“It’s certainly not bareknuckle:” Comments to a journalist about a critique of mindfulness research

We can’t assume authors of mindfulness studies are striving to do the best possible science, including being prepared for the possibility of being proven incorrect by their results.

mind the brain logo

I recently had a Skype interview with science journalist Peter Hess concerning an article in Psychological Science.

Peter was exceptionally prepared, had a definite point of view, but was open to what I said. In the end seem to be persuaded by me on a number of points.  The resulting article in Inverse  faithfully conveyed my perspective and juxtaposed quotes from me with those from an author of the Psych Science piece in a kind of debate.

My point of view

larger dogWhen evaluating an article about mindfulness in a peer-reviewed journal, we need to take into account that authors may not necessarily be striving to do the best science, but to maximally benefit their particular brand of mindfulness, their products, or the settings in which they operate. Many studies of mindfulness are a little more than infomercials, weak research intended only to get mindfulness promoters’ advertisement of themselves into print or to allow the labeling of claims as “peer-reviewed”. Caveat Lector.

We cannot assume authors of mindfulness studies are striving to do the best possible science, including being prepared for the possibility of being proven incorrect by their results. Rather they may be simply try to get the strongest possible claims through peer review, ignoring best research practices and best publication practices.

Psychologists Express Growing Concern With Mindfulness Meditation

“It’s not bare-knuckle, that’s for sure.”

There was much from the author of the Psych Science article with which  I would agree:

“In my opinion, there are far too many organizations, companies, and therapists moving forward with the implementation of ‘mindfulness-based’ treatments, apps, et cetera before the research can actually tell us whether it actually works, and what the risk-reward ratio is,” corresponding author and University of Melbourne research fellow Nicholas Van Dam, Ph.D. tells Inverse.

Bravo! And

“People are spending a lot of money and time learning to meditate, listening to guest speakers about corporate integration of mindfulness, and watching TED talks about how mindfulness is going to supercharge their brain and help them live longer. Best case scenario, some of the advertising is true. Worst case scenario: very little to none of the advertising is true and people may actually get hurt (e.g., experience serious adverse effects).”

But there were some statements that renewed the discomfort and disappointment I experienced when I read the original article in Psychological Science:

 “I think the biggest concern among my co-authors and I is that people will give up on mindfulness and/or meditation because they try it and it doesn’t work as promised,” says Van Dam.

“There may really be something to mindfulness, but it will be hard for us to find out if everyone gives up before we’ve even started to explore its best potential uses.”

So, how long before we “give up” on thousands of studies pouring out of an industry? In the meantime, should consumers act on what seem to be extravagant claims?

The Inverse article segued into some quotes from me after delivering another statement from the author which I could agree:

The authors of the study make their attitudes clear when it comes to the current state of the mindfulness industry: “Misinformation and poor methodology associated with past studies of mindfulness may lead public consumers to be harmed, misled, and disappointed,” they write. And while this comes off as unequivocal, some think they don’t go far enough in calling out specific instances of quackery.

“It’s not bare-knuckle, that’s for sure. I’m sure it got watered down in the review process,” James Coyne, Ph.D., an outspoken psychologist who’s extensively criticized the mindfulness industry, tells Inverse.

Coyne agrees with the conceptual issues outlined in the paper, specifically the fact that many mindfulness therapies are based on science that doesn’t really prove their efficacy, as well as the fact that researchers with copyrights on mindfulness therapies have financial conflicts of interest that could influence their research. But he thinks the authors are too concerned with tone policing.

“I do appreciate that they acknowledged other views, but they kept out anybody who would have challenged their perspective,” he says.

Regarding Coyne’s criticism about calling out individuals, Van Dam says the authors avoided doing that so as not to alienate people and stifle dialogue.

“I honestly don’t think that my providing a list of ‘quacks’ would stop people from listening to them,” says Van Dam. “Moreover, I suspect my doing so would damage the possibility of having a real conversation with them and the people that have been charmed by them.” If you need any evidence of this, look at David “Avocado” Wolfe, whose notoriety as a quack seems to make him even more popular as a victim of “the establishment.” So yes, this paper may not go so far as some would like, but it is a first step toward drawing attention to the often flawed science underlying mindfulness therapies.

To whom is the dialogue directed about unwarranted claims from the mindfulness industry?

As one of the authors of an article claiming to be an authoritative review from a group of psychologists with diverse expertise, Van Dam says he is speaking to consumers. Why won’t he and his co-authors provide citations and name names so that readers can evaluate for themselves what they are being told? Is the risk of reputational damage and embarrassment to the psychologists so great as to cause Van Dam to protect them versus protecting consumers from the exaggerated and even fraudulent claims of psychologists hawking their products branded as ‘peer-reviewed psychological and brain science’.

I use the term ‘quack’ sparingly outside of discussing unproven and unlikely-to-be-proven products supposed to promote physical health and well-being or to prevent or cure disease and distress.

I think Harvard psychologist Ellen Langer deserves the term “quack” for her selling of expensive trips to spas in Mexico to women with advanced cancer so that they can change their mind set to reverse the course of their disease. Strong evidence, please! Given that this self-proclaimed mother of mindfulness gets her claims promoted through the Association for Psychological Science website, I think it particularly appropriate for Van Dam and his coauthors to name her in their publication in an APS journal. Were they censored or only censoring themselves?

Let’s put aside psychologists who can be readily named as quacks. How about Van Dam and co-authors naming names of psychologists claiming to alter the brains and immune systems of cancer patients with mindfulness practices so that they improve their physical health and fight cancer, not just cope better with a life-altering disease?

I simply don’t buy Van Dam’s suggestion that to name names promotes quackery any more than I believe exposing anti-vaxxers promotes the anti-vaccine cause.

Is Van Dam only engaged in a polite discussion with fellow psychologists that needs to be strictly tone-policed to avoid offense or is he trying to reach, educate, and protect consumers as citizen scientists looking after their health and well-being? Maybe that is where we parted ways.

Creating illusions of wondrous effects of yoga and meditation on health: A skeptic exposes tricks

The tour of the sausage factory is starting, here’s your brochure telling you’ll see.


A recent review has received a lot of attention with it being used for claims that mind-body interventions have distinct molecular signatures that point to potentially dramatic health benefits for those who take up these practices.

What Is the Molecular Signature of Mind–Body Interventions? A Systematic Review of Gene Expression Changes Induced by Meditation and Related Practices.  Frontiers in Immunology. 2017;8.

