The PACE PLOS One data will not be released and the article won’t be retracted

PLOS One has bought into discredited arguments about patient consent forms not allowing sharing of anonymized data. PLOS One is no longer at the vanguard of open science through routine data sharing.

mind the brain logo

Two years have passed since I requested release of the PLOS One PACE data, eight months since the Expression of Concern was posted. What can we expect?

expression of concern-page-0

9 dot problem
Solving the 9-dot problem involves paying attention and thinking outside the box.

If we spot some usually unrecognized connections, we can see the PLOS One editors are biased towards the PACE investigators, favoring them over other stakeholders in whether the data are released as promised..

Spoiler: The PLOS One Senior Editors completed the pre-specified process of deciding what to do about the data not being shared.  They took no action. Months later the Senior Editors reopened the process and invited one of PACE investigators Trudy Chalder’s outspoken co-authors to help them reconsider.

A lot of us weren’t cynical enough to notice.

International trends will continue toward making uploading data into publicly accessible repositories a requirement for publication. PLOS One has slowed down by buying into discredited arguments about patient consent forms not allowing sharing of anonymized data.

PLOS One is no longer at the vanguard of open science through routine data sharing.

The expression of concern

actual display of expression of concern on PLOS article
Actual Expression of Concern on display on PLOS One article.

The editors’ section of the Expression of Concern ends with:

In spite of requests to the authors and Queen Mary University of London, we have not yet received confirmation that an institutional process compatible with the existing PLOS data policy at the time has been developed or implemented for the independent evaluation of requests for data from this study. We conclude that the lack of resolution towards release of the dataset is not in line with the journal’s editorial policy and we are thus issuing this Expression of Concern to alert readers about the concerns raised about this article.

This is followed by the PACE investigators’ response:

Statement from the authors

We disagree with the Expression of Concern about our health economic paper that PLOS ONE has issued and do not accept that it is justified. We believe that data should be made available and have shared data from the PACE trial with other researchers previously, in line with our data sharing policy. This is consistent with the data sharing policies of Queen Mary University of London, and the Medical Research Council, which funded the trial. The policy allows for the sharing of data with other researchers, so long as safeguards are agreed regarding confidentiality of the data and consent as specified by the Research Ethics Committee (REC). We have also pointed out to PLOS ONE that our policy includes an independent appeal process, if a request is declined, so this policy is consistent with the journal’s policy when the paper was published.

During negotiations with the journal over these matters, we have sought further guidance from the PACE trial REC. They have advised that public release, even of anonymised data, is not appropriate. As a consequence, we are unable to publish the individual patient data requested by the journal. However, we have offered to provide key summarised data, sufficient to provide an independent re-analysis of our main findings, so long as it is consistent with the REC decision, on the PLOS ONE website. As such we are surprised by and question the decision by the journal to issue this Expression of Concern.

Check out my critique of their claim to have shared data from the PACE trial with other researchers-

Don’t bother to apply: PACE investigators issue guidance for researchers requesting access to data.

Nothing_to_DeclareConflict of interest: Nothing to declare?

 The PACE authors were thus given an extraordinary opportunity to undermine the editors’ Expression of Concern.

It is just as extraordinary that there is no disclosure of conflict of interest. After all, it is their paper is receiving expression of concern because of the authors’ failure to provide data as promised.

In contrast, when the PLOS One editors placed a discreet Editors Note in 2015 in the comment section of the article about the data not being shared when requested, it carried a COI declaration:

Competing interests declared: PLOS ONE Staff

That COI aroused the curiosity of Retraction Watch who asked PLOS One:

We weren’t sure what the last line was referring to, so contacted Executive Editor Veronique Kiermer. She told us that staff sometimes include their byline under “competing interests,” so the authorship is immediately clear to readers who may be scanning a series of comments.

Commentary from Retraction Watch

PLOS upgrades flag on controversial PACE chronic fatigue syndrome trial; authors “surprised”

Notable excerpts:

A spokesperson for PLOS told us this is the first time the journal has included a statement from the authors in an EOC:

This has been a complex case involving many stakeholders and we wanted to document the different aspects of the case in a fair manner.


We asked if the journal plans to retract the paper if the authors fail to provide what it’s asked for; the spokesperson explained:

At this time, PLOS stands by its Expression of Concern. For now, we have exhausted the options to make the data available in accordance with our policy at the time, but PLOS still seeks a positive outcome to this case for all parties. It is our intention to update this notice when a mechanism is established that allows concerns about the article’s analyses to be addressed while protecting patient privacy. PLOS has not given the authors a deadline.

Note: “PLOS did not given the authors a deadline.”

One of the readers who has requested the data is James Coyne, a psychologist at the University Medical Center, Groningen, who submitted his request 18 months ago (and wrote about it on the PLOS blog site). Although some of the data have been released (to one person under the Freedom of Information Act), it’s not nearly enough to conduct an analysis, Coyne told us:

This small data set does not allow recalculation of original primary outcomes but did allow recalculation of recovery data. Release of the PLOS data is crucial for a better understanding of what went on in that trial. That’s why the investigators are fighting so hard.

Eventually, Coyne began suggesting to PLOS that he would organize public protests and scientific meetings attended by journal representatives.

I think it is the most significant issue in psychotherapy today, in terms of data sharing. It’s a flagrant violation of international standards.

