spurious p values

The Statistics Wars and Intellectual Conflicts of Interest

.

My editorial in Conservation Biology is published (open access): “The Statistical Wars and Intellectual Conflicts of Interest”. Share your comments, here and/or send a separate item (to Error), if you wish, for possible guest posting*. (All readers are invited to a special January 11 Phil Stat Session with Y. Benjamini and D. Hand described here.) Here’s most of the editorial:

The Statistics Wars and Intellectual Conflicts of Interest

How should journal editors react to heated disagreements about statistical significance tests in applied fields, such as conservation science, where statistical inferences often are the basis for controversial policy decisions? They should avoid taking sides. They should also avoid obeisance to calls for author guidelines to reflect a particular statistical philosophy or standpoint. The question is how to prevent the misuse of statistical methods without selectively favoring one side.

The statistical‐significance‐test controversies are well known in conservation science. In a forum revolving around Murtaugh’s (2014) “In Defense of P values,” Murtaugh argues, correctly, that most criticisms of statistical significance tests “stem from misunderstandings or incorrect interpretations, rather than from intrinsic shortcomings of the P value” (p. 611). However, underlying those criticisms, and especially proposed reforms, are often controversial philosophical presuppositions about the proper uses of probability in uncertain inference. Should probability be used to assess a method’s probability of avoiding erroneous interpretations of data (i.e., error probabilities) or to measure comparative degrees of belief or support? Wars between frequentists and Bayesians continue to simmer in calls for reform.

Consider how, in commenting on Murtaugh (2014), Burnham and Anderson (2014 : 627) aver that “P‐values are not proper evidence as they violate the likelihood principle (Royall, 1997).” This presupposes that statistical methods ought to obey the likelihood principle (LP), a long‐standing point of controversy in the statistics wars. The LP says that all the evidence is contained in a ratio of likelihoods (Berger & Wolpert, 1988). Because this is to condition on the particular sample data, there is no consideration of outcomes other than those observed and thus no consideration of error probabilities. One should not write this off because it seems technical: methods that obey the LP fail to directly register gambits that alter their capability to probe error. Whatever one’s view, a criticism based on presupposing the irrelevance of error probabilities is radically different from one that points to misuses of tests for their intended purpose—to assess and control error probabilities.

Error control is nullified by biasing selection effects: cherry‐picking, multiple testing, data dredging, and flexible stopping rules. The resulting (nominal) p values are not legitimate p values. In conservation science and elsewhere, such misuses can result from a publish‐or‐perish mentality and experimenter’s flexibility (Fidler et al., 2017). These led to calls for preregistration of hypotheses and stopping rules–one of the most effective ways to promote replication (Simmons et al., 2012). However, data dredging can also occur with likelihood ratios, Bayes factors, and Bayesian updating, but the direct grounds to criticize inferences as flouting error probability control is lost. This conflicts with a central motivation for using p values as a “first line of defense against being fooled by randomness” (Benjamini, 2016). The introduction of prior probabilities (subjective, default, or empirical)–which may also be data dependent–offers further flexibility.

Signs that one is going beyond merely enforcing proper use of statistical significance tests are that the proposed reform is either the subject of heated controversy or is based on presupposing a philosophy at odds with that of statistical significance testing. It is easy to miss or downplay philosophical presuppositions, especially if one has a strong interest in endorsing the policy upshot: to abandon statistical significance. Having the power to enforce such a policy, however, can create a conflict of interest (COI). Unlike a typical COI, this one is intellectual and could threaten the intended goals of integrity, reproducibility, and transparency in science.

If the reward structure is seducing even researchers who are aware of the pitfalls of capitalizing on selection biases, then one is dealing with a highly susceptible group. For a journal or organization to take sides in these long-standing controversies—or even to appear to do so—encourages groupthink and discourages practitioners from arriving at their own reflective conclusions about methods.

