Tuesday, January 26, 2021

I tried to report scientific misconduct. How did it go?

This is the story of how I found what I believe to be scientific misconduct and what happened when I reported it.

Science is supposed to be self-correcting. To test whether science is indeed self-correcting, I tried reporting this misconduct via several mechanisms of scientific self-correction. The results have shown me that psychological science is largely defenseless against unreliable data.

I want to share this story with you so that you understand a few things. You should understand that there are probably a few people in your field producing work that is either fraudulent or so erroneous it may as well be fraudulent. You should understand that their work is cited in policy statements and included in meta-analyses. You should understand that, if you want to see the data or to report concerns, those things happen according to the inclinations of the editor-in-chief at the journal. You should understand that if the editor-in-chief is not inclined to help you, they generally not accountable to anyone and they can always ignore you until the statute of limitations runs out.

Basically, it is very easy to generate unreliable data, and it is very difficult to get it retracted.

Qian Zhang

Two years ago, I read a journal article that appeared to have gibberish for all its statistics (Zhang, Espelage, & Zhang, 2018). None of the numbers in the tables added up: the values didn't match the values, the values didn't match the means and SDs, and the degrees of freedom didn't match the sample size. This was distressing because the sample size was a formidable 3,000 participants. If these numbers were wrong, they were going to receive a lot of weight in future meta-analyses. I sent the editor a note saying "Hey, none of these numbers make sense." The editor said they'd ask the authors to correct, and I moved on with my life.


Figure 1. Table from Zhang, Espelage, & Zhang, (2018). The means and SDs don’t make sense, and the significance asterisks are incorrect given the F values.

Then I read the rest of Dr. Zhang's first-authored articles and realized there was a broader, more serious problem – one that I am still spending time and energy trying to clean up, two years later.


Problems in Qian Zhang’s articles

Zhang’s papers would often report impossible statistics. Many papers had subgroup means that could not be combined to yield the grand mean. For example, one paper reported mean task scores of 8.98ms and 6.01ms for males and females, respectively, but a grand mean task score of 23ms.

Other papers had means and SDs that were impossible given the range. For example, one study reported a sample of 3,000 children with ages ranging from 10 to 20 years (M = 15.76, SD = 1.18), of which 1,506 were between ages 10 and 14 and 1,494 were between ages 15 and 20. If you put those numbers into SPRITE, you will find that, to meet the reported mean and SD of age, all the participants must be between the ages of 14 and 19, and only about 500 participants could be age 14.

More seriously still, tables of statistical output seemed to be recycled from paper to paper. Two different articles describing two different experiments on two different populations would come up with very similar cell means and F values. Even if one runs exactly the same experiment twice, sampling error means that the odds of getting all six cells of a 2 × 3 design to come up again within a few decimal points are quite low. The odds of getting them on an entirely different experiment years later in a different population would be smaller still.

As an example, consider this table, published in Zhang, Espelage, and Rost (2018)Youth and Society (Panel A)in which 2,000 children (4th-6th grade) perform a two-color emotion Stroop task. The means and F values closely match the same values as a sample of 74 high schoolers (Zhang, Xiong, & Tian, 2013Scientific Research: Health, Panel B) and a sample of 190 high schoolers (Zhang, Zhang, & Wang, 2013Scientific Research: Psychology, Panel C).

Figure 2. Three highly similar tables from three different experiments by Zhang and colleagues. The degree of similarity for all nine values of the table is suspiciously high.

Dr. Zhang publishes some corrigenda 

After my first quick note to Youth and Society that Zhang’s p values didn't match the F values, Dr. Zhang started submitting corrections to journals. What was remarkable about these corrections is that they would simply add an integer to the F values so that they would be statistically significant.

Consider, for example, this correction at Personality and Individual Differences (Zhang, Tian, Cao, Zhang, & Rodkin, 2016):

Figure 3. An uninterpretable ANOVA table is corrected by the addition or subtraction of an integer value from its F statistics.

The correction just adds 2 or 3 onto the nonsignificant values to make them match their asterisks, and it subtracts 5 from the significant F value to make it match its lack of asterisks.

Or this correction to 
Zhang, Espelage, and Zhang (2018)Youth and Society, now retracted:


Figure 4. Nonsignificant F values become statistically significant through the addition of a tens digit. Note that these should now have three asterisks rather than one and two, respectively.

Importantly, none of the other summary or inferential statistics had to be changed in these corrigenda, as one might expect if there was an error in analysis. Instead, it was a simple matter of clobbering the F values so that they’d match the significance asterisks.

Asking for raw data

While I was investigating Zhang’s work from 2018 and earlier, he published another massive 3,000-participant experiment in Aggressive Behavior (Zhang et al., 2019). Given the general sketchiness of the reports, I was getting anxious about the incredible volume of data Zhang was publishing. 

I asked Dr. Zhang if I could see the data from these studies to try to understand what had happened. He refused, saying only the study team could see the data. 

So, I decided I’d ask the study team. I asked Zhang’s American co-author if they had seen the data. They said they hadn't. I suggested they ask for the data. They said Zhang refused. I asked them if they thought that was odd. They said, no, "It's a China thing."


Reporting Misconduct to the Institution

Given the recycling of tables across studies, the impossible statistics, the massive sample sizes, the secrecy around the data, and the corrigenda which had simply bumped the F values into significance, I suspected I had found research misconduct.  In May 2019, I wrote up a report and sent it to the Chairman of the Academic Committee at his institution, Southwest University Chongqing. You can read that report here.

A month later, I was surprised to get an email from Dr. Zhang. It was the raw data from the Youth & Society article I had previously asked for and been refused.

Looking at the raw data revealed a host of suspicious issues. For starters, participants were supposed to be randomly assigned to movie, but girls and students with high trait aggression were dramatically more likely to be assigned to the nonviolent movie. 