The Retraction Watch article cited a 2015 STAT article that was written by Retraction Watch co-founders Ivan Oransky and Adam Marcus. That article was sympathetic to my request:

If the information Coyne is seeking is harmful and distressing to the staff of the university — and that’s the university’s claim, not ours — that’s only because the information is in fact harmful and distressing. In other words, revealing that you have nothing to hide is much less embarrassing than revealing that you’re hiding something.

The STAT article also said:

To be clear, Coyne’s not asking for sex tapes or pictures of lab workers taking bong hits. He’s asking for raw data so that he can evaluate whether what a group of scientists reported in print is in fact what those data show. It’s called replication, and as Richard Smith, former editor of The BMJ (and a member of our board of directors), put it last week, the refusal goes “against basic scientific principles.” But, unfortunately, stubborn researchers and institutions have used legal roadblocks before to prevent scrutiny of science.

The PLOS One Editors’ blog  post.

The Expression of Concern was accompanied by a blog post from PLOS Iratxe Puebla, Managing Editor for PLOS ONE and Joerg Heber, Editor-in-Chief on May 2, 2017

Data sharing in clinical research: challenges and open opportunities

Since we feel we have exhausted the options to make the data available responsibly, and considering the questions that were raised about the validity of the article’s conclusions, we have decided to post an Expression of Concern [5] to alert readers that the data are not available in line with the journal’s editorial policy. It is our intention to update this notice when a mechanism is established that allows concerns about the article’s analyses to be addressed while protecting patient privacy.

This statement seems to suggest that the ball is in the PACE investigators’ court and that PLOS One editors are prepared to wait. But reading the rest of the blog post, it becomes apparent that PLOS One is wavering on the data sharing policy

Current challenges and opportunities ahead

During our follow up it became clear that there is little consensus of opinion on the sharing of this particular dataset. Experts from the Data Advisory Board whom we consulted expressed different views on the stringency of the journal reaction. Overall they agreed on the need to consider the risk to confidentiality of the trial participants and on the relevance of developing mechanisms for consideration of data requests by an independent body or committee. Interestingly, the ruling of the FOI Tribunal also indicated that the vote did not reflect a consensus among all committee members.

Fact checking the PLOS One’s Editors’ blog and a rebuttal

John Peter fact checked  the PLOS One editors’ blog. It came up short on a number of points.

“Interestingly, the ruling of the FOI Tribunal also indicated that the vote did not reflect a consensus among all committee members.”

This line is misleading and reveals either ignorance or misunderstanding of the decision in Matthees.

The Information Tribunal (IT) is not a committee. It is part of the courts system of England and Wales.

…the IT’s decisions may be appealed to a higher court. As QMUL chose not to exercise this right but to opt instead to accept the decision, then clearly it considered there were no grounds for appeal. The decision stands in its entirety and applies without condition or caveat.


The court had two decisions to make:

First, could and should trial data be released and if so what test should apply to determine whether particular data should be made public? Second, when that test is applied to this particular set of data, do they meet that test?

The unanimous decision on the first question was very clear: there is no legal or ethical consideration which prevents release; release is permitted by the consent forms; there is a strong public interest in the release; making data available advances legitimate scientific debate; and the data should be released.

The test set by this unanimous decision was simple: whether data can be anonymized. Furthermore, again unanimously, the Tribunal stated that the test for anonymization is not absolute. It is whether the risk of identification is reasonably likely, not whether it is remote, and whether patients can be identified without prior knowledge, specialist knowledge or equipment, or resort to criminality.

It was on applying this test to the data requested, on whether they could be properly anonymized, that the IT reached a majority decision.

On the principles, on how these decisions should be made, on the test which should be applied and on the nature of that test, the court was unanimous.

It should also be noted that to share data which have not been anonymized would be in breach of the Data Protection Act. QMUL has shared these data with other researchers. QMUL should either report itself to the Information Commissioner’s Office or accept that the data can be anonymized. In which case, the unanimous decision of the IT is very clear: the data should be shared.

PLOS ONE should apply the IT decision and its own regulations and demand the data be shared or the paper retracted.

Data Advisory Board

The Editors’ blog referred to “Experts from the Data Advisory Board.. express[ing] different views on the stringency of the journal reaction.”

That was a source of puzzlement for me. Established procedures make no provision for an advisory board as part of the process or any appeal.

A Google Search clarified. I had been to this page a number of times before and did not remember seeing this statement. There is no date or any indication it was added after the rest of the statement.

PLOS has formed an external board of advisors across many fields of research published in PLOS journals. This board will work with us to develop community standards for data sharing across various fields, provide input and advice on especially complex data-sharing situations submitted to the journals, define data-sharing compliance, and proactively work to refine our policy. If you have any questions or feedback, we welcome you to write to us at

The availability of data from reanalysis and independent probing has lots of stakeholders. Independent investigators, policymakers, and patients all have a stake. I don’t recognize the names on this list and see no indication that consumers affected by what is reported in clinical and health services papers have role in making decisions about the release of data. But one name stands out.

Who is Malcolm Macleod and what is he doing in this decision-making process?

Malcolm Macleod is quoted in the Science Media Centre reaction to the PACEgate special issue:

 Expert reaction to Journal of Health Psychology’s Special Issue on The PACE Trial

Prof. Malcolm Macleod, Professor of Neurology and Translational Neuroscience, University of Edinburgh, said:

“The PACE trial, while not perfect, provides far and away the best evidence for the effectiveness of any intervention for chronic fatigue; and certainly is more robust than any of the other research cited. Reading the criticisms, I was struck by how little actual meat there is in them; and wondered where some of the authors came from. In fact, one of them lists as an institution a research centre (Soerabaja Research Center) which only seems to exist as an affiliation on papers he wrote criticising the PACE trial.