Few who are tweeting about this review or its press coverage are likely to have read it or to understand it, if they read it. Most of the new agey coverage in social media does nothing more than echo or amplify the message of the review’s press release.  Lazy journalists and bloggers can simply pass on direct quotes from the lead author or even just the press release’s title, ‘Meditation and yoga can ‘reverse’ DNA reactions which cause stress, new study suggests’:

“These activities are leaving what we call a molecular signature in our cells, which reverses the effect that stress or anxiety would have on the body by changing how our genes are expressed.”


“Millions of people around the world already enjoy the health benefits of mind-body interventions like yoga or meditation, but what they perhaps don’t realise is that these benefits begin at a molecular level and can change the way our genetic code goes about its business.”

[The authors of this review actually identified some serious shortcomings to the studies they reviewed. I’ll be getting to some excellent points at the end of this post that run quite counter to the hype. But the lead author’s press release emphasized unwarranted positive conclusions about the health benefits of these practices. That is what is most popular in media coverage, especially from those who have stuff to sell.]

Interpretation of the press release and review authors’ claims requires going back to the original studies, which most enthusiasts are unlikely to do. If readers do go back, they will have trouble interpreting some of the deceptive claims that are made.

Yet, a lot is at stake. This review is being used to recommend mind-body interventions for people having or who are at risk of serious health problems. In particular, unfounded claims that yoga and mindfulness can increase the survival of cancer patients are sometimes hinted at, but occasionally made outright.

This blog post is written with the intent of protecting consumers from such false claims and providing tools so they can spot pseudoscience for themselves.

Discussion in the media of the review speaks broadly of alternative and complementary interventions. The coverage is aimed at inspiring  confidence in this broad range of treatments and to encourage people who are facing health crises investing time and money in outright quackery. Seemingly benign recommendations for yoga, tai chi, and mindfulness (after all, what’s the harm?) often become the entry point to more dubious and expensive treatments that substitute for established treatments.  Once they are drawn to centers for integrative health care for classes, cancer patients are likely to spend hundreds or even thousands on other products and services that are unlikely to benefit them. One study reported:

More than 72 oral or topical, nutritional, botanical, fungal and bacterial-based medicines were prescribed to the cohort during their first year of IO care…Costs ranged from $1594/year for early-stage breast cancer to $6200/year for stage 4 breast cancer patients. Of the total amount billed for IO care for 1 year for breast cancer patients, 21% was out-of-pocket.

Coming up, I will take a skeptical look at the six randomized trials that were highlighted by this review.  But in this post, I will provide you with some tools and insights so that you do not have to make such an effort in order to make an informed decision.

Like many of the other studies cited in the review, these randomized trials were quite small and underpowered. But I will focus on the six because they are as good as it gets. Randomized trials are considered a higher form of evidence than simple observational studies or case reports [It is too bad the authors of the review don’t even highlight what studies are randomized trials. They are lumped with others as “longitudinal studies.]

As a group, the six studies do not actually add any credibility to the claims that mind-body interventions – specifically yoga, tai chi, and mindfulness training or retreats improve health by altering DNA.  We can be no more confident with what the trials provide than we would be without them ever having been done.

I found the task of probing and interpreting the studies quite labor-intensive and ultimately unrewarding.

I had to get past poor reporting of what was actually done in the trials, to which patients, and with what results. My task often involved seeing through cover ups with authors exercising considerable flexibility in reporting what measures were they actually collected and what analyses were attempted, before arriving at the best possible tale of the wondrous effects of these interventions.

Interpreting clinical trials should not be so hard, because they should be honestly and transparently reported and have a registered protocol and stick to it. These reports of trials were sorely lacking, The full extent of the problems took some digging to uncover, but some things emerged before I got to the methods and results.

The introductions of these studies consistently exaggerated the strength of existing evidence for the effects of these interventions on health, even while somehow coming to the conclusion that this particular study was urgently needed and it might even be the “first ever”. The introductions to the six papers typically cross-referenced each other, without giving any indication of how poor quality the evidence was from the other papers. What a mutual admiration society these authors are.

One giveaway is how the introductions  referred to the biggest, most badass, comprehensive and well-done review, that of Goyal and colleagues.

That review clearly states that the evidence for the effects of mindfulness is poor quality because of the lack of comparisons with credible active treatments. The typical randomized trial of mindfulness involves a comparison with no-treatment, a waiting list, or patients remaining in routine care where the target problem is likely to be ignored.  If we depend on the bulk of the existing literature, we cannot rule out the likelihood that any apparent benefits of mindfulness are due to having more positive expectations, attention, and support over simply getting nothing.  Only a handful  of hundreds of trials of mindfulness include appropriate, active treatment comparison/control groups. The results of those studies are not encouraging.

One of the first things I do in probing the introduction of a study claiming health benefits for mindfulness is see how they deal with the Goyal et al review. Did the study cite it, and if so, how accurately? How did the authors deal with its message, which undermines claims of the uniqueness or specificity of any benefits to practicing mindfulness?

For yoga, we cannot yet rule out that it is better than regular exercising – in groups or alone – having relaxing routines. The literature concerning tai chi is even smaller and poorer quality, but there is the same need to show that practicing tai chi has any benefits over exercising in groups with comparable positive expectations and support.

Even more than mindfulness, yoga and tai chi attract a lot of pseudoscientific mumbo jumbo about integrating Eastern wisdom and Western science. We need to look past that and insist on evidence.

Like their introductions, the discussion sections of these articles are quite prone to exaggerating how strong and consistent the evidence is from existing studies. The discussion sections cherry pick positive findings in the existing literature, sometimes recklessly distorting them. The authors then discuss how their own positively spun findings fit with what is already known, while minimizing or outright neglecting discussion of any of their negative findings. I was not surprised to see one trial of mindfulness for cancer patients obtain no effects on depressive symptoms or perceived stress, but then go on to explain mindfulness might powerfully affect the expression of DNA.

If you want to dig into the details of these studies, the going can get rough and the yield for doing a lot of mental labor is low. For instance, these studies involved drawing blood and analyzing gene expression. Readers will inevitably encounter passages like:

In response to KKM treatment, 68 genes were found to be differentially expressed (19 up-regulated, 49 down-regulated) after adjusting for potentially confounded differences in sex, illness burden, and BMI. Up-regulated genes included immunoglobulin-related transcripts. Down-regulated transcripts included pro-inflammatory cytokines and activation-related immediate-early genes. Transcript origin analyses identified plasmacytoid dendritic cells and B lymphocytes as the primary cellular context of these transcriptional alterations (both p < .001). Promoter-based bioinformatic analysis implicated reduced NF-κB signaling and increased activity of IRF1 in structuring those effects (both p < .05).

Intimidated? Before you defer to the “experts” doing these studies, I will show you some things I noticed in the six studies and how you can debunk the relevance of these studies for promoting health and dealing with illness. Actually, I will show that even if these 6 studies got the results that the authors claimed- and they did not- at best, the effects would trivial and lost among the other things going on in patients’ lives.