The American Statistical Association (ASA) Board appointed a President’s Task Force on Statistical Significance and Replicability in 2019 that was put in the odd position of needing to “address concerns that a 2019 editorial [by the ASA’s executive director (Wasserstein et al., 2019)] might be mistakenly interpreted as official ASA policy” (Benjamini et al., 2021)—as if the editorial continues the 2016 ASA Statement on p-values (Wasserstein & Lazar, 2016). That policy statement merely warns against well‐known fallacies in using p values. But Wasserstein et al. (2019) claim it “stopped just short of recommending that declarations of ‘statistical significance’ be abandoned” and announce taking that step. They call on practitioners not to use the phrase statistical significance and to avoid p value thresholds. Call this the no‐threshold view. The 2016 statement was largely uncontroversial; the 2019 editorial was anything but. The President’s Task Force should be commended for working to resolve the confusion (Kafadar, 2019). Their report concludes: “P-values are valid statistical measures that provide convenient conventions for communicating the uncertainty inherent in quantitative results” (Benjamini et al., 2021). A disclaimer that Wasserstein et al., 2019 was not ASA policy would have avoided both the confusion and the slight to opposing views within the Association.

The no‐threshold view has consequences (likely unintended). Statistical significance tests arise “to test the conformity of the particular data under analysis with [a statistical hypothesis] H0 in some respect to be specified” (Mayo & Cox, 2006: 81). There is a function D of the data, the test statistic, such that the larger its value (d), the more inconsistent are the data with H0. The p value is the probability the test would have given rise to a result more discordant from H0 than d is were the results due to background or chance variability (as described in H0). In computing p, hypothesis H0 is assumed merely for drawing out its probabilistic implications. If even larger differences than d are frequently brought about by chance alone (p is not small), the data are not evidence of inconsistency with H0. Requiring a low pvalue before inferring inconsistency with H0 controls the probability of a type I error (i.e., erroneously finding evidence against H0).

Whether interpreting a simple Fisherian or an N‐P test, avoiding fallacies calls for considering one or more discrepancies from the null hypothesis under test. Consider testing a normal mean H0: μ ≤ μ0 versus H1: μ > μ0. If the test would fairly probably have resulted in a smaller p value than observed, if μ = μ1 were true (where μ1 = μ0 + γ, for γ > 0), then the data provide poor evidence that μ exceeds μ1. It would be unwarranted to infer evidence of μ > μ1. Tests do not need to be abandoned when the fallacy is easily avoided by computing p values for one or two additional benchmarks (Burgman, 2005; Hand, 2021; Mayo, 2018; Mayo & Spanos, 2006).

The same is true for avoiding fallacious interpretations of nonsignificant results. These are often of concern in conservation, especially when interpreted as no risks exist. In fact, the test may have had a low probability to detect risks. But nonsignificant results are not uninformative. If the test very probably would have resulted in a more statistically significant result were there a meaningful effect, say μ > μ1 (where μ1 = μ0 + γ, for γ > 0), then the data are evidence that μ < μ1. (This is not to infer μ ≤ μ0.) “Such an assessment is more relevant to specific data than is the notion of power” (Mayo & Cox, 2006: 89). This also matches inferring that μ is less than the upper bound of the corresponding confidence interval (at the associated confidence level) or a severity assessment (Mayo, 2018). Others advance equivalence tests (Lakens, 2017; Wellek, 2017). An N‐P test tells one to specify H0 so that the type I error is the more serious (considering costs); that alone can alleviate problems in the examples critics adduce (H0would be that the risk exists).

Many think the no‐threshold view merely insists that the attained p value be reported. But leading N‐P theorists already recommend reporting p, which “gives an idea of how strongly the data contradict the hypothesis…[and] enables others to reach a verdict based on the significance level of their choice” (Lehmann & Romano, 2005: 63−64). What the no‐threshold view does, if taken strictly, is preclude testing. If one cannot say ahead of time about any result that it will not be allowed to count in favor of a claim, then one does not test that claim. There is no test or falsification, even of the statistical variety. What is the point of insisting on replication if at no stage can one say the effect failed to replicate? One may argue for approaches other than tests, but it is unwarranted to claim by fiat that tests do not provide evidence. (For a discussion of rival views of evidence in ecology, see Taper & Lele, 2004.)