“Their main criticisms seem to revolve around the primary outcome was changed halfway through the trial: there are lots of reasons this can happen, some justifiable and others not; the main think is whether it was done without knowledge of the outcomes already accumulated in the trial and before data lock – which is what was done here.

“So I don’t think there is really a story here, apart from a group of authors, some of doubtful provenance, kicking up dust about a study which has a few minor wrinkles (as all do) but still provides information reliable enough to shape practice. If you substitute ‘CFS’ for ‘autism’ and ‘PACE trial’ for ‘vaccination’ you see a familiar pattern…”

The declaration of interest is revealing in what it says and what it does not say.

Prof. MacLeod: “Prof Sharpe used to have an office next to my wife’s; and I sit on the PLoS Data board that considered what to do about one of their other studies.

The declaration fails to reveal a recent publication co-authored by Macleod and Trudy  Chalder.

Wu S, Mead G, Macleod M, Chalder T. Model of understanding fatigue after stroke. Stroke. 2015 Mar 1;46(3):893-8.

This press release comes from an organization strongly committed to the protection of the PACE trial from independent scrutiny. The SMC even organized a letter writing campaign headed by Peter White to petition Parliament to exclude universities for Freedom of Information Act requests. Of course, that will effectively block request for data.

Why would the PLOS One editors involved such a person to reconsider what been a decision in favor of releasing the data?

Connect the dots.

Trends will continue toward making uploading data into publicly accessible repositories a requirement for publication. PLOS One has bought into discredited arguments about patient consent forms not allowing sharing of anonymized data. PLOS One is no longer at the vanguard of open science through routine data sharing.

Better days: When PLOS Blogs honored my post about fatal flaws in the PACE chronic fatigue syndrome follow-up study (2015)

The back story on my receiving this honor was that PLOS Blogs only days before had shut down the blog site because of complaints from someone associated with the PACE trial. I was asked to resign. I refused. PLOS Blogs relented when I said it would be a publicity disaster for PLOS Blogs.

mind the brain logoThe back story on my receiving this honor was that PLOS Blogs only days before had shut down the blog site because of complaints from someone associated with the PACE trial. I was asked to resign. I refused. PLOS Blogs relented when I said it would be a publicity disaster for PLOS Blogs.

screen shot 11th most accessedA Facebook memory of what I was posting two years ago reminded me of better days when PLOS Blogs honored my post about the PACE trial.

Your Top 15 in ’15: Most popular on PLOS BLOGS Network

I was included in a list of the most popular blog posts in a network that received over 2.3 million visitors reading more than 600 new posts. [It is curious that the sixth and seventh most popular posts were omitted from this list, but that’s another story]

I was mentioned for number 11:

11) Uninterpretable: Fatal flaws in PACE Chronic Fatigue Syndrome follow-up study Mind the Brain 10/29/15

Investigating and sharing potential errors in scientific methods and findings, particularly involving psychological research, is the primary reason Clinical Health Psychologist (and PLOS ONE AE) Jim Coyne blogs on Mind the Brain and elsewhere. This closely followed post is one such example.

Earlier decisions by the investigator group preclude valid long-term follow-up evaluation of CBT for chronic fatigue syndrome (CFS). At the outset, let me say that I’m skeptical whether we can hold the PACE investigators responsible… Read more

The back story was that only days before, I had gotten complaints from readers of Mind the Brain who found they were blocked from leaving comments at my blog site. I checked and found that I couldn’t even access the blog as an author.

I immediately emailed Victoria Costello and asked her what it happened. We agreed to talk by telephone, even though it was already late night where I was in Philadelphia. She was in the San Francisco PLOS office.

In the telephone conversation,  I was reminded me that there were some topics about which was not supposed to blog. Senior management at PLOS found me in violation of that prohibition and wanted me to stop blogging.

As is often the case with communication with the senior management of PLOS, no specifics had been given.  There was no formal notice or disclosure about what topics I couldn’t blog or who had complained. And there had been no warning when my access to the blog site was cut. Anything that I might say publicly could be met with a plausible denial.

I reminded Victoria that I had never received any formal specification about what I could blog nor from whom the complaint hand come. There had been a vague communication from her about not blogging about certain topics. I knew that complaints from either Gabrielle Oettingen or her family members had led to request the blog about the flaws in her book,  Rethinking Positive Thinking . That was easy to do because I was not planning another post about that dreadful self-help book.  Any other prohibition was left so vague that had no idea that I couldn’t blog about the PACE trial. I had known that the authors of the British Psychological Society’s Understanding Psychosis were quite upset with what I had said in heavily accessed blog posts. Maybe that was the source of the other prohibition, but no one made that clear. And I wasn’t sure I wanted to honor it, anyway.

I pressed Victoria Costello for details. She said an editor had complained. When I asked if it was Richard Horton, she paused and mumbled something that I took as an affirmative. Victoria then suggested that  it would be best for the blog network and myself if we had a mutually agreed-upon parting of ways. I told her that I would probably publicly comment that the breakup was not mutual and it would be a publicity disaster for the blog.

igagged_jpg-scaled500Why I was even blogging for PLOS Blogs? Victoria Costello had recruited me over after I expressed discontent with the censorship that I was receiving at Psychology Today. The PT editors there had complained that some of my blogging about antidepressants might discourage ads from pharmaceutical companies for which they depended for revenue. The editors had insisted on  the right to approve my posts before I uploaded them. In inviting me to PLOS Blogs, Victoria told me that she too was a refugee from blogging at Psychology Today.  I wouldn’t have to worry about restrictions on what I could say at Mind the Brain, beyond avoiding libel.