There was something else about the reaction time data that is a little more technical but very serious. Basically, reaction time data on a task like the Stroop should show within-subject effects (some conditions have faster RTs than others) and between-subject effects (some people are faster than others). Consequently, even an incongruent trial from Quick Draw McGraw could be faster than a congruent trial from Slowpoke Steven.

Because of these between-subject effects, there should be a correlation between a subject’s reaction times in one condition and their reaction times in the other. If you look at color-Stroop data I grabbed from a reliable source on the OSF, you can see that correlation is very strong. 

Figure 5. The correlation between subjects' mean congruent-word RT and mean incongruent-word RT in a color-word Stroop task. Data from Lin, Inzlicht, Saunders, & Friese (2019).

If you look at Zhang’s data, you see the correlation is completely absent. You might also notice that the distribution of subjects’ means is weirdly boxy, unlike the normal or log-normal distribution you might expect.

Figure 6. The correlation between subjects' mean aggressive-word RT and nonaggressive-word RT in an aggressive-emotion Stroop task. Data from Zhang, Espelage, and Rost (2018). The distribution of averages is odd, and the correlation unusually weak.

There was no way the study was randomized, and there was no way that the study data was reliable Stroop data. I wrote an additional letter to the institution detailing these oddities. You can read that additional letter here.

A month after that, Southwest University cleared Dr. Zhang of all charges.

The letter I received declared: "Dr. Zhang Qian was deficient in statistical knowledge and research methods, yet there is insufficient evidence to prove that data fraud [sic]." It explained that Dr. Zhang was just very, very bad at statistics and would be receiving remedial training and writing some corrigenda. The letter noted that, as I had pointed out, the ANOVA tables were gibberish and the degrees of freedom did not match the reported sample sizes. It also noted that the "description of the procedure and the object of study lacks logicality, and there is a suspicion of contradiction in the procedure and inconsistency in the sample," whatever that means.

However, the letter did not comment on the strongest pieces of evidence for misconduct: the recycled tables, the impossible statistics, and the unrealistic properties of the raw data. I pressed the Chairman for comment on these issues. 

After four months, the Chairman replied that the two experts they consulted determined that "these discussions belong to academic disputes." I asked to see the report from the experts. I did not receive a reply.


Reporting Misconduct to the Journals

The institution being unwilling to fix anything, I decided to approach the journals. In September and October 2019, I sent each journal a description of the problems in the specific article each had published, as well as a description of the broader evidence for misconduct across articles. 

I hoped that these letters would inspire some swift retractions, or at least, expressions of concern. I would be disappointed.

Some journals appeared to make good-faith attempts to investigate and retract. Other journals have been less helpful.

The Good Journals

Youth and Society reacted the most swiftly, retracting both articles two months later

Personality and Individual Differences took 10 months to decide to retract. In July 2020, the editor showed me a retraction notice for the article. I am still waiting for the retraction notice to be published. It was apparently lost when changing journal managers; once recovered, it then had to be sent to the authors and publisher for another round of edits and approvals.

Computers in Human Behavior is still investigating. The editor received my concerns with an appropriate degree of attention, but it seems there was some confusion about whether the editor or the publisher is supposed to investigate that has slowed down the process.

I felt these journals generally did their best, and the slowness of the process likely comes from the bureaucracy of the process and the inexperience editors have with that process. Other journals, I felt, did not make such an attempt.

Aggressive Behavior

In October 2019, Zhang sent me the data from his Aggressive Behavior article. I found the data had the same bizarre features that I had found when I received the raw data from Zhang's now-retracted Youth and Society article. I wrote a letter detailing my concerns and sent it to Aggressive Behavior's editor in chief, Craig Anderson. 

The letter, which you can read here, detailed four concerns. One was about the plausibility of the average Stroop effect reported, which was very large. Another was about failures of random assignment: chi-squared tests found the randomly-assigned conditions differed in sex and trait aggression, with p values of less than one in a trillion. The other two concerns regarded the properties of the raw data.

It took three months and two emails to the full editorial board to receive acknowledgement of my letter. Another four months after that, the journal notified me that it would investigate. 

Now, fifteen months after the submission of my complaint, the journal has made the disappointing decision to correct the article. The correction explains away the failures of randomization as an error in translation; the authors now claim that they let participants self-select their condition. This is difficult for me to believe. The original article’s stressed multiple times its use of random assignment and described the design as a "true experiment.” They also had perfectly equal samples per condition ("n = 1,524 students watched a 'violent' cartoon and n = 1,524 students watched a 'nonviolent' cartoon.") which is exceedingly unlikely to happen without random assignment. 

The correction does not mention the multiple suspicious features of the raw data. 

This correction has done little to assuage my concerns. I feel it is closer to a cover-up. I will express my displeasure with the process at Aggressive Behavior in greater detail in a future post.


Zhang’s newest papers

Since I started contacting journals, Zhang has published four new journal articles and one ResearchSquare preprint. I also served as a peer reviewer on two of his other submissions: One was rejected, and the other Zhang withdrew when I repeatedly requested raw data and materials.

These newest papers all carefully avoid the causes of my previous complaints. I had complained it was unlikely that Zhang should collect 3,000 subjects every experiment; the sample sizes in the new studies range from 174 to 480. I had complained that the distribution of aggressive-trial and nonaggressive-trial RTs within a subject didn’t make sense; the new studies analyze and present only the aggressive-trial RTs, or they report a measure that does not require RTs.

Two papers include a public dataset as part of the online supplement, but the datasets contain only the aggressive-trial RTs. When I contacted Zhang, he refused to share the nonaggressive-trial RTs. He has also refused to share the accuracy data for any trials. This might be a strategy to avoid tough questions about the kind of issues I found in his Youth & Society and Aggressive Behavior articles. 