Fortunately, there are lots of signs that you can dismiss such studies and go on to something more useful, if you know what to look for.

Some general rules:

  1. Don’t accept claims of efficacy/effectiveness based on underpowered randomized trials. Dismiss them. The rule of thumb is reliable to dismiss trials that have less than 35 patients in the smallest group. Over half the time, true moderate sized effects will be missed in such studies, even if they are actually there.

Due to publication bias, most of the positive effects that are published from such sized trials will be false positives and won’t hold up in well-designed, larger trials.

When significant positive effects from such trials are reported in published papers, they have to be large to have reached significance. If not outright false, these effect sizes won’t be matched in larger trials. So, significant, positive effect sizes from small trials are likely to be false positives and exaggerated and probably won’t replicate. For that reason, we can consider small studies to be pilot or feasibility studies, but not as providing estimates of how large an effect size we should expect from a larger study. Investigators do it all the time, but they should not: They do power calculations estimating how many patients they need for a larger trial from results of such small studies. No, no, no!

Having spent decades examining clinical trials, I am generally comfortable dismissing effect sizes that come from trials with less than 35 patients in the smaller group. I agree with a suggestion that if there are two larger trials are available in a given literature, go with those and ignore the smaller studies. If there are not at least two larger studies, keep the jury out on whether there is a significant effect.

Applying the Rule of 35, 5 of the 6 trials can be dismissed and the sixth is ambiguous because of loss of patients to follow up.  If promoters of mind-body interventions want to convince us that they have beneficial effects on physical health by conducting trials like these, they have to do better. None of the individual trials should increase our confidence in their claims. Collectively, the trials collapse in a mess without providing a single credible estimate of effect size. This attests to the poor quality of evidence and disrespect for methodology that characterizes this literature.

  1. Don’t be taken in by titles to peer-reviewed articles that are themselves an announcement that these interventions work. Titles may not be telling the truth.

What I found extraordinary is that five of the six randomized trials had a title that indicating a positive effect was found. I suspect that most people encountering the title will not actually go on to read the study. So, they will be left with the false impression that positive results were indeed obtained. It’s quite a clever trick to make the title of an article, by which most people will remember it, into a false advertisement for what was actually found.

For a start, we can simply remind ourselves that with these underpowered studies, investigators should not even be making claims about efficacy/effectiveness. So, one trick of the developing skeptic is to confirm that the claims being made in the title don’t fit with the size of the study. However, actually going to the results section one can find other evidence of discrepancies between what was found in what is being claimed.

I think it’s a general rule of thumb that we should be careful of titles for reports of randomized that declare results. Even when what is claimed in the title fits with the actual results, it often creates the illusion of a greater consistency with what already exists in the literature. Furthermore, even when future studies inevitably fail to replicate what is claimed in the title, the false claim lives on, because failing to replicate key findings is almost never a condition for retracting a paper.

  1. Check the institutional affiliations of the authors. These 6 trials serve as a depressing reminder that we can’t go on researchers’ institutional affiliation or having federal grants to reassure us of the validity of their claims. These authors are not from Quack-Quack University and they get funding for their research.

In all cases, the investigators had excellent university affiliations, mostly in California. Most studies were conducted with some form of funding, often federal grants.  A quick check of Google would reveal from at least one of the authors on a study, usually more, had federal funding.

  1. Check the conflicts of interest, but don’t expect the declarations to be informative. But be skeptical of what you find. It is also disappointing that a check of conflict of interest statements for these articles would be unlikely to arouse the suspicion that the results that were claimed might have been influenced by financial interests. One cannot readily see that the studies were generally done settings promoting alternative, unproven treatments that would benefit from the publicity generated from the studies. One cannot see that some of the authors have lucrative book contracts and speaking tours that require making claims for dramatic effects of mind-body treatments could not possibly be supported by: transparent reporting of the results of these studies. As we will see, one of the studies was actually conducted in collaboration with Deepak Chopra and with money from his institution. That would definitely raise flags in the skeptic community. But the dubious tie might be missed by patients in their families vulnerable to unwarranted claims and unrealistic expectations of what can be obtained outside of conventional medicine, like chemotherapy, surgery, and pharmaceuticals.

Based on what I found probing these six trials, I can suggest some further rules of thumb. (1) Don’t assume for articles about health effects of alternative treatments that all relevant conflicts of interest are disclosed. Check the setting in which the study was conducted and whether it was in an integrative [complementary and alternative, meaning mostly unproven.] care setting was used for recruiting or running the trial. Not only would this represent potential bias on the part of the authors, it would represent selection bias in recruitment of patients and their responsiveness to placebo effects consistent with the marketing themes of these settings.(2) Google authors and see if they have lucrative pop psychology book contracts, Ted talks, or speaking gigs at positive psychology or complementary and alternative medicine gatherings. None of these lucrative activities are typically expected to be disclosed as conflicts of interest, but all require making strong claims that are not supported by available data. Such rewards are perverse incentives for authors to distort and exaggerate positive findings and to suppress negative findings in peer-reviewed reports of clinical trials. (3) Check and see if known quacks have prepared recruitment videos for the study, informing patients what will be found (Serious, I was tipped off to look and I found that).

  1. Look for the usual suspects. A surprisingly small, tight, interconnected group is generating this research. You could look the authors up on Google or Google Scholar or  browse through my previous blog posts and see what I have said about them. As I will point out in my next blog, one got withering criticism for her claim that drinking carbonated sodas but not sweetened fruit drinks shortened your telomeres so that drinking soda was worse than smoking. My colleagues and I re-analyzed the data of another of the authors. We found contrary to what he claimed, that pursuing meaning, rather than pleasure in your life, affected gene expression related to immune function. We also showed that substituting randomly generated data worked as well as what he got from blood samples in replicating his original results. I don’t think it is ad hominem to point out a history for both of the authors of making implausible claims. It speaks to source credibility.
  1. Check and see if there is a trial registration for a study, but don’t stop there. You can quickly check with PubMed if a report of a randomized trial is registered. Trial registration is intended to ensure that investigators commit themselves to a primary outcome or maybe two and whether that is what they emphasized in their paper. You can then check to see if what is said in the report of the trial fits with what was promised in the protocol. Unfortunately, I could find only one of these was registered. The trial registration was vague on what outcome variables would be assessed and did not mention the outcome emphasized in the published paper (!). The registration also said the sample would be larger than what was reported in the published study. When researchers have difficulty in recruitment, their study is often compromised in other ways. I’ll show how this study was compromised.