I ended the conversation accepting the prohibition about blogging about the PACE trial. This is was despite disagreeing with the rationale that it would be a conflict of interest for me to blog about it after requesting the data from the PLOS One paper.

Since then, I repeatedly requested that the PLOS management acknowledge the prohibition on my blogging or at least put it in writing. My request was met with repeated refusals from Managing Editor Iratxe Puebla, who always cited my conflict of interest.

In early 2017, I began publicly tweeting about the issue, stimulating some curiosity others about whether there was a prohibition. InJuly 2017, the entire Mind the Brain site, not just my blog, was shut.

In early 2018, I will provide more backstory on that shutdown and dispute what was said in the blog post below. And more about the collusion between PLOS One senior management and the PACE investigators in the data not being available 2 years after I requested it.

Message for Mind the Brain readers from PLOSBLOGS

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This strange thumbnail is the default for when no preferred image is provided. It could indicate the haste with which this blog was posted.

Posted July 31, 2017 by Victoria Costello in Uncategorized

After five years and over a hundred posts, PLOSBLOGS is retiring its psychology blog, Mind the Brain, from our PLOS-hosted blog network. By mutual agreement with the primary Mind the Brain blogger, James Coyne, Professor Coyne will retain the name of this blog and will take his archive of posts for reuse on his independent website,

According to PLOSBLOGS’ policy for all our retired (inactive) blogs, any and all original posts published on Mind the Brain will retain their PLOS web addresses as intact urls, so links made previously from other sites will not be broken. In addition, PLOS will supply the archive of his posts directly to Prof Coyne so that he may repost them anywhere he may wish.

PLOS honors James Coyne’s voice as an important one in peer-to-peer scientific criticism. As discussed with Professor Coyne in recent days, after careful consideration PLOSBLOGS has concluded that it does not have the staff resources required to vet the sources, claims and tone contained in his posts, to assure they are aligned with our PLOSBLOGS Community Guidelines. This has lead us to the conclusion that Professor Coyne and his content would be better served on his own independent blog platform. We wish James Coyne the best with his future blogging.

—Victoria Costello, Senior Editor, PLOSBLOGS & Communities


Danish RCT of cognitive behavior therapy for whatever ails your physician about you

I was asked by a Danish journalist to examine a randomized controlled trial (RCT) of cognitive behavior therapy (CBT) for functional somatic symptoms. I had not previously given the study a close look.

I was dismayed by how highly problematic the study was in so many ways.

I doubted that the results of the study showed any benefits to the patients or have any relevance to healthcare.

I then searched and found the website for the senior author’s clinical offerings.  I suspected that the study was a mere experimercial or marketing effort of the services he offered.

Overall, I think what I found hiding in plain sight has broader relevance to scrutinizing other studies claiming to evaluate the efficacy of CBT for what are primarily physical illnesses, not psychiatric disorders. Look at the other RCTs. I am confident you will find similar problems. But then there is the bigger picture…

[A controversial assessment ahead? You can stop here and read the full text of the RCT  of the study and its trial registration before continuing with my analysis.]

Schröder A, Rehfeld E, Ørnbøl E, Sharpe M, Licht RW, Fink P. Cognitive–behavioural group treatment for a range of functional somatic syndromes: randomised trial. The British Journal of Psychiatry. 2012 Apr 13:bjp-p.

A summary overview of what I found:

 The RCT:

  • Was unblinded to patients, interventionists, and to the physicians continuing to provide routine care.
  • Had a grossly unmatched, inadequate control/comparison group that leads to any benefit from nonspecific (placebo) factors in the trial counting toward the estimated efficacy of the intervention.
  • Relied on subjective self-report measures for primary outcomes.
  • With such a familiar trio of design flaws, even an inert homeopathic treatment would be found effective, if it were provided with the same positive expectations and support as the CBT in this RCT. [This may seem a flippant comment that reflects on my credibility, not the study. But please keep reading to my detailed analysis where I back it up.]
  • The study showed an inexplicably high rate of deterioration in both treatment and control group. Apparent improvement in the treatment group might only reflect less deterioration than in the control group.
  • The study is focused on unvalidated psychiatric diagnoses being applied to patients with multiple somatic complaints, some of whom may not yet have a medical diagnosis, but most clearly had confirmed physical illnesses.

But wait, there is more!

  • It’s not CBT that was evaluated, but a complex multicomponent intervention in which what was called CBT is embedded in a way that its contribution cannot be evaluated.

The “CBT” did not map well on international understandings of the assumptions and delivery of CBT. The complex intervention included weeks of indoctrination of the patient with an understanding of their physical problems that incorporated simplistic pseudoscience before any CBT was delivered. We focused on goals imposed by a psychiatrist that didn’t necessarily fit with patients’ sense of their most pressing problems and the solutions.

OMGAnd the kicker.

  • The authors switched primary outcomes – reconfiguring the scoring of their subjective self-report measures years into the trial, based on a peeking at the results with the original scoring.