Because Zhang refused me access to the data, I had to try asking the editors at those journals to enforce the APA Code of Ethics section 8.14 which requires sharing of data for the purpose of verifying results.

At Journal of Experimental Child Psychology, I asked editor-in-chief David Bjorklund to intervene. Dr. Bjorklund has asked Dr. Zhang to provide the requested data. I thank him for upholding the Code of Ethics. A month and half have passed since Dr. Bjorklund's intervention, and I yet to receive the requested data and materials from Dr. Zhang.

At Children and Youth Services Review, I asked editor-in-chief Duncan Lindsey to intervene. Zhang claimed that the data consisted only of aggressive-trial RTs, and that he could not share the program because it “contained many private information of children and had copyrights.”

I explained my case to Lindsey. Lindsey sent me nine words — "You will need to solve this with the authors." — and never replied again.

Dr. Lindsey's failure to uphold the Code of Ethics at his journal is shameful. Scholars should be aware that Children and Youth Services Review has chosen not to enforce data-sharing standards, and research published in Children and Youth Services Review cannot be verified through inspection of the raw data.

I have not yet asked for the data behind Zhang’s new articles in Cyberpsychology, Behavior, and Social Networking or Journal of Aggression, Maltreatment, & Trauma.


I was curious to see how the self-correcting mechanisms of science would respond to what seemed to me a rather obvious case of unreliable data and possible research misconduct. It turns out Brandolini’s Law still holds: “The amount of energy needed to refute bullshit is an order of magnitude larger than to produce it.” However, I was not prepared to be resisted and hindered by the self-correcting institutions of science itself.

I was disappointed by the response from Southwest University. Their verdict has protected Zhang and enabled him to continue publishing suspicious research at great pace. However, this result does not seem particularly surprising given universities' general unwillingness to investigate their own and China's general eagerness to clear researchers of fraud charges.

I have also generally been disappointed by the response from journals. It turns out that a swift two-month process like the one at Youth and Society is the exception, not the norm.

In the cases that an editor in chief has been willing to act, the process has been very slow, moving only in fits and starts. I have read before that editors and journals have very little time or resources to investigate even a single case of misconduct. It is clear to me that the publishing system is not ready to handle misconduct at scale.

In the cases that an editor in chief has been unwilling to act, there is little room for appeal. Editors can act busy and ignore a complainant, and they can get indignant if one tries to go around them to the rest of the editorial board. It is not clear who would hold the editors accountable, or how. I have little leverage over Craig Anderson or Duncan Lindsey besides my ability to bad-mouth them and their journals in this report. At best, they might retire in another year or two and I could have a fresh editor with whom to plead my case.

The clearest consequence of my actions has been that Zhang has gotten better at publishing. Every time I reported an irregularity with his data, his next article would not feature that irregularity. In essence, each technique for pointing out the implausibility of the data can be used only once, because an editor’s or university’s investigation consists of showing the authors all the irregularities and asking for benign explanations. This is a serious problem when even weak explanations like “I didn’t understand what randomized assignment means” or “I’m just very bad at statistics” are considered acceptable.

Zhang has reported experiments with sample sizes totaling to more than 11,000 participants (8,000 given the Aggressive Behavior correction). This is an amount of data that rivals entire meta-analyses and ManyLabs projects. If this data is flawed, it will have serious consequences for reviews and meta-analyses.

In total, trying to get these papers retracted has been much more difficult, and rather less rewarding, than I had expected. The experience has led me to despair for the quality and integrity of our science. If data this suspicious can’t get a swift retraction, it must be impossible to catch a fraud equipped with skills, funding, or social connections.

Thursday, October 15, 2020

Fraud and Erroneous Judgment: Varieties of Deception in the Social Sciences (1995)

Killing time in the UChicago stacks in the summer of 2019, I found a book from 1995 called Fraud and Erroneous Judgment in the Social Sciences. It's been an interesting read, because despite having been written nearly 25 years ago, much of it reads like it was written today. Specifically, there is very little substance about actually preventing, detecting, or prosecuting fraud, presumably because all these things are very difficult to do. 

Instead, a substantial portion of the text is dedicated to the easier task of fighting the culture war. Nearly half the book consists of polemics from scientists who think their ability to speak hard truths about sexual assault or intelligence or race or whatever has been suppressed by the bleeding hearts. This is particularly depressing and unhelpful when you see that two of the thirteen chapters are written by Linda Gottfredson and J. Phillippe Rushton, scientists receiving funding from the Pioneer Fund, an organization founded to study and promote eugenics.


For a text that is notionally about fraud, there is very little substance about actual fraud. Instead, most of the chapters are dedicated to the latter topic of "fallible judgment". Only three instances of research misconduct in psychology are discussed. Two of them appear in brief bullet points in the first chapter: In one, a psychologist fabricated data to demonstrate the efficacy of a drug for preventing self-harm in the mentally disabled; in the other, a researcher may have massaged his data to overstate the potential harms of low levels of lead exposure.

The third case consists of the allegations surrounding Cyril Burt. Cyril Burt was an early behavior geneticist. He argued that intelligence was heritable, and he demonstrated this through studies of the similarity of identical twins raised apart.

Burt was unpopular at the time because the view that intelligence was heritable sounded to many like Nazi ideology. While he was alive, people protested him as a far-right ideologue. (Other hereditarians experienced similar treatment; Hans Eysenck reportedly needed bodyguards as a result of his 1971 views that some of the Black-White intelligence gap was genetic in nature.) 

Five years after his death, allegations arose that Burt had invented a number of his later samples. These allegations claimed that Burt, having found an initial sample that supported his hypothesis, and frustrated by the public resistance to his findings as well as the challenge of finding more identical twins raised apart, decided to help the process along by fabricating data from twin pairs. As evidence of this, his heritability coefficient remained .77 as the sample size increased from 15 twin pairs to 53 twin pairs. (Usually parameter estimates change a little bit as new data comes in.) He was further alleged to have made up two research assistants, but these assistants were later found. Complicating matters further, his housekeeper burnt all his research records shortly after his death (!) purportedly on the advice of one of Burt's scientific rivals (?!?).