Many sign on to the no‐threshold view thinking it blocks perverse incentives to data dredge, multiple test, and p hack when confronted with a large, statistically nonsignificant p value. Carefully considered, the reverse seems true. Even without the word significance, researchers could not present a large (nonsignificant) p value as indicating a genuine effect. It would be nonsensical to say that even though more extreme results would frequently occur by random variability alone that their data are evidence of a genuine effect. The researcher would still need a small value, which is to operate with a threshold. However, it would be harder to hold data dredgers culpable for reporting a nominally small p value obtained through data dredging. What distinguishes nominal p values from actual ones is that they fail to meet a prespecified error probability threshold.

 

While it is well known that stopping when the data look good inflates the type I error probability, a strict Bayesian is not required to adjust for interim checking because the posterior probability is unaltered. Advocates of Bayesian clinical trials are in a quandary because “The [regulatory] requirement of Type I error control for Bayesian [trials] causes them to lose many of their philosophical advantages, such as compliance with the likelihood principle” (Ryan etal., 2020: 7).

It may be retorted that implausible inferences will indirectly be blocked by appropriate prior degrees of belief (informative priors), but this misses the crucial point. The key function of statistical tests is to constrain the human tendency to selectively favor views they believe in. There are ample forums for debating statistical methodologies. There is no call for executive directors or journal editors to place a thumb on the scale. Whether in dealing with environmental policy advocates, drug lobbyists, or avid calls to expel statistical significance tests, a strong belief in the efficacy of an intervention is distinct from its having been well tested. Applied science will be well served by editorial policies that uphold that distinction.

For the acknowledgments and references, see the full editorial here.

I will cite as many (constructive) readers’ views as I can at the upcoming forum with Yoav Benjamini and David Hand on January 11 on zoom (see this post). *Authors of articles I put up as guest posts or cite at the Forum will get a free copy of my Statistical Inference as Severe Testing: How to Get Beyond the Statistics Wars (CUP, 2018).

Categories: significance tests, spurious p values, stat wars and their casualties, strong likelihood principle | 3 Comments

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*

.

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. Continue reading

Categories: Bayesian/frequentist, fallacy of rejection, P-values, reforming the reformers, spurious p values | 3 Comments

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

.

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

Categories: Bayesian/frequentist, fallacy of rejection, P-values, reforming the reformers, spurious p values

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)?

 

Categories: P-values, spurious p values, statistical tests, Statistics

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

.

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.

 

 

Illustration by Slate

                 Illustration by Slate

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

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

screen-shot-2016-10-26-at-10-23-07-pm

.

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

gigerenzer-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

Categories: Fisher, frequentist/Bayesian, Gigerenzer, Gigerenzer, P-values, spurious p values, Statistics

Some statistical dirty laundry: have the stains become permanent?

images

.

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

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

images

The unpopular P-value is invited to dance.

  1. The Paradox of Replication

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.)

Continue reading

Categories: replication research, reproducibility, spurious p values, Statistics

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

Objectivity 1: Will the Real Junk Science Please Stand Up?

.

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

Some statistical dirty laundry

Objectivity 1: Will the Real Junk Science Please Stand Up?

.

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

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

cropped-qqqq.jpg 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.
Continue reading

Categories: Higgs, spurious p values, Statistics

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

YoungPhoto2008

images-6S. 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.

Categories: Phil6334, science communication, spurious p values, Statistical fraudbusting, Statistics | Tags:

capitalizing on chance (ii)

Mayo playing the slots

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

Categories: junk science, selection effects, spurious p values, Statistical fraudbusting, Statistics

Probability that it is a statistical fluke [i]

cropped-qqqq.jpgFrom 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

Categories: Error Statistics, Severity vs Posterior Probabilities, spurious p values

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

500x307-embo-reports-vol-73-meeting-report-fig-1-abcAn 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

Some statistical dirty laundry

Objectivity 1: Will the Real Junk Science Please Stand Up?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.images
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

“Bad statistics”: crime or free speech?

wavy-capital3Hunting 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

Blog at WordPress.com.