Investigators have a website which is marketing services. Rather than a quality contribution to the literature, this study can be seen as an experimercial doomed to bad science and questionable results from before the first patient was enrolled. An undeclared conflict of interest in play? There is another serious undeclared conflict of interest for one of the authors.

For the uninformed and gullible, the study handsomely succeeds as an advertisement for the investigators’ services to professionals and patients.

Personally, I would be indignant if a primary care physician tried to refer me or friend or family member to this trial. In the absence of overwhelming evidence to the contrary, I assume that people around me who complain of physical symptoms have legitimate physical concerns. If they do not yet have a confirmed diagnosis, it serves little purpose to stop the probing and refer them to psychiatrists. This trial operates with an anachronistic Victorian definition of psychosomatic condition.

something is rotten in the state of DenmarkBut why should we care about a patently badly conducted trial with switched outcomes? Is it only a matter of something being rotten in the state of Denmark? Aside from the general impact on the existing literature concerning CBT for somatic conditions, results of this trial  were entered into a Cochrane review of nonpharmacological interventions for medically unexplained symptoms. I previously complained about one of the authors of this RCT also being listed as an author on another Cochrane review protocol. Prior to that, I complained to Cochrane  about this author’s larger research group influencing a decision to include switched outcomes in another Cochrane review.  A lot of us rightfully depend heavily on the verdict of Cochrane reviews for deciding best evidence. That trust is being put into jeopardy.

Detailed analysis

1.This is an unblinded trial, a particularly weak methodology for examining whether a treatment works.

The letter that alerted physicians to the trial had essentially encouraged them to refer patients they were having difficulty managing.

‘Patients with a long-term illness course due to medically unexplained or functional somatic symptoms who may have received diagnoses like fibromyalgia, chronic fatigue syndrome, whiplash associated disorder, or somatoform disorder.

Patients and the physicians who referred them subsequently got feedback about to which group patients were assigned, either routine care or what was labeled as CBT. This information could have had a strong influence on the outcomes that were reported, particularly for the patients left in routine care.

Patients’ learning that they did not get assigned to the intervention group was undoubtedly disappointing and demoralizing. The information probably did nothing to improve the positive expectations and support available to patients in routine. This could have had a nocebo effect. The feedback may have contributed to the otherwise  inexplicably high rates of subjective deterioration [to be noted below] reported by patients left in the routine care condition. In contrast, the authors’ disclosure that patients had been assigned to the intervention group undoubtedly boosted the morale of both patients and physicians and also increased the gratitude of the patients. This would be reflected in the responses to the subjective outcome measures.

The gold standard alternative to an unblinded trial is a double-blind, placebo-controlled trial in which neither providers, nor patients, nor even the assessors rating outcomes know to which group particular patients were assigned. Of course, this is difficult to achieve in a psychotherapy trial. Yet a fair alternative is a psychotherapy trial in which patients and those who refer them are blind to the nature of the different treatments, and in which an effort is made to communicate credible positive expectations about the comparison control group.

Conclusion: A lack of blinding seriously biases this study toward finding a positive effect for the intervention, regardless of whether the intervention has any active, effective component.

2. A claim that this is a randomized controlled trial depends on the adequacy of the control offered by the comparison group, enhanced routine care. Just what is being controlled by the comparison? In evaluating a psychological treatment, it’s important that the comparison/control group offers the same frequency and intensity of contact, positive expectations, attention and support. This trial decidedly did not.

 There were large differences between the intervention and control conditions in the amount of contact time. Patients assigned to the cognitive therapy condition received an additional 9 group sessions with a psychiatrist of 3.5 hour duration, plus the option of even more consultations. The over 30 hours of contact time with a psychiatrist should be very attractive to patients who wanted it and could not otherwise obtain it. For some, it undoubtedly represented an opportunity to have someone to listen to their complaints of pain and suffering in a way that had not previously happened. This is also more than the intensity of psychotherapy typically offered in clinical trials, which is closer to 10 to 15, 50-minute sessions.

The intervention group thus received substantially more support and contact time, which was delivered with more positive expectations. This wealth of nonspecific factors favoring the intervention group compromises an effort to disentangle the specific effects of any active ingredient in the CBT intervention package. From what has been said so far, the trials’ providing a fair and generalizable evaluation of the CBT intervention is nigh impossible.

Conclusion: This is a methodologically poor choice of control groups with the dice loaded to obtain a positive effect for CBT.

3.The primary outcomes, both as originally scored and after switching, are subjective self-report measures that are highly responsive to nonspecific treatments, alleviation of mild depressive symptoms and demoralization. They are not consistently related to objective changes in functioning. They are particularly problematic when used as outcome measures in the context of an unblinded clinical trial within an inadequate control group.

There have been consistent demonstrations that assigning patients to inert treatments and measuring the outcomes with subjective measures may register improvements that will not correspond to what would be found with objective measures.

For instance, a provocative New England Journal of Medicine study showed that sham acupuncture as effective as an established medical treatment – an albuterol inhaler – for asthma when judged with subjective measures, but there was a large superiority for the established medical treatment obtained with objective measures.

There have been a number of demonstrations that treatments such as the one offered in the present study to patient populations similar to those in the study produce changes in subjective self-report that are not reflected in objective measures.

Much of the improvement in primary outcomes occurred before the first assessment after baseline and not very much afterwards. The early response is consistent with a placebo response.