Burt sounds like a real horse's ass. In a separate book, Cyril Burt: Fraud or Framed?, Hans Eysenck reports that Burt would sometimes sock-puppet, writing articles according to his own views, then leaving his name off of the work and handing it off to a junior researcher, giving the impression that some independent scholar shared his view. Burt purportedly went one further by editing articles submitted to his journal, inserting his own stances and invective into others' work and publishing it without their approval.

Two chapters in Fraud and Erroneous Judgment are devoted to the Burt affair. The first chapter, written by Robert B. Joynson, argues that, strictly speaking, you can't prove he committed fraud. Probably we will never know. Burt is dead and his records destroyed. Even if he made up the data, the potentially made-up data are at least consistent with what we believe today, so maybe it doesn't matter.

The other, written by the late J. Phillippe Rushton, one-time head of the Pioneer Fund, argues more stridently that Burt was framed. According to his perspective, the various social justice warriors and bleeding hearts of today's the 1970s' hyper-liberal universities couldn't bear the uncomfortable truths Burt preached. Rather than refute Burt's ideas in the arena of logic and facts and science, they resorted to underhanded callout-culture tactics to smear him after his death and spoil his legacy.

So in the only involved discussion of an actual fraud allegation in this 181-page book, all that can be said is "maybe he did, or maybe he didn't."

Some material is useful. Chapter 3 recognizes that scientific fraud is a human behavior that is motivated by, and performed within, a social system. One author theorizes that fraud is most often committed under three conditions: 1) there is pressure to publish, whether to advance one's career or to refute critics, 2) the researcher thinks they know the answer already, so that actually doing the experiment is unneccessary, and 3) the research area involves an amount of stochastic variability, such that a failure to replicate can be shaken off as Type I error or hidden moderators. It certainly sounds plausible, but I wonder how useful it is. Most research fulfills all three conditions: all of us are under pressure to publish, all of us have a theory or two to suggest a "right" answer, and all of us experience sampling error and meta-uncertainty.

One thing that hasn't changed one bit is that demonstrating fraud requires demonstrating intent, which is basically impossible. Then and now, people instead have to couch concerns in the language of error, presuming sloppiness instead of malfeasance. Even then, it's not clear at what level of sloppiness crosses the threshold between error and misconduct.

...and Erroneous Judgment

The other cases all concern "erroneous judgment". They reflect ideologically-biased interpretations of data, a lack of scientific rigor, or an excessive willingness to be fooled. These cases vary in their seriousness. At the extremely harmful end, there is a discussion of recovered-memory therapy; this therapy involves helping patients to recover memories of childhood abuse through a process indistinguishable from that one would use to create a false memory. Chillingly, recovered memories became permissible as court evidence in 15 states and lead to a number of false accusations and possible convictions during the Satanic Panic of the 1980s. At the less harmful end, there's an argument about whether the Greeks made up their culture by copying off of the Egyptians. Fun to think about maybe, but nobody is going to jail over that.

Other examples include overexaggeration of societal problems in order to drum up support for research and advocacy. Neil Gilbert illustrates how moral entrepreneurs can extrapolate from sloppy statistical work, small samples, and bad question wording to estimate that 100 billion children are abducted every 3.7 seconds. This fine example is, however, paired with a criticism of feminism and research on sexual assault that has aged poorly; the author's argument boils down to "c'mon, sexual assault can't be that common, right?" Maybe it can be, Neil.

According to the authors, these cases of fallible judgment are caused by excessive enthusiasm rather than deliberate intention to deceive. Therapists dealing in recovered memories are too excited to root out satanic child-abuse cults, too ignorant of the basic science of memory, and too dependent on the perceived efficacy of their practice to know better. Critics of the heritability of IQ are blinded by political correctness and "the egalitarian hoax" of blank-slate models of human development. Political correctness is cited as influencing "fallible judgments" as diverse as the removal of homosexuality from the DSM (and its polite replacement in diagnosis of other disorders so that homosexual patients could continue billing their insurance), the estimation of the prevalence of sexual harassment, failures to test and report racial differences in outcomes, or the attribution of the accomplishments of the Greeks to the Egyptians.

Again, it seems revealing that so little is known about actual cases of fraud that the vast majority of the volume is dedicated to cases where it is unclear who is right. Unable to discover and discuss actual frauds, the discussion has to focus instead on ideological opponents whom the authors don't trust to interpret and represent their data fairly.

Have we made progress?

What's changed between 1995 and now? Today we have more examples to draw upon and more forensic tools. We can use GRIM and SPRITE to catch what are either honest people making typographical mistakes or fraudsters too stupid to make up raw data (good luck telling which is which!). The Data Colada boys keep coming up with new tests for detecting suspicious patterns in data. It's become a little less weird to ask for data and a little more weird to refuse to share data. So there's progress.

Even so, we're still a billion miles away from being able to detect most fraud and to demonstrate intent. Demonstration of intent generally requires a confession or someone on the inside. Personally, I've suspect that fraud detection at scale is probably impossible unless we ask scientists to provide receipts. I can't imagine researchers going for another layer of bureaucracy like that.

One recurring theme is the absence of an actual science police. The discussion of the Burt affair complains that the Council of the British Psychological Society did little to examine Burt's case on its own, instead accepting the conclusions of a biographer. Chapters 1 and 2 discuss the political events that put "Science under Siege" and lead to the creation of the Office of Research Integrity, an institution only grudgingly accepted in Chapter 2. Huffing that every great scientist from Mendel to Millikan had to massage their data a bit from time to time to make their point, David Goodstein cautions the ORI, "I can only hope that we won't arrange things in such a way as would have inhibited Newton or Millikan from doing his thing."