Well, it looks like applying these generally useful rules of thumb is not always so easy with these studies. I think the small sample size across all of the studies would be enough to decide this research has yet to yield meaningful results and certainly does not support the claims that are being made.

But readers who are motivated to put in the time of probing deeper come up with strong signs of p-hacking and questionable research practices.

  1. Check the report of the randomized trial and see if you can find any declaration of one or two primary outcomes and a limited number of secondary outcomes. What you will find instead is that the studies always have more outcome variables than patients receiving these interventions. The opportunities for cherry picking positive findings and discarding the rest are huge, especially because it is so hard to assess what data were collected but not reported.
  1. Check and see if you can find tables of unadjusted primary and secondary outcomes. Honest and transparent reporting involves giving readers a look at simple statistics so they can decide if results are meaningful. For instance, if effects on stress and depressive symptoms are claimed, are the results impressive and clinically relevant? Almost in all cases, there is no peeking allowed. Instead, authors provide analyses and statistics with lots of adjustments made. They break lots of rules in doing so, especially with such a small sample. These authors are virtually assured to get results to crow about.

Famously, Joe Simmons and Leif Nelson hilariously published claims that briefly listening to the Beatles’ “When I’m 64” left students a year and a half older younger than if they were assigned to listening to “Kalimba.”  Simmons and Leif Nelson knew this was nonsense, but their intent was to show what researchers can do if they have free reign with how they analyze their data and what they report and  . They revealed the tricks they used, but they were so minor league and amateurish compared to what the authors of these trials consistently did in claiming that yoga, tai chi, and mindfulness modified expression of DNA.

Stay tuned for my next blog post where I go through the six studies. But consider this, if you or a loved one have to make an immediate decision about whether to plunge into the world of woo woo unproven medicine in hopes of  altering DNA expression. I will show the authors of these studies did not get the results they claimed. But who should care if they did? Effects were laughably trivial. As the authors of this review about which I have been complaining noted:

One other problem to consider are the various environmental and lifestyle factors that may change gene expression in similar ways to MBIs [Mind-Body Interventions]. For example, similar differences can be observed when analyzing gene expression from peripheral blood mononuclear cells (PBMCs) after exercise. Although at first there is an increase in the expression of pro-inflammatory genes due to regeneration of muscles after exercise, the long-term effects show a decrease in the expression of pro-inflammatory genes (55). In fact, 44% of interventions in this systematic review included a physical component, thus making it very difficult, if not impossible, to discern between the effects of MBIs from the effects of exercise. Similarly, food can contribute to inflammation. Diets rich in saturated fats are associated with pro-inflammatory gene expression profile, which is commonly observed in obese people (56). On the other hand, consuming some foods might reduce inflammatory gene expression, e.g., drinking 1 l of blueberry and grape juice daily for 4 weeks changes the expression of the genes related to apoptosis, immune response, cell adhesion, and lipid metabolism (57). Similarly, a diet rich in vegetables, fruits, fish, and unsaturated fats is associated with anti-inflammatory gene profile, while the opposite has been found for Western diet consisting of saturated fats, sugars, and refined food products (58). Similar changes have been observed in older adults after just one Mediterranean diet meal (59) or in healthy adults after consuming 250 ml of red wine (60) or 50 ml of olive oil (61). However, in spite of this literature, only two of the studies we reviewed tested if the MBIs had any influence on lifestyle (e.g., sleep, diet, and exercise) that may have explained gene expression changes.

How about taking tango lessons instead? You would at least learn dance steps, get exercise, and decrease any social isolation. And so what if there were more benefits than taking up these other activities?



Was independent peer review of the PACE trial articles possible?

I ponder this question guided by Le Chavalier C. Auguste Dupin, the first fictional detective, before anyone was called “detective.”

mccartney too manyArticles reporting the PACE trial have extraordinary numbers of authors, acknowledgments, and institutional affiliations. A considerable proportion of all persons and institutions involved in researching chronic fatigue and related conditions in the UK have a close connection to PACE.

This raises issues about

  • Obtaining independent peer review of these articles that is not tainted by reviewer conflict of interest.
  • Just what authorship on a PACE trial paper represents and whether granting of authorship conforms to international standards.
  • The security of potential critics contemplating speaking out about whatever bad science they find in the PACE trial articles. The security of potential reviewers who are negative and can be found out. Critics within the UK risk isolation and blacklisting from a large group who have investments in what could be exaggerated estimates of the quality and outcome of PACE trial.
  • Whether grants associated with multimillion pound PACE study could have received the independent peer review that is so crucial to assuring that proposals selected to be funded are of the highest quality.

Issues about the large number of authors, acknowledgments, and institutional affiliations become all the more salient as critics [1, 2, 3] find again serious flaws inthe conduct and the reporting of the Lancet Psychiatry 2015 long-term follow-up study. Numerous obvious Questionable Research Practices (QRPs) survived peer review. That implies at least ineptness in peer review or even Questionable Publication Practices (QPPs).

The important question becomes: how is the publication of questionable science to be explained?

Maybe there were difficulties finding reviewers with relevant expertise who were not in some way involved in the PACE trial or affiliated with departments and institutions that would be construed as benefiting from a positive review outcome, i.e. a publication?

Or in the enormous smallness of the UK, is independent peer review achieved by persons putting those relationships and affiliations aside to produce an impeccably detached and rigorous review process?

The untrustworthiness of both the biomedical and psychological literatures are well-established. Nonpharmacological interventions have fewer safeguards than drug trials, in terms of adherence to preregistration, reporting standards like CONSORT, and enforcement of sharing of data.

Open-minded skeptics should be assured of independent peer review of nonpharmacological clinical trials, particularly when there is evidence that persons and groups with considerable financial interests attempt to control what gets published and what is said about their favored interventions. Reviewers with potential conflicts of interest should be excluded from evaluation of manuscripts.

Independent peer review of the PACE trial by those with relevant expertise might not be possible the UK where much of the conceivable expertise is in some way directly or indirectly attached to the PACE trial.

A Dutch observer’s astute observations about the PACE articles

My guest blogger Dutch research biologist Klaas van Dijk  called attention to the exceptionally large number of authors and institutions listed for a pair of PACE trial papers.

klaasKlaas noted

The Pubmed entry for the 2011 Lancet paper lists 19 authors:

B J Angus, H L Baber, J Bavinton, M Burgess, T Chalder, L V Clark, D L Cox, J C DeCesare, K A Goldsmith, A L Johnson, P McCrone, G Murphy, M Murphy, H O’Dowd, PACE trial management group*, L Potts, M Sharpe, R Walwyn, D Wilks and P D White (re-arranged in an alphabetic order).