The study actually included one largely unnoticed objective measure, utilization of routine care. Presumably if the CBT was effective as claimed, it would have produced a significant reduction in healthcare utilization. After all, isn’t the point of this trial to demonstrate that CBT can reduce health-care utilization associated with (as yet) medically unexplained symptoms? Curiously, utilization of routine care did not differ between groups.

The combination of the choice of subjective outcomes, unblinded nature of the trial, and poorly chosen control group bring together features that are highly likely to produce the appearance of positive effects, without any substantial benefit to the functioning and well-being of the patients.

Conclusion: Evidence for the efficacy of a CBT package for somatic complaints that depends solely on subjective self-report measures is unreliable, and unlikely to generalize to more objective measures of meaningful impact on patients’ lives.

4. We need to take into account the inexplicably high rates of deterioration in both groups, but particularly in the control group receiving enhanced care.

There was an unexplained deterioration of 50% deterioration in the control group and 25% in the intervention group. Rates of deterioration are only given a one-sentence mention in the article, but deserve much more attention. These rates of deterioration need to qualify and dampen any generalizable clinical interpretation of other claims about outcomes attributed to the CBT. We need to keep in mind that the clinical trials cannot determine how effective treatments are, but only how different a treatment is from a control group. So, an effect claimed for a treatment and control can largely or entirely come from deterioration in the control group, not what the treatment offers. The claim of success for CBT probably largely depends on the deterioration in the control group.

One interpretation of this trial is that spending an extraordinary 30 hours with a psychiatrist leads to only half the deterioration experienceddoing nothing more than routine care. But this begs the question of why are half the patients left in routine care deteriorating in such a large proportion. What possibly could be going on?

Conclusion: Unexplained deterioration in the control group may explain apparent effects of the treatment, but both groups are doing badly.

5. The diagnosis of “functional somatic symptoms” or, as the authors prefer – Severe Bodily Distress Syndromes – is considered by the authors to be a psychiatric diagnosis. It is not accepted as a valid diagnosis internationally. Its validation is limited to the work done almost entirely within the author group, which is explicitly labeled as “preliminary.” This biased sample of patients is quite heterogeneous, beyond their physicians having difficulty managing them. They have a full range of subjective complaints and documented physical conditions. Many of these patients would not be considered primarily having a psychiatric disorder internationally and certainly within the US, except where they had major depression or an anxiety disorder. Such psychiatric disorders were not an exclusion criteria.

Once sent on the pathway to a psychiatric diagnosis by their physicians’ making a referral to the study, patients had to meet additional criteria:

To be eligible for participation individuals had to have a chronic (i.e. of at least 2 years duration) bodily distress syndrome of the severe multi-organ type, which requires functional somatic symptoms from at least three of four bodily systems, and moderate to severe daily living.

The condition identified in the title of the article is not validated as a psychiatric diagnosis. Two papers to which the authors refer to their  own studies ( 1 , 2 ) from a single sample. The title of one of these papers makes a rather immodest claim:

Fink P, Schröder A. One single diagnosis, bodily distress syndrome, succeeded to capture 10 diagnostic categories of functional somatic syndromes and somatoform disorders. Journal of Psychosomatic Research. 2010 May 31;68(5):415-26.

In neither the two papers nor the present RCT is there sufficient effort to rule out a physical basis for the complaints qualifying these patients for a psychiatric diagnosis. There is also a lack of follow-up to see if physical diagnoses were later applied.

Citation patterns of these papers strongly suggest  the authors are not having got much traction internationally. The criteria of symptoms from three out of four bodily systems is arbitrary and unvalidated. Many patients with known physical conditions would meet these criteria without any psychiatric diagnosis being warranted.

The authors relate what is their essentially homegrown diagnosis to functional somatic syndromes, diagnoses which are themselves subject to serious criticism. See for instance the work of Allen Frances M.D., who had been the chair of the American Psychiatric Association ‘s Diagnostic and Statistical Manual (DSM-IV) Task Force. He became a harsh critic of its shortcomings and the failures of APA to correct coverage of functional somatic syndromes in the next DSM.

Mislabeling Medical Illness As Mental Disorder

Unless DSM-5 changes these incredibly over inclusive criteria, it will greatly increase the rates of diagnosis of mental disorders in the medically ill – whether they have established diseases (like diabetes, coronary disease or cancer) or have unexplained medical conditions that so far have presented with somatic symptoms of unclear etiology.


The diagnosis of mental disorder will be based solely on the clinician’s subjective and fallible judgment that the patient’s life has become ‘subsumed’ with health concerns and preoccupations, or that the response to distressing somatic symptoms is ‘excessive’ or ‘disproportionate,’ or that the coping strategies to deal with the symptom are ‘maladaptive’.


 “These are inherently unreliable and untrustworthy judgments that will open the floodgates to the overdiagnosis of mental disorder and promote the missed diagnosis of medical disorder.

The DSM 5 Task force refused to adopt changes proposed by Dr. Frances.

Bad News: DSM 5 Refuses to Correct Somatic Symptom Disorder

Leading Frances to apologize to patients:

My heart goes out to all those who will be mislabeled with this misbegotten diagnosis. And I regret and apologize for my failure to be more effective.

The chair of The DSM Somatic Symptom Disorder work group has delivered a scathing critique of the very concept of medically unexplained symptoms.

Dimsdale JE. Medically unexplained symptoms: a treacherous foundation for somatoform disorders?. Psychiatric Clinics of North America. 2011 Sep 30;34(3):511-3.