Can we ever know the truth?

Earlier, I mentioned that the book contains three cases of purported fraud: the self-harm study, Cyril Burt's 38 twin-pairs raised apart, and the researcher possibly massaging his data to overestimate the harms of lead. This last case appears to be a reference to the late Herbert Needleman, accused in 1990 of p-hacking his model, an offense Newsweek described at the time as "like bringing a felony indictment for jaywalking." Needleman was exonerated in 1992, and the New York Times ran an obituary honoring him following his death in 2017.

Would I be impressed by Needleman's work today, or would I count him out as another garden-variety noise-miner looking for evidence to support a foregone conclusion? Maybe it doesn't matter. In the Newsweek article, the EPA is quoted as saying "We don't even use Needleman's study anymore" because subsequent research recommended even lower safety thresholds than did Needleman's controversial work. The tempest has blown over. The winners write their history, and the losers get paid by the Cato Institute to go on Fox News and argue against "lead hysteria".

There's a lot that hasn't changed

We think that science has only been subjective, partisan, and politicized in our current "war on science" post-2016 world, but the 1990s also had "science under siege" (Time, Aug 26, 1991) and intractable debates between competing groups with vested interests in there being a crisis or not being a crisis. The tobacco wars reappear in every decade.

Similarly, the froth and stupidity of daytime TV lives on in today's Daily Mail and Facebook groups. In the 90s, people with more outrage than sense believed in vast networks of underground Satanist cults that tortured children and "programmed" them to become pawns in their world domination scheme. Today, those people believe the Democratic party runs child trafficking ring through a pizza parlor and a furniture website and that Donald Trump is on a one-man mission to stop them.

Regarding fraud, we find that scientific self-policing only tends to emerge in response to crisis and scandal. NIH and NSF don't seem to have had formal recommendations regarding fraud until 1988; these were apparently motivated by pressure from Congress following the 1981 case of John Darsee, a Harvard cardiologist who had been faking his data. Those who do scientific self-policing aren't welcomed with open arms -- the book briefly stops to sneer at Walter Stewart and Ned Feder as "a kind of self-appointed truth squad. According to their critics, they had not been very productive scientists and were trying to find a way of holding on to their lab space." Nobody likes having fraud oversight, and everybody does the minimum possible to maintain public respectability until the scandal blows over.

Finally, each generation seems to suspect its successors of being fatally blinded by political correctness. This is clearest in the chapter dedicated to the defense of Cyril Burt, in which Rushton complains that academia will only become more corrupted by political correctness:
Today, the campus radicals of earlier decades are the tenured radicals of the 1990s. Some are chairmen, deans, and presidents. The 1960s mentality of peace, love, and above all equality now constitutes a significant portion of the intellectual establishment in the Western world. The equalitarian dogma is more, not less, entrenched than ever before. Yet, it is based on the scientific hoax of the century.
Will every generation of academics forever consider their successors insufferably and disreputably woke? Should they? It seems that, despite Rushton's concerns, the hereditarian perspective has won out in the end. Today we have researchers who not only recognize heritability, but have given careful thought to the meaning, causality, and societal implications of the research. I see this as tremendous progress when compared to the way the book tends to frame the debate over heritability, which invites the reader to choose between two equally misguided perspectives of either ignorant blank-slate idealism or Rushton's inhumane "race realism."


Some things have changed since 1995, but much has stayed the same.

Compared to 25 years ago, I think we have a better set of tools for detecting fraud. We have new statistical tricks and stronger community norms around data sharing and editorial action. We have the Office of Research Integrity and Retraction Watch.

But some things haven't changed. Researchers checking each other's work are still, at times, regarded coldly: the "self-appointed truth squad" of 1995 is the "self-appointed data police" of 2016. Demonstrating intent to deceive remains a very high bar for those investigating misconduct; probably some number of fraudsters escape oversight by claiming mere incompetence. Because it is difficult to prove intent to deceive, it's easier to fight culture war -- one can wave to an opponent's political bias without getting slapped with a libel suit. And we still don't know much about who commits fraud, why they commit fraud, and how we'll ever catch them.

Thursday, January 30, 2020

Are frauds incompetent?

Nick Brown asks:

My answer is that we are not spotting the competent frauds. This becomes obvious when we think about all the steps that are necessary to catch a fraud:
  1. The fraudulent work must be suspicious enough to get a closer look.
  2. Somebody must be motivated to take it upon themselves to take that closer look.
  3. That motivated person must have the necessary skill to detect the fraud.
  4. The research records available to that motivated and skilled person must be complete and transparent enough to detect the fraud.
  5. That motivated and skilled person must then be brave enough (foolish enough? equipped with lawyers enough?) to contact the research institution.
  6. That research institution must be motivated enough to investigate.
  7. That research institution must also be skilled enough to find and interpret the evidence for fraud.

Considering all these stages at which one could fail to detect or pursue misconduct, it seems immediately obvious to me that we are finding only the most obvious and least protected frauds.

Consider the "Boom, Headshot!" affair. I had read this paper several times and never suspected a thing; nothing in the summary statistics indicates any cause for concern. The only reason anybody discovered the deception was because Pat Markey was curious enough about the effect of skewness on the results to spend months asking the authors and journal for the data and happened to discover values edited by the grad student.

Are all frauds stupid?

Some of the replies to Nick's question imply that faking data convincingly is too much hassle compared to actually collecting data. If you know a lot about data and simulation, why would you bother faking data? This perspective assumes that fraud is difficult and requires skills that could be more profitably used for good. But I don't think either of those is true.