The actual article from the Lancet website ( http://www.thelancet.com/pdfs/journals/lancet/PIIS0140-6736(11)60096-2.pdf and also http://www.thelancet.com/journals/lancet/article/PIIS0140-6736(11)60096-2/fulltext ) lists 19 authors who are acting ‘on behalf of the PACE trial management group†’. But the end of the paper (page 835) states: “PACE trial group.” This term is not identical to “PACE trial management group”.
In total, another 19 names are listed under “PACE trial group” (page 835): Hiroko Akagi, Mansel Aylward, Barbara Bowman Jenny Butler, Chris Clark, Janet Darbyshire, Paul Dieppe, Patrick Doherty, Charlotte Feinmann, Deborah Fleetwood, Astrid Fletcher, Stella Law, M Llewelyn, Alastair Miller, Tom Sensky, Peter Spencer, Gavin Spickett, Stephen Stansfeld and Alison Wearden (re-arranged in an alphabetic order).

There is no overlap with the first 19 people who are listed as author of the paper.

So how many people can claim to be an author of this paper? Are all these 19 people of the “PACE trial management group” (not identical to “PACE trial group”???) also some sort of co-author of this paper? Do all these 19 people of the second group also agree with the complete contents of the paper? Do all 38 people agree with the full contents of the paper?

The paper lists many affiliations:
* Queen Mary University of London, UK
* King’s College London, UK
* University of Cambridge, UK
* University of Cumbria, UK
* University of Oxford, UK
* University of Edinburgh, UK
* Medical Research Council Clinical Trials Unit, London, UK
* South London and Maudsley NHS Foundation Trust, London, UK
* The John Radcliffe Hospital, Oxford, UK
* Royal Free Hospital NHS Trust, London, UK
* Barts and the London NHS Trust, London, UK
* Frenchay Hospital NHS Trust, Bristol, UK;
* Western General Hospital, Edinburgh, UK

Do all these affiliations also agree with the full contents of the paper? Am I right to assume that all 38 people (names see above) and all affiliations / institutes (see above) plainly refuse to give critics / other scientists / patients / patient groups (etc.) access to the raw research data of this paper and am I am right with my assumption that it is therefore impossible for all others (including allies of patients / other scientists / interested students, etc.) to conduct re-calculations, check all statements with the raw data, etc?

Decisions whether to accept manuscripts for publication are made in dark places based on opinions offered by people whose identities may be known only to editors. Actually, though, in a small country like the UK, peer-reviewed may be a lot less anonymous than intended and possibly a lot less independent and free of conflict of interests. Without a lot more transparency than is currently available concerning peer review the published papers underwent, we are left to our speculation.

Prepublication peer review is just one aspect of the process of getting research findings vetted and shaped and available to the larger scientific community, and an overall process that is now recognized as tainted with untrustworthiness.

Rules for granting authorship

Concerns about gift and unwarranted authorship have increased not only because of growing awareness of unregulated and unfair practices, but because of the importance attached to citations and authorship for professional advancement. Journals are increasingly requiring documentation that all authors have made an appropriate contribution to a manuscript and have approved the final version

Yet operating rules for granting authorship in many institutional settings vary greatly from the stringent requirements of journals. Contrary to the signed statements that corresponding authors have to make in submitting a manuscript to a journal, many clinicians expect an authorship in return for access to patients. Many competitive institutions award and withhold authorship based on politics and good or bad behavior that have nothing to do with requirements of journals.

Basically, despite the existence of numerous ethical guidelines and explicit policies, authors and institutions can largely do what they want when it comes to granting and withholding authorship.

Persons are quickly disappointed when they are naïve enough to complain about unwarranted authorships or being forced to include authors on papers without appropriate contribution or being denied authorship for an important contribution. They quickly discover that whistleblowers are generally considered more of a threat to institutions and punished more severely than alleged wrongdoers, no matter how strong the evidence may be.

The Lancet website notes

The Lancet is a signatory journal to the Recommendations for the Conduct, Reporting, Editing, and Publication of Scholarly Work in Medical Journals, issued by the International Committee of Medical Journal Editors (ICMJE Recommendations), and to the Committee on Publication Ethics (COPE) code of conduct for editors. We follow COPE’s guidelines.

The ICMJE recommends that an author should meet all four of the following criteria:

  • Substantial contributions to the conception or design of the work; or the acquisition, analysis, or interpretation of data for the work;
  • Drafting the work or revising it critically for important intellectual content;
  • Final approval of the version to be published;
  • Agreement to be accountable for all aspects of the work in ensuring that questions related to the accuracy or integrity of any part of the work are appropriately investigated and resolved.”

The intent of these widely endorsed recommendations is that persons associated with a large project have to do a lot to claim their places as authors.

Why the fuss about acknowledgments?

I’ve heard from a number of graduate students and junior investigators that they have had their first manuscripts held up in the submission process because they did not obtain written permission for acknowledgments. Why is that considered so important?

Mention in an acknowledgment is an honor. But it implies involvement in a project and approval of a resulting manuscript. In the past, there were numerous instances where people were named in acknowledgments without having given permission. There was a suspicion sometimes confirmed, that they had been acknowledged only to improve the prospects of a manuscript for getting published. There are other instances where persons were included in acknowledgments without permission with the intent of authors avoiding them in the review process because of the appearance of a conflict of interest.

The expectation is that anyone contributing enough to a manuscript to be acknowledged as a potential conflict of interest in deciding whether it is suitable for publication.

But, as in other aspects of a mysterious and largely anonymous review process, whether people who were acknowledged in manuscripts were barred from participating in review of a manuscript cannot be established by readers.

What is the responsibility of reviewers to declare conflict of interest?

Reviewers are expected to declare conflicts of interest accepting a manuscript to review. But often they are presented with a tick box without a clear explanation of the criteria for the appearance of conflict of interest. But reviewers can usually continue considering a manuscript after acknowledging that they do have an association with authors or institutional affiliation, but they do not consider it a conflict. It is generally accepted that statement.

Authors excluding from the review process persons they consider to have a negative bias

In submitting a manuscript, authors are offered an opportunity to identify persons who should be excluded because of the appearance of a negative bias. Editors generally take these requests quite seriously. As an editor, I sometimes receive a large number of requested exclusions by authors who worry about opinions of particular people.

While we don’t know what went on in prepublication peer review, the PACE investigators have repeatedly and aggressively attempted to manipulate post publication portrayals of their trial in the media. Can we rule out that they similarly try to control potential critics in the prepublication peer review of their papers?

