spurious p values

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.

 

 

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.

P-values are tricky business, but here’s the basics on how they work: Let’s say I’m conducting a drug trial, and I want to know if people who take drug A are more likely to go deaf than if they take drug B. I’ll state that my hypothesis is “drugs A and B are equally likely to make someone go deaf,” administer the drugs, and collect the data. The data will show me the number of people who went deaf on drugs A and B, and the p-value will give me an indication of how likely it is that the difference in deafness was due to random chance rather than the drugs. If the p-value is lower than 0.05, it means that the chance this happened randomly is very small—it’s a 5 percent chance of happening, meaning it would only occur 1 out of 20 times if there wasn’t a difference between the drugs. If the threshold is lowered to 0.005 for something to be considered significant, it would mean that the chances of it happening without a meaningful difference between the treatments would be just 1 in 200.

On its face, this doesn’t seem like a bad idea. If this change requires scientists to have more robust evidence before they can come to conclusions, it’s easy to think it’s a step in the right direction. But one of the issues at the heart of making this change is that it seems to assume there’s currently a consensus around how p-value ought to be used and this consensus could just be tweaked to be stronger.

P-value use already varies by scientific field and by journal policies within those fields. Several journals in epidemiology, where the stakes of bad science are perhaps higher than in, say, psychology (if they mess up, people die), have discouraged the use of p-values for years. And even psychology journals are following suit: In 2015, Basic and Applied Social Psychology, a journal that has been accused of bad statistical (and experimental) practice, banned the use of p-values. Many other journals, including PLOS Medicine and Journal of Allergy and Clinical Immunology, actively discourage the use of p-values and significance testing already.

On the other hand, the New England Journal of Medicine, one of the most respected journals in that field, codes the 0.05 threshold for significance into its author guidelines, saying “significant differences between or among groups (i.e P<.05) should be identified in a table.” That may not be an explicit instruction to treat p-values less than 0.05 as significant, but an author could be forgiven for reading it that way. Other journals, like the Journal of Neuroscience and the Journal of Urology, do the same.

Another group of journals—including Science, Nature, and Cell—avoid giving specific advice on exactly how to use p-values; rather, they caution against common mistakes and emphasize the importance of scientific assumptions, trusting the authors to respect the nuance of any statistics tools. Deborah Mayo, award-wining philosopher of statistics and professor at Virginia Tech, thinks this approach to statistical significance, where various fields have different standards, is the most appropriate. Strict cutoffs, regardless of where they fall, are generally bad science.

Mayo was skeptical that it would have the kind of widespread benefit the authors assumed. Their assessment suggested tightening the threshold would reduce the rate of false positives—results that look true but aren’t—by a factor of two. But she questioned the assumption they had used to assess the reduction of false positives—that only 1 in 10 hypotheses a scientist tests is true. (Mayo said that if that were true, perhaps researchers should spend more time on their hypotheses.)

But more broadly, she was skeptical of the idea that lowering the informal p-value threshold will help fix the problem, because she’s doubtful such a move will address “what almost everyone knows is the real cause of nonreproducibility”: the cherry-picking of subjects, testing hypothesis after hypothesis until one of them is proven correct, and selective reporting of results and methodology.

There are plenty of other ways that scientists are testing to help address the replication crisis. There’s the move toward pre-registration of studies before analyzing data, in order to avoid fishing for significance. Researchers are also now encouraged to make data and code public so a third party can rerun analyses efficiently and check for discrepancies. More negative results are being published. And, perhaps most importantly, researchers are actually conducting studies to replicate research that has already been published. Tightening standards around p-values might help, but the debate about reproducibility is more than just a referendum on the p-value. The solution will need to be more than that as well.

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 [i] We did not discuss that recent test ban(“Don’t ask don’t tell”).  If we had, I might have pointed him to my post on “P-value madness”. 

Link to Nick Thieme’s Slate article:Will Lowering P-Value Thresholds Help Fix Science? P-values are already all over the map, and they’re also not exactly the problem.”

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)

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

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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

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 | 11 Comments

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)

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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 | 21 Comments

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

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

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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

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

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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?

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 | 7 Comments

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: | 12 Comments

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 | 4 Comments

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 | 22 Comments

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 | 13 Comments

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 | 6 Comments

“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 | 27 Comments

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