Being good at data doesn't remove temptations for fraud

When news of the LaCour scandal hit, the first thing that struck me was how good this guy was at fancy graphics. Michael LaCour really knew his way around analyzing and presenting statistics in an exciting and accessible way.

But that's not enough to get LaCour's job offer at Princeton. You need to show that you can collect exciting data and get exciting results! When hundreds of quant-ninja, tech-savvy grad students are scrambling for a scant handful of jobs, you need a result that lands you on This American Life. And those of us on the tenure track have our own temptations: bigger grants, bigger salaries, nicer positions, and respect.

Some might even be tempted by the prospect of triumphing over their scientific rivals. Cyril Burt, once president of the British Psychological Society, was alleged to have made up extra twin pairs in order to silence critics of his discovered link between genetics and IQ. Hans Eysenck, the most-cited psychologist of his time, published and defended dozens of papers using likely-fabricated data from his collaborator that supported his views on the causes of cancer.

Skill and intellect and fame and power do not seem to be vaccines against misconduct. And it doesn't take a lot of skill to commit misconduct, either, because...

Frauds don't need to be clever

A fraud does not need a deep understanding of data to make a convincing enough forgery. A crude fake might get some of the complicated multivariate relationships wrong, sure. But will those be detected and prosecuted? Probably not.

You don't need to be the Icy Black Hand of Death to get away with data fakery.
(img source fbi.gov)

Why not? Those complicated relationships don't need to be reported in the paper. Nobody will think to check them. If they want to check them, they'll need to send you an email requesting the raw data. You can ignore them for some months, then tell them your dog ate the raw data, then demand they sign an oath of fealty to you if they're going to look at your raw data.

Getting the complicated covariation bits a little wrong is not likely to reveal a fraud, anyway. Can a psychologist predict even the first digit of simple correlations? A complicated relationship that we know less about will be harder to predict, and it will be harder to persuade co-authors, editors, and institutions that any misspecification is evidence of wrongdoing. Maybe the weird covariation can be explained away as an unusual feature of the specific task or study population. The evidence is merely circumstantial.

...because data forensics can rarely stop them.

Direct evidence requires some manner of internal whistleblower who notices and reports research misconduct. Again, one would need the actually see the misconduct, which is especially unlikely in today's projects in which data and reports come from distant collaborators. Then one would need to actually blow the whistle, after which they might expect to lose their career and get stuck in a years-long court case. Most frauds in psychology are caught this way (Stroebe, Postmes, & Spears, 2012).

In data forensics, by contrast, most evidence for misconduct is merely circumstantial. Noticing in the data very similar means and standard deviations or duplicated data points or duplicated images might be suggestive, but requires assumptions, and is open to alternative explanations. Maybe there was an error in data preprocessing, or the research assistants managed the data wrong, or someone used file IMG4015.png instead of IMG4016.png.

This circumstantial evidence means that nonspecific screw-ups are often a plausible alternative hypothesis. It seems possible to me that a just-competent fraud could falsify a bunch of reports, plead incompetence, issue corrections as necessary, and refine one's approach to data falsification for quite a long time.

A play in one act:

The means were 2.50, 2.50, 2.35, 2.15, 2.80, 2.40, and 2.67.

It is exceedingly unlikely that you would receive such consistent means. I suspect you have fabricated these summary statistics.

Oops, haha, oh shit, did I say those were the means? Major typo! The means were actually, uh, 2.53, 3.12, 2.07, 1.89...

Ahh, nice to see this quickly resolved with a corrigendum. Bye everyone.

We are fully committed to upholding the highest ethical standards etc. any concerns are thoroughly etc. etc.

FRAUDSTER (sotto voce) 
That was close! Next time I fake data I will avoid this error.

The field isn't particularly trying to catch frauds, either.

Trying to prosecute fraud sounds terrible. It takes a very long time, it requires a very high standard of evidence, and lawyers get involved. It is for these reasons, I think, that the self-stated goal of many data thugs is to "correct the literature" rather than "find and punish frauds".

But I worry about this blameless approach, because there's no guarantee that the data that appears in a corrigendum is any closer to the truth. If the original data was a fabrication, chances are good the corrigendum is just a report of slightly-better-fabricated data. And even if the paper is retracted, the perpetrator may learn from the experience and find a way to refine his fabrications and enjoy a long, prosperous life of polluting the scientific literature.

In summary,

I don't think you have to be particularly clever to be a fraud. It seems to me that most discovered frauds involve either direct evidence from a whistleblower or overwhelming circumstantial evidence due to rampant sloppiness. I think that there are probably many more frauds with just a modicum of skill that have gone undiscovered. There are probably also a number of cases that are quietly resolved without the institution announcing the discovered fraud. I spend a lot of time thinking about what it would take to change this, and what the actual prevalence would be if we could uncover it.

Saturday, November 23, 2019

Weighing bullets, not hot sauce

It's been a rich week of readings for wondering just what the hell we're doing. Loyka et al. (2019) present a framework for considering external validity, and this framework reminds us just how poorly we are doing at considering actual real-world human behavior. Tal Yarkoni has a preprint up that describes how implausible it is that the situations and stimuli we study will generalize to other situations and stimuli. Danielle Navarro has clarified her stance on preregistration by elaborating on how misguided she perceives hypothesis testing to be. Together, these articles remind us of the importance of studying the thing we actually care about, rather than what's convenient, because chances are that our findings won't generalize as simply as we expect, because a significant p-value only means that the null is wrong, and not that the alternative is correct.

These readings reminded me of some thoughts I'd jotted down following APA 2019. I'd been invited to present some of my research on violent video games. While I had a great session and had a lot of fun talking to a receptive audience about issues like measurement validity and publication bias, the overall APA experience was personally challenging. This is because one of the major themes of APA 2019 was gun violence and what the APA can do about it.