The 2015 Lancet Psychiatry secondary mediation analysis article

Chalder, T., Goldsmith, K. A., Walker, J., & White, P. D. Sharpe, M., Pickles, A.R. Rehabilitative therapies for chronic fatigue syndrome: a secondary mediation analysis of the PACE trial. The Lancet Psychiatry, 2: 141–52

The acknowledgments include

We acknowledge the help of the PACE Trial Management Group, which consisted of the authors of this paper, excluding ARP, plus (in alphabetical order): B Angus, H Baber, J Bavinton, M Burgess, LV Clark, DL Cox, JC DeCesare, P McCrone, G Murphy, M Murphy, H O’Dowd, T Peto, L Potts, R Walwyn, and D Wilks. This report is independent research partly arising from a doctoral research fellowship supported by the NIHR.

Fifteen of the authors of the 2011 Lancet PACE paper are no longer present, and another author has been added. The PACE Trial Management Group is again acknowledged, but there is no mention of the separate PACE trial group. We can’t tell why there has been a major reduction in the number of authors and acknowledgments or why it came about. Or whether people who would been dropped participated in a review of this paper. But what is obvious is that this is an exceedingly flawed mediation analysis crafted to a foregone conclusion. I’ll say more about that in future blogs, but we can only speculate how the bad publication practices made it through peer review.

This article is a crime against the practice of secondary mediation analyses. If I were a prospect of author present in a discussion, I would flee before it became a crime scene.

I am told I have over 350 publications, but I considered vulgar for authors to keep track of exact numbers. But there are many potential publications that are not included in this number because I declined authorship because I could not agree with the spin that others were trying to put on the reporting of the findings. In such instances, I exclude myself from review of the resulting manuscript because of the appearance of a conflict of interest. We can ponder how many of the large pool of past PACE authors refused authorship on this paper when it was offered and homely declined to participate in subsequent peer review because of the appearance of a conflict of interest.

The 2015 Lancet Psychiatry long-term follow-up article

Sharpe, M., Goldsmith, K. A., Chalder, T., Johnson, A.L., Walker, J., & White, P. D. (2015). Rehabilitative treatments for chronic fatigue syndrome: long-term follow-up from the PACE trial. The Lancet Psychiatry, http://dx.doi.org/10.1016/S2215-0366(15)00317-X

The acknowledgments include

We gratefully acknowledge the help of the PACE Trial Management Group, which consisted of the authors of this paper, plus (in alphabetical order): B Angus, H Baber, J Bavinton, M Burgess, L V Clark, D L Cox, J C DeCesare, E Feldman, P McCrone, G Murphy, M Murphy, H O’Dowd, T Peto, L Potts, R Walwyn, and D Wilks, and the King’s Clinical Trials Unit. We thank Hannah Baber for facilitating the long-term follow-up data collection.

Again, there are authors and acknowledgments missing from the early paper and were in the dark about how and why that happened and whether missing persons were considered free enough of conflict of interest to evaluate this article when it was in manuscript form. But as documented in a blog post at Mind the Brain, there were serious, obvious flaws in the conduct and reporting of the follow-up study. It is a crime against best practices for the proper conduct and reporting of clinical trials. And again we can speculate how it got through peer review.

… And grant reviews?

Where can UK granting agencies obtain independent peer review of past and future grants associated with the PACE trial? To take just one example, the 2015 Lancet Psychiatry secondary mediation analysis was funded in part by a NIHR doctoral research fellowship grant. The resulting paper has many fewer authors than the 2011 Lancet. Did everyone who was an author or mentioned in the acknowledgments on that paper exclude themselves from review of the screen? Who, then, would be left

In Germany and the Netherlands, concerns about avoiding the appearance of conflict of interest in obtaining independent peer review of grants has led to heavy reliance on expertise from outside the country. This does not imply any improprieties from expertise within these countries, but rather the necessity of maintaining a strong appearance that vested interests have not unduly influenced grant review. Perhaps the situation of apparent with the PACE trial suggests that journals and grant review panels within the UK might consider similar steps.

Contemplating the evidence against independent peer review

  • We have a mob of people as authors and mentions in acknowledgments. We have a huge conglomerate of institutions acknowledged.
  • We have some papers with blatant questionable research and reporting practices published in prestigious journals after ostensible peer review.
  • We are left in the dark about what exactly happened in peer review, but that the articles were adequately peer reviewed is a crucial part of their credability.

What are we to conclude?

The_Purloined_LetterI think of what Edgar Allen Poe’s wise character, Le Chevalier C. Auguste Dupin would say. For those of you who don’t know who he is:

Le Chevalier C. Auguste Dupin  is a fictional detective created by Edgar Allan Poe. Dupin made his first appearance in Poe’s “The Murders in the Rue Morgue” (1841), widely considered the first detective fiction story.[1] He reappears in “The Mystery of Marie Rogêt” (1842) and “The Purloined Letter” (1844)…

Poe created the Dupin character before the word detective had been coined. The character laid the groundwork for fictitious detectives to come, including Sherlock Holmes, and established most of the common elements of the detective fiction genre.

I think if we asked Dupin, he would say the danger is that the question is too fascinating to give up, but impossible to resolve without evidence we cannot access. We can blog, we can discuss this important question, but in the end we cannot answer it with certainty.


Sex and the single amygdala: A tale almost saved by a peek at the data

So sexy! Was bringing up ‘risky sex’ merely a strategy to publish questionable and uninformative science?

wikipedia 1206_FMRIMy continuing question: Can skeptics who are not specialists, but who are science-minded and have some basic skills, learn to quickly screen and detect questionable science in the journals and media coverage?

You don’t need a weatherman to know which way the wind blows.” – Bob Dylandylan wind blows

I hope so. One goal of my blogging is to arouse readers’ skepticism and provide them some tools so that they can decide for themselves what to believe, what to reject, and what needs a closer look or a check against trusted sources.

Skepticism is always warranted in science, but it is particularly handy when confronting the superficial application of neuroscience to every aspect of human behavior. Neuroscience is increasingly being brought into conversations to sell ideas and products when it is neither necessary nor relevant. Many claims about how the brain is involved are false or exaggerated not only in the media, but in the peer-reviewed journals themselves.

A while ago I showed how a neuroscientist and a workshop guru teamed up to try to persuade clinicians with functional magnetic resonance imaging (fMRI) data  that a couples therapy was more sciencey than the rest. Although I took a look at some complicated neuroscience, a lot of my reasoning [1, 2, 3] merely involved applying basic knowledge of statistics and experimental design. I raised sufficient skepticism to dismiss the neuroscientist and psychotherapy guru’s claims, Even putting aside the excellent specialist insights provided by Neurocritic and his friend Magneto.

In this issue of Mind the Brain, I’m pursuing another tip from Neurocritic about some faulty neuroscience in need of debunking.

The paper

Victor, E. C., Sansosti, A. A., Bowman, H. C., & Hariri, A. R. (2015). Differential Patterns of Amygdala and Ventral Striatum Activation Predict Gender-Specific Changes in Sexual Risk Behavior. The Journal of Neuroscience, 35(23), 8896-8900.

