Size

In Section 31.2.6 we used a hypothetical example to illustrate the implications of the fact that the variance of the mean of a sample in which bias is suspected is

$${\sigma }^2\left(x\right)={\sigma }^2\left(\tilde{\beta }\right)+\frac{1}{n}{\sigma }^2\left(\widetilde{ϵ}\right)\frac{N-n}{N-1}$$

so that only the second term decreases as the sample size increases and the total can never be less than the fixed value of the first term. To emphasize the importance of this point by a real example we recall the most famous sampling fiasco in history, the presidential poll conducted by the Literary Digest in 1936⁠. Over 2 million registered voters filled in and returned the straw ballots sent out by the Digest, so that there was less than one chance in 1 billion of a sampling error as large as 2⁄10 of one percentage point⁸⁠, and yet the poll was actually off by nearly 18 percentage points: it predicted that 54.5 per cent of the popular vote would go to Landon, who in fact received only 36.7 per cent.^{9 10}

Since sampling error cannot account for any appreciable part of the 18-point discrepancy, it is virtually all actual bias. A part of this total bias may be measurement bias due to the fact that not all people voted as they said they would vote; the implications of this possibility were discussed in Section 31.3. The larger part of the total bias, however, was almost certainly selection bias. The straw ballots were mailed to people whose names were selected from lists of owners of telephones and automobiles and the subpopulation which was effectively sampled was even more restricted than this: it consisted only of those owners of telephones and automobiles who were willing to fill out and return a straw ballot. The true mean of this subpopulation proved to be entirely different from the true mean of the population of all United States citizens who voted in 1936.

It is true that there was no evidence at the time this poll was planned which would have suggested that the bias would be as great as the 18 percentage points actually realized, but experience with previous polls had shown biases which would have led any sensible person to assign to $\tilde{\beta }$ a distribution with $\sigma \left(\tilde{\beta }\right)$ equal to at least 1 percentage point. A sample of only 23,760 returned ballots, one 1⁄100th the size actually used, would have given $\sigma \left(ϵ\right)$ a value of only 1⁄3 percentage point, so that the standard deviation of x would have been

$$\sigma \left(x\right)=\sqrt{{\sigma }^2\left(\tilde{\beta }\right)+{\sigma }^2\left(ϵ\right)}=\sqrt{1+.11}=1.05$$

percentage points. Using a sample 100 times this large reduced σ(ε) from 1⁄3 point to virtually zero, but it could not affect $\sigma \left(\tilde{\beta }\right)$ and thus on the most favorable assumption could reduce σ(x) only from 1.05 points to 1 point. To collect and tabulate over 2 million additional ballots when this was the greatest gain that could be hoped for was obviously ridiculous before the fact and not just in the light of hindsight.

What’s particularly sad is when people read something like this and decide to rely on anecdotes, personal experiments, and alternative medicine where there are even more systematic errors and no way of reducing random error at all! Science may be the lens that sees its own flaws⁠, but if other epistemologies do not boast such long detailed self-critiques, it’s not because they are flawless… It’s like that old Jamie Zawinski quote: Some people, when faced with the problem of mainstream medicine & epidemiology having serious methodological weaknesses, say “I know, I’ll turn to non-mainstream medicine & epidemiology. After all, if only some medicine is based on real scientific method and outperforms placebos, why bother?” (Now they have two problems.) Or perhaps Isaac Asimov: “John, when people thought the earth was flat, they were wrong. When people thought the earth was spherical, they were wrong. But if you think that thinking the earth is spherical is just as wrong as thinking the earth is flat, then your view is wronger than both of them put together.”

See Also

• How Often Does Correlation = Causality?

• Why Correlation Usually ≠ Causation: Causal Nets Cause Common Confounding

• Littlewood’s Law and the Global Media

• The Existential Risk of Math Error

• QUestionable Research Findings:

  • Leprechaun hunting
  • “Hydrocephalus and Intelligence: The Hollow Men”
  • On the ‘Mouse Utopia’ experiment
  • Dual N-Back Meta-Analysis
  • Lunar circadian rhythms
  • On the Jeanne Calment longevity anomaly
  • Munksgaard et al 2016, “A replication and methodological critique of the study ‘Evaluating drug trafficking on the Tor Network’”

Appendix