Dimsdale noted that applying this psychiatric diagnosis sidesteps the quality of medical examination that led up to it. Furthermore:

Many illnesses present initially with nonspecific signs such as fatigue, long before the disease progresses to the point where laboratory and physical findings can establish a diagnosis.

And such diagnoses may encompass far too varied a group of patients for any intervention to make sense:

One needs to acknowledge that diseases are very heterogeneous. That heterogeneity may account for the variance in response to intervention. Histologically, similar tumors have different surface receptors, which affect response to chemotherapy. Particularly in chronic disease presentations such as irritable bowel syndrome or chronic fatigue syndrome, the heterogeneity of the illness makes it perilous to diagnose all such patients as having MUS and an underlying somatoform disorder.

I tried making sense of a table of the additional diagnoses that the patients in this study had been given. A considerable proportion of patients had physical conditions that would not be considered psychiatric problems in the United States.. Many patients could be suffering from multiple symptoms not only from the conditions, but side effects of the medications being offered. It is very difficult to manage multiple medications required by multiple comorbidities. Physicians from the community found their competence and ability to spend time with these patients taxing.

table of functional somatic symptoms

Most patients had a diagnosis of “functional headaches.” It’s not clear what this designation means, but conceivably it could include migraine headaches, which are accompanied by multiple physical complaints. CBT is not an evidence-based treatment of choice for functional headaches, much less migraines.

Over a third of the patients had irritable bowel syndrome (IBS). A systematic review of the comorbidity  of irritable bowel syndrome concluded physical comorbidity is the norm in IBS:

The nongastrointestinal nonpsychiatric disorders with the best-documented association are fibromyalgia (median of 49% have IBS), chronic fatigue syndrome (51%), temporomandibular joint disorder (64%), and chronic pelvic pain (50%).

In the United States, many patients and specialists would consider considering irritable bowel syndrome as a psychiatric condition offensive and counterproductive. There is growing evidence that irritable bowel syndrome is a disturbance in the gut microbiota. It involves a gut-brain interaction, but the primary direction of influence is of the disturbance in the gut on the brain. Anxiety and depression symptoms are secondary manifestations, a product of activity in the gut influencing the nervous system.

Most of the patients in the sample had a diagnosis of fibromyalgia and over half of all patients in this study had a diagnosis of chronic fatigue syndrome.

Other patients had diagnosable anxiety and depressive disorders, which, particularly at the lower end of severity, are responsive to nonspecific treatments.

Undoubtedly many of these patients, perhaps most of them, are demoralized by not been able to get a  diagnosis for what they have good basis to believe is a medical condition, aside from the discomfort, pain, and interference with their life that they are experiencing. They could be experiencing a demoralization secondary to physical illness.

These patients presented with pain, fatigue, general malaise, and demoralization. I have trouble imagining how their specific most pressing concerns could be addressed in group settings. These patients pose particular problems for making substantive clinical interpretation of outcomes that are highly general and subjective.

Conclusion: Diagnosing patients with multiple physical symptoms as having a psychiatric condition is highly controversial. Results will not generalize to countries and settings where the practice is not accepted. Many of the patients involved in the study had recognizable physical conditions, and yet they are being shunted to psychiatrists who focused only on their attitude towards the symptoms. They are being denied the specialist care and treatments that might conceivably reduce the impact of their conditions on their lives

6. The “CBT” offered in this study is as part of a complex, multicomponent treatment that does not resemble cognitive behavior therapy as it is practiced in the United States.

it is thoughtAs seen in figure 1 in the article, The multicomponent intervention is quite complex and consists of more than cognitive behavior therapy. Moreover, at least in the United States, CBT has distinctive elements of collaborative empiricism. Patients and therapist work together selecting issues on which to focus, developing strategies, with the patients reporting back on efforts to implement them. From the details available in the article, the treatment sounded much more like an exhortation or indoctrination, even arguing with the patients, if necessary. An English version available on the web of the educational material used in initial sessions confirmed a lot of condescending pseudoscience was presented to convince the patients that their problems were largely in their heads.

Without a clear application of learning theory, behavioral analysis, or cognitive science, the “CBT”  treatment offered in this RCT has much more in common with the creative novation therapy offered by Hans Eysenck, which is now known to have been justified with fraudulent data. Indeed,  the educational materials  for this study to what is offered in Eysenck’s study reveal striking similarities. Eysenck was advancing the claim that his intervention could prevent cardiovascular disease and cancer and overcome the iatrogenic effects. I know, this sounds really crazy, but see my careful documentation elsewhere.

Conclusion: The embedding of an unorthodox “CBT” in a multicomponent intervention in this study does not allow isolating any specific, active component ofCBT that might be at work.

7. The investigators disclose having altered their scoring of their primary outcome years after the trial began, and probably after a lot of outcome data had been collected.

I found a casual disclosure in the method section of this article unsettling, particularly noting that the original trial registration was:

We found an unexpected moderate negative correlation of the physical and mental component summary measures, which are constructed as independent measures. According to the SF-36 manual, a low or zero correlation of the physical and mental components is a prerequisite of their use.23 Moreover, three SF-36 scales that contribute considerably to the PCS did not fulfil basic scaling assumptions.31 These findings, together with a recent report of problems with the PCS in patients with physical and mental comorbidity,32 made us concerned that the PCS would not reliably measure patients’ physical health in the study sample. We therefore decided before conducting the analysis not to use the PCS, but to use instead the aggregate score as outlined above as our primary outcome measure. This decision was made on 26 February 2009 and registered as a protocol change at clinical trials. gov on 11 March 2009. Only baseline data had been analysed when we made our decision and the follow-up data were still concealed.