I attended a number of interesting sessions with presenters who studied actual violence by working and serving in communities, doing ride-alongs with police, interviewing people who had suffered violence and had perpetrated violence. This was draining in two ways. 

First, there's a lot of human suffering out there. One presenter had found that many felons serving prison sentences for gun violence had themselves been victims of gun violence, often as early as age 14. He further found that, when people knew who shot them, they were less likely to tell the police. They trust the police so little that they would prefer to settle the score themselves, and the police are just somebody you can dump your cold cases on as one last hail mary. A mother from Newtown was there. Both of her children had been shot in the massacre. One died. She described crying until the capillaries burst in both her eyes. One gets the feeling that tragedy cannot be prevented and that many people are doomed to poverty and violence from the moment they're born.

Second, it made me frustrated with how far removed we are from the actual societal problem we want to study. We want to prevent gang violence, child abuse, intimate partner violence, bullying, aggressive driving, and harassment. Instead of studying the community members of South- and West-Side Chicago, we study college undergraduates, a bunch of nerds who would rather read a book than fight somebody and generally have enough money and safety to be able to do just that. Instead of studying shootings or fights or abuse, we study how much hot sauce these undergrads pour for each other or whether they think a rude RA should be able to keep their job. We even use proxies of proxies -- when it's too much trouble to see how much hot sauce they'll pour for somebody, we give them KI__ and watch whether they fill it in as KILL or KISS.

One of the APA speakers closed by reference to the old joke about the drunkard looking for his keys. The drunk is looking for his keys under the streetlight. A friend joins him and helps him look for a while, with no progress. Eventually the friend, exasperated, says "Let's try something different. Where did you last see your keys?" The drunk says "I dropped my keys over there in the bushes." The bewildered friend asks "Well then, why are we searching over here by the streetlight?" To which the drunk replies "Well, the light's good over here, and I'm afraid of the dark." 

The light's good over here playing parlor tricks with college undergraduates and hot sauce. And it's certainly less scary than trying to get out in the rough parts of Chicago!

It's possible that I'm not well read and that there's a lot of great aggression research going on that studies these real problems. But mostly I see us running little experiments with just-significant results, or running survey designs that tell us something obvious and hopelessly confounded. Interviews and ethnography and field work seem to be for sociologists or criminologists, not psychologists.

What am I doing about it?  Not much. For now, I'm doing my part by trying to test the convergent validity of our lab measures and see whether they actually agree with each other (preliminary answer: they don't). I often worry about my career, because I've never "discovered" some effect. You could do a decent job summarizing my last ten years as digging a deeper and deeper hole in what we think we already know, hoping to find some sort of bedrock that we can build from. So far, I'm still shoveling, assessing publication bias, failing to replicate findings, criticizing too-good-to-be-true results, and trying to figure out if our measures are at all valid and reliable

I like the work that I do, and I think it's the best work I can do given my skills and resources and timeframe. But that work could be much more valuable if I could get out into the actual populations and environments that we're worried about. I had an RA with a connection at a maximum-security prison, but I wasn't able to pursue the lead aggressively enough and it slipped through my fingers. I'm not particularly smooth or adventurous, so I'm not enthusiastic about going into communities to understand gun violence. I'm pre-tenure, so what makes the most sense for me career-wise is to stick to doing more of the same research with college undergrads and MTurk workers. Maybe try to find some sort of eyebrow-raising lab effect that I can wildly extrapolate from.

I'm not sure what to recommend. As a field, we probably recalibrate our expectations; we can't expect a scientist to make three or four noteworthy, generalizable discoveries a year. Getting actionable and generalizable psychological findings will probably require orders of magnitude more effort and investmentWe can make psychological science prepared for that investment by trying to improve the transparency and honesty of that process.

I'm gonna try to read more sociology and criminology. Maybe they know something we don't?

Monday, June 17, 2019

Comment on Chang & Bushman (2019): Effects of outlier exclusion

Recent research by Chang & Bushman (2019) reports how video games may cause children to be more likely to play with a real handgun. In this experiment, children participate in the study in pairs. They play one of three versions of Minecraft for 20 minutes. One version has no violence (control), another has monsters that they fight with swords (sword violence), and another has monsters that they fight with guns (gun violence). 

The children are then left to play in a room in which, hidden in a drawer, are two very real 9mm handguns. The handguns are disabled -- their firing mechanism has been taken out and replaced with a clicker that counts the number of trigger pulls. But these guns look and feel like the real thing, so one would hope that a child would not touch them or pull their triggers.

The authors report four study outcomes: whether the kid touches the gun, how long they hold the gun, how many times they pull the trigger, and how many times they pull the trigger while the gun is pointed at somebody (themself or the other kid).

I think it's an interesting paradigm. The scenario has a certain plausibility about it, and the outcome is certainly important. It must have been a lot of work to get the ethics board approval.

However, the obtained results depend substantially on the authors' decision to exclude two participants from the control group for playing with the guns a lot. I feel that this is an inappropriate discarding of data. Without this discard, the results are not statistically significant.

Overinterpretation of marginal significance

The results section reports one significant and three marginally significant outcomes:
  • "The difference [in handgun touching] across conditions was nonsignificant [...]" (p = .09)
  • "The gun violence condition increased time spent holding a handgun, although the effect was nonsignificant [...]" (p = .080)
  • "Participants in the gun violence condition pulled the trigger more times than participants in other conditions, although the effect was nonsignificant [...]" (p = .097)
  • "Participants in the violent game conditions pulled the trigger at themselves or their partner more than participants in the nonviolent condition." (p = .007)
These nonsignificant differences are overinterpreted in the discussion section, which begins: "In this study, playing a violent video game increased the likelihood that children would touch a real handgun, increased time spent holding a handgun, and increased pulling the trigger at oneself and others." I found this very confusing; I thought I had read the wrong results section. One has to dig into Supplement 2 to see the exact p values.