Unfortunately, the paper is behind a pay wall. If you can’t get it through a university library portal, you can send a request for a PDF to the corresponding author, elizabeth.victor@duke.edu.

The abstract

Although the initiation of sexual behavior is common among adolescents and young adults, some individuals express this behavior in a manner that significantly increases their risk for negative outcomes including sexually transmitted infections. Based on accumulating evidence, we have hypothesized that increased sexual risk behavior reflects, in part, an imbalance between neural circuits mediating approach and avoidance in particular as manifest by relatively increased ventral striatum (VS) activity and relatively decreased amygdala activity. Here, we test our hypothesis using data from seventy 18- to 22-year-old university students participating in the Duke Neurogenetics Study. We found a significant three-way interaction between amygdala activation, VS activation, and gender predicting changes in the number of sexual partners over time. Although relatively increased VS activation predicted greater increases in sexual partners for both men and women, the effect in men was contingent on the presence of relatively decreased amygdala activation and the effect in women was contingent on the presence of relatively increased amygdala activation. These findings suggest unique gender differences in how complex interactions between neural circuit function contributing to approach and avoidance may be expressed as sexual risk behavior in young adults. As such, our findings have the potential to inform the development of novel, gender-specific strategies that may be more effective at curtailing sexual risk behavior.

My thought processes

Hmm, sexual risk behavior -meaning number of partners? How many new partners during a follow-up period constitutes “risky” and does it matter whether safe sex was practiced? Well, ignoring these issues and calling it “sexual risk behavior “allows the authors to claim relevance to hot topics like HIV prevention….

But let’s cut to the chase: I’m always skeptical about a storyline depending on a three-way statistical interaction. These effects are highly unreliable, particularly in a sample size of only N = 70. I’m suspicious why investigators ahead of time staking their claims on a three-way interaction, not something simpler. I will be looking for evidence that they started with this hypothesis in mind, rather than cooking it up after peeking at the data.

fixed-designs-for-psychological-research-35-638Three-way interactions involve dividing a sample up into at eight boxes, in this case, 2 x (2) x (2). Such interactions can be mind-boggling to interpret, and this one is no exception

Although relatively increased VS activation predicted greater increases in sexual partners for both men and women, the effect in men was contingent on the presence of relatively decreased amygdala activation and the effect in women was contingent on the presence of relatively increased amygdala activation.

And then the “simple” interpretation?

These findings suggest unique gender differences in how complex interactions between neural circuit function contributing to approach and avoidance may be expressed as sexual risk behavior in young adults.

And the public health implications?

As such, our findings have the potential to inform the development of novel, gender-specific strategies that may be more effective at curtailing sexual risk behavior.

hs-amygdalaJust how should these data inform public health strategies beyond what we knew before we stumbled upon this article? Really, should we stick people’s heads in a machine and gather fMRI data  before offering them condoms? Should we encourage computer dating services to post along with a recent headshot, recent fMRI images showing that prospective dates do not have their risky behavior center in the amygdala activated? Or encourage young people to get their heads examined with an fMRI before deciding whether it’s wise to sleep with somebody new?

So it’s difficult to see the practical relevance of these findings, but let’s stick around and consider the paragraph that Neurocritic singled out.

The paragraph

outlierThe majority of the sample reported engaging in vaginal sex at least once in their lifetime (n = 42, 60%). The mean number of vaginal sexual partners at baseline was 1.28 (SD =0.68). The mean increase in vaginal sexual partners at the last follow-up was 0.71 (SD = 1.51). There were no significant differences between men and women in self-reported baseline or change in self-reported number of sexual partners (t=0.05, p=0.96; t=1.02, p= 0.31, respectively). Although there was not a significant association between age and self-reported number of partners at baseline (r = 0.17, p= 0.16), younger participants were more likely to report a greater increase in partners over time (r =0.24, p =0.04). Notably, distribution analyses revealed two individuals with outlying values (3 SD from M; both subjects reported an increase in 8 partners between baseline and follow up). Given the low rate of sexual risk behavior reported in the sample, these outliers were not excluded, as they likely best represent young adults engaging in sexual risk behavior.

What triggers skepticism?

This paragraph is quite revealing if we just ponder it a bit.

First, notice there is only a single significant correlation (p=.04) in a subgroup analysis. Differences between men and women were examined finding no significant findings in either baseline or changes in number of sexual partners over the length of the observation. However, disregarding that finding, the authors went on to explore changes in number of partners over time among the younger participants and, bingo, there was their p =0.04.

Whoa! Age was never mentioned in the abstract. We are now beyond the 2 x 2 x 2 interaction mentioned in the abstract and rooting through another dimension, younger versus older.

But, worse, getting that significance required retaining two participants with eight new sexual partners each during the follow-up period. The decision to retain these participants was made after the pattern of results was examined with and without inclusion of these outliers. The authors say so and essentially say they decided because it made a better story.

The only group means and standard deviation included these two participants. Even including the participants, the average number of new sexual partners was less than one during some follow-up. We have no idea whether that one was risky or not. It’s a safer assumption that having eight new partners is risky, but even that we don’t know for sure.

Keep in mind for future reference: Investigators are supposed to make decisions about outliers without reference to the fate of the hypothesis being studied. And knowing nothing about this particular study, most authorities would say if two people out of 70 are way out there on a particular variable that otherwise has little variance, you should exclude them.

It is considered a Questionable Research Practice to make decisions about inclusion/exclusion based on what story the outcome of this decision allows the authors to tell. It is p-hacking, and significance chasing.

And note the distribution of numbers of vaginal sex partners. Twenty eight participants had none at the end of the study. Most accumulated less than one during the follow up, and even that mean number was distorted by two having eight partners. Hmm, it is going to be hard to get multivariate statistics to work appropriately when we get to the fancy neuroscience data. We could go off on discussions of multivariate normal or Poisson distributions or just think a bit..

We can do a little detective work and determine that one outlier was a male, another a female. (*1) Let’s go back to our eight little boxes of participants that are involved in the interpretation of the three-way interaction. It’s going to make a great difference exactly where the deviant male and female are dropped into one of the boxes or whether they are left out.

And think about sampling issues. What if, for reasons having nothing to with the study, neither of these outliers had shown up? Or if only one of them had showed up, it would skew the results in a particular direction, depending on whether the participant was the male or female.

Okay, if we were wasting our time continuing to read the article after finding what we did in the abstract, we are certainly wasting more of our time by continuing after reading this paragraph. But let’s keep poking around as an educational exercise.