Switching outcomes, particularly after some results are known, constitutes a serious violation of best research practices and leads to suspicion of the investigators refining their hypotheses after they had peeked at the data. See How researchers dupe the public with a sneaky practice called “outcome switching”.

The authors had originally proposed a scoring consistent with a very large body of literature. Dropping the original scoring precludes any direct comparison with this body of research, including basic norms. They claim that they switched scoring because two key subscales were correlated in the opposite direction of what is reported in the larger literature. This is troubling indication that something has gone terribly wrong in authors’ recruitment of a sample. It should not be pushed under the rug.

The authors claim that they switched outcomes based only on examining of baseline data from their study. However, one of the authors, Michael Sharpe is also an author on the controversial PACE trial  A parallel switch was made to the scoring of the subjective self-reports in that trial. When the data were eventually re-analyzed using the original scoring, any positive findings for the trial were substantially reduced and arguably disappeared.

Even if the authors of the present RCT did not peekat their outcome data before deciding to switch scoring of the primary outcome, they certainly had strong indications from other sources that the original scoring would produce weak or null findings. In 2009, one of the authors, Michael Sharpe had access to results of a relevant trial. What is called the FINE trial had null findings, which affected decisions to switch outcomes in the PACE trial. Is it just a coincidence that the scoring of the outcomes was then switched for the present RCT?

Conclusion: The outcome switching for the present trial  represents bad research practices. For the trial to have any credibility, the investigators should make their data publicly available so these data could be independently re-analyzed with the original scoring of primary outcomes.

The senior author’s clinic

 I invite readers to take a virtual tour of the website for the senior author’s clinical services  ]. Much of it is available in English. Recently, I blogged about dubious claims of a health care system in Detroit achieving a goal of “zero suicide.” . I suggested that the evidence for this claim was quite dubious, but was a powerful advertisement for the health care system. I think the present report of an RCT can similarly be seen as an infomercial for training and clinical services available in Denmark.

Conflict of interest

 No conflict of interest is declared for this RCT. Under somewhat similar circumstances, I formally complained about undeclared conflicts of interest in a series of papers published in PLOS One. A correction has been announced, but not yet posted.

Aside from the senior author’s need to declare a conflict of interest, the same can be said for one of the authors, Michael Sharpe.

Apart from the professional and reputational interest, (his whole career has been built making strong claims about such interventions) Sharpe works for insurance companies, and publishes on the subject. He declared a conflict of interest for the for PACE trial.

MS has done voluntary and paid consultancy work for government and for legal and insurance companies, and has received royalties from Oxford University Press.

Here’s Sharpe’s report written for the social benefits reinsurance company UnumProvident.

If results of this are accepted at face, they will lend credibility to the claims that effective interventions are available to reduce social disability. It doesn’t matter that the intervention is not effective. Rather persons receiving social disability payments can be disqualified because they are not enrolled in such treatment.

Effects on the credibility of Cochrane collaboration report

The switched outcomes of the trial were entered into a Cochrane systematic review, to which primary care health professionals look for guidance in dealing with a complex clinical situation. The review gives no indication of the host of problems that I exposed here. Furthermore, I have glanced at some of the other trials included and I see similar difficulties.

I been unable to convince the Cochrane to clean up conflicts of interest that are attached to switched outcomes being entered in reviews. Perhaps some of my readers will want to approach Cochrane to revisit this issue.
I think this post raises larger issues about whether Cochrane has any business conducting and disseminating reviews of such a bogus psychiatric diagnosis, medically unexplained symptoms. These reviews do patients no good, and may sidetrack them from getting the medical care they deserve. The reviews do serve the interest of special interests, including disability insurance companies.

Special thanks to John Peters and to Skeptical Cat for their assistance with my writing this blog. However, I have sole responsibility for any excesses or distortions.


What patients should require before consenting to participate in research…

A bold BMJ editorial  calls for more patient involvement in the design, implementation, and interpretation of research – but ends on a sobering note: The BMJ has so little such involvement to report.

In this edition of Mind the Brain, I suggest how patients, individually and collectively, can take responsibility for advancing this important initiative themselves.

I write in a context defined by recent events.

  • Government-funded researchers offered inaccurate interpretations of their results [1, 2].
  • An unprecedented number of patients have judged the researchers’ interpretation of their results as harmful to their well-being.
  • The researchers then violated government-supported data sharing policies in refusing to release their data for independent analysis.
  • Patients were vilified in the investigators’ efforts to justify their refusal to release the data.

These events underscore the need for patients to require certain documentation before deciding whether to participate in research.

Declining to participate in clinical research is a patient’s inalienable right that must not jeopardize the receipt of routine treatment or lead to retaliation.

A simple step: in deciding whether to participate in research, patients can insist that any consent form they sign contains documentation of patient involvement at all phases of the research. If there is no detailing of how patients were involved in the design of this study and how they will be involved in the interpretation, patients should consider not consenting.

Similarly, patients should consider refusing to sign consent forms that do not expressly indicate that the data will be readily available for further analyses, preferably by placing the data in a publicly accessible depository.

Patients exercising their rights in these ways will make for better and more useful biomedical research, as well as research that is more patient-oriented

The BMJ editorial

bmj-logo-ogThe editorial Research Is the