Exclusion of outliers

The distribution of the data is both zero-inflated and powerfully right skewed. About half of the kids did not touch the gun at all, much less pull its trigger. Among the minority of kids that did pull the trigger, they pulled it many times. This is a noisy outcome, and difficult to model: you would need a zero-inflated negative binomial regression with cluster-adjusted variances. The authors present a negative binomial regression with cluster-adjusted variances, ignoring the zero-inflation, which is fine enough by me since I can't figure out how to do all that at once either.

Self-other trigger pulls outcome. The pair in red were excluded because the coders commented that they were acting unusually wild. The pair in green were excluded for having too high a score on the outcomes.

Noisy data affords many opportunities for subjectivity. The authors report: "We eliminated 1 pair who was more than 5 SDs from the mean for both time spent holding a handgun and trigger pulls [green pair].  The coders also recommended eliminating another pair because of unusual and extremely aggressive behavior [red pair]." The CONSORT flow diagram reveals that these four excluded subjects with very high scores on the dependent variables were all from the nonviolent control condition, in which participants were expected to spend the least time holding the gun and pulling its trigger. 

The authors tell me that the pair eliminated because of unusual and extremely aggressive behavior was made on the coders' recommendation, blind to condition. That may be true, but the registration is generally rather vague and says nothing about excluding participants on coder recommendation.

The authors also tell me that the pair eliminated because of high scores were eliminated without looking at the results. That may be true as well, but I feel as though one could predict how this exclusion might affect the results.

This latter exclusion of the high-scoring pair is not acceptable to me. You can consider this decision in two ways: First, you can see that there are scores still more extreme in the other two conditions. With data this zero-inflated and skewed, it is no great feat to be more than 5 SDs from the mean. Second, you can look at the model diagnostics. The excluded outliers are not "outliers" in any model influence sense -- their Cook's distances are less than 0.2. (Thresholds of 0.5 or 1.0 are often suggested for Cook's distance.)

Here are the nonzero values in log space, which is where the model fits the negative binomial. On a log scale, the discarded data points still do not look at all like outliers to me.

Revised results

If the high-scoring pair is retained for analysis, none of the results are statistically significant:
  • Touching the gun: omnibus F(2, 79.5) = 1.04, p = .359; gun-vs-control contrast p = .148.
  • Time holding gun: omnibus F(2, 79.5) = .688, p = .506; gun-vs-control contrast p = .278.
  • Trigger pulls at self or other: omnibus F(2, 79.4) = 1.80, p = .172; gun-vs-control contrast p = .098.
From here, adding the coder-suggested pair to the analysis moves the results further still from statistical significance.

If you're worried about the influence of the zero inflation and the long tail, a simpler way to look at the data might be to ask "is the trigger pulled at all while the gun is pointed at somebody?" After all, the difference between not being shot and being shot once is a big deal; the difference between being shot four times and being shot five times less so. Think of this as winsorizing all the values in the tail to 1. Then you could just fit a logistic regression and not have to worry about influence.

Analyzed this way, there are 6 events in the control group, 10 in the sword-game group, and 13 in the gun-game group. The authors excluded four of these six control-group events as outliers. With these exclusions, there is a statistically significant effect, p = .029. If you return either pair to the control group, the effect is not statistically significant, p = .098. If you return both pairs to the control group, the effect is not statistically significant, p = .221.

I wish the authors and peer reviewers had considered the sensitivity of the results to the questionable exclusion of this pair. While these results are suggestive, they are much less decisive than the authors have presented them.

Journal response

I attempted to send JAMA Open a version of this comment, but their publication portal does not accept comment submissions. I asked to speak with an editor; the editor declined to discuss the article with me. The journal's stance is that, as an online-only journal, they don't consider letters to the editor. They invited me to post a comment in their Youtube-style comments field, which appears on a separate tab where it will likely go unread.

I am disturbed by the ease with which peer reviewers would accept ad hoc outlier exclusion and frustrated that the article and press release do little to present the uncertainty. It seems like one could get up to a lot of mischief at JAMA Open by excluding hypothesis-threatening datapoints.

Author response

I discussed these criticisms intensely with the authors as I prepared my concerns for JAMA Open and for this blog post. Dr. Bushman replied:

We believe that [the coder-suggested pair] was removed completely legitimately, although you are correct this was not documented ahead of time on the clinicaltrials.gov site. We believe [the high-scoring pair] should also have been excluded, but you do not. We acknowledge there may be honest differences of opinion regarding [the high-scoring pair]. 
As stated in our comment on JAMA Open, “Importantly, both pairs were eliminated before we knew how they would impact our analyses and whether their results would support our hypotheses.”
Again, I disagree with the characterization of the removal of the high-scoring pair as a subjective decision. I don't see any justifiable criterion for throwing this data away, and one can anticipate how this removal would influence the analyses and results.


I was successfully able to reproduce the results presented by Chang and Bushman (2019). However, those results seem to depend heavily on the exclusion of four of the six most aggressive participants in the nonviolent control group. The justification that these four participants are unusually aggressive does not seem tenable in light of the low influence of these datapoints and similarly aggressive participants retained in the other two conditions. 

While I admire the researchers for their passion and their creative setup, I am also frustrated. I believe that researchers have an obligation to quantify uncertainty to the best of their ability. I feel that the exclusion of high-scoring participants from the control group serves to understate the uncertainty and facilitate the anticipated headlines. The sensitivity of the results to this questionable exclusion should be made clearer.

See my code at https://osf.io/8jgrp/. Analyses reproduced in R using MASS::glm.nb for negative binomial regression with log link and clubSandwich for cluster-robust variance estimation. Data available upon request from the authors. Thanks to James Pustejovsky for making clubSandwich. Thanks to Jeff Rouder for talking with me about all this when I needed to know I wasn't taking crazy pills.