The rest of the methods and results sections

We learn from the methods section that there was an ethnically diverse sample with a highly variable follow-up, from zero days to 3.9 years (M = 188.72 d, SD = 257.15; range = 0 d–3.19 years). And there were only 24 men in the original sample for the paper of 70 participants.

We don’t know whether these two outliers had eight sexual partners within a week of the first assessment or they were the ones captured in extending the study to almost 4 years. That matters somewhat, but we also have to worry whether this was an appropriate sample – with so few participants in it in the first place and even fewer who had sex by the end of the study – and length of follow-up to do such a study. The mean follow-up of about six months and huge standard deviation suggest there is not a lot of evidence of risky behavior, at least in terms of casual vaginal sex.

This is all getting very funky.

So I wondered about the larger context of the study, with increasing doubts that the authors had gone to all this trouble just to test an a priori hypothesis about risky sex.

We are told that the larger context is the ongoing “Duke Neurogenetics Study (DNS), which assesses a wide range of behavioral and biological traits.” The extensive list of inclusions and exclusions suggests a much more ambitious study. If we had more time, we could go look up the Duke Neurogenetics Study and see if that’s the case. But I have a strong suspicion that the study was not organized around the specific research questions of this paper (*2). I really can’t tell without any preregistration of this particular paper but I certainly have questions about how much Hypothesizing after the Results Are Known (HARKing) is going on here in the refining of hypotheses and measures, and decisions about which data to report.

Further explorations of the results section

I remind readers that I know little about fMRI data. Put it aside and we can discover some interesting things reading through the brief results section.

Main effects of task

As expected, our fMRI paradigms elicited robust affect-related amygdala and reward-related VS activity across the entire parent sample of 917 participants (Fig. 1). In our substudy sample of 70 participants, there were no significant effects of gender (t(70) values < 0.88, p values >0.17) or age (r values < 0.22; p values > 0.07) on VS or amygdala activity in either hemisphere.

figure1Hmm, let’s focus on the second sentence first. The authors tell us absolutely nothing is going on in terms of differences in amygdala and reward-related VS activity in relation to age and gender in the sample of 70 participants in the current study. In fact, we don’t even need to know what “amygdala and reward-related VS activity” is to wonder why the first sentence of this paragraph directs us to a graph not of the 70 participants, but a larger sample of 917 participants. And when we go to figure 1, we see some wild wowie zowie, hit-the-reader-between-the-eyes differences (in technical terms, intraocular trauma) for women. And claims of p < 0.000001 twice. But wait! One might think significance of that magnitude would have to come from the 917 participants, except the labeling of the X-axis must come from the substudy of the 70 participants for whom data concerning number of sex partners was collected. Maybe the significance comes from the anchoring of one of the graph lines by the one wayout outlier.

Note that the outlier woman with eight partners anchors the blue line for High Left Amygdala. Without inclusion of that single woman, the nonsignificant trends between women with High Left Amygdala versus women with Low Left Amygdala would be reversed.

figure2The authors make much of the differences between Figure 1 showing Results for Women and Figure 2 showing Results for Men. The comparison seems dramatic except that, once again, the one outlier sends the red line for Low Left Amygdala off from the blue line for High Left Amygdala. Otherwise, there is no story to tell. Mind-boggling, but I think we can safely conclude that something is amiss in these Frankenstein graphs.

Okay, we should stop beating a corpse of an article. There are no vital signs left.

Alternatively, we could probe the section on Poisson regressions and minimally note some details. There is the flash of some strings of zeros in the P values, but it seems complicated and then we are warned off with “no factors survive Bonferroni correction.” And then in the next paragraph, we get to exploring dubious interactions. And there is the final insult of the authors bringing in a two-way interaction trending toward significance among men, p =.051.

But we were never told how all this would lead as we were promised in the end of the abstract, “to the development of novel, gender-specific strategies that may be more effective at curtailing sexual risk behavior.”

Rushing through the discussion section, we note the disclosure that

The nature of these unexpected gender differences on clear and warrants further consideration.

So, the authors confess that they did not start with expectations of finding a gender difference. They had nothing to report from a subset of data from an ambitious project put together for other purposes with an ill-suited follow-up for the research question (and even an ill-suited experimental task. They made a decision to include two outliers, salvaged some otherwise weak and inconsistent differences, and then constructed a story that depended on their inclusion. Bingo, they can survive confirmation bias and get published.

Readers might have been left with just their skepticism about the three-way interaction described in the abstract. However, the authors implicated themselves by disclosing in the article their examination of a distribution and reasons for including outlier. Then they further disclosed they did not start with a hypothesis about gender differences.

Why didn’t the editor and reviewers at Journal of Neuroscience (impact factor 6.344) do their job and cry foul? Questionable research practices (QRPs) are brought to us courtesy of questionable publication practices (QPPs).

And then we end with the confident

These limitations notwithstanding, our current results suggest the importance of considering gender-specific patterns of interactions between functional neural circuits supporting approach and avoidance in the expression of sexual risk behavior in young adults.

Yet despite this vague claim, the authors still haven’t explained how this research could be translated to practice.

Takeaway points for the future.

Without a tip from NeuroCritic, I might not have otherwise zeroed in on the dubious complex statistical interaction on which the storyline in the abstract depended. I also benefited from the authors for whatever reason telling us that they had peeked at the data and telling us further in the discussion that they had not anticipated the gender difference. With current standards for transparency and no preregistration of such studies, it would’ve been easy for us to miss what was done because the authors did not need to alert us. Until there are more and better standards enforced, we just need to be extra skeptical of claims of the application of neuroscience to everyday life.

Trust your skepticism.

Apply whatever you know about statistics and experimental methods. You probably know more than you think you do

Beware of modest sized neuroscience studies for which authors develop storylines from the patterning authors can discover in their data, not from a priori hypotheses suggested by a theory. If you keep looking around in the scientific literature and media coverage of it, I think you will find a lot of this QRP and QPP.

Don’t go into a default believe-it mode just because an article is peer-reviewed.


  1. If both the outliers were of the same gender, it would have been enough for that gender to have had significantly more sex partners than the other.
  1. Later we had told in the Discussion section that particular stimuli for which fMRI data were available were not chosen for relevance to the research question claimed for this this paper.

We did not measure VS and amygdala activity in response to sexually provocative stimuli but rather to more general representations of reward and affective arousal. It is possible that variability in VS and amygdala activity to such explicit stimuli may have different or nonexistent gender-specific patterns that may or may not map onto sexual risk behaviors.

Special thanks to Neurocritic for suggesting this blog post and for feedback, as well as to Neuroskeptic, Jessie Sun, and Hayley Jach for helpful feedback. However, @CoyneoftheRealm bears sole responsibility for any excesses or errors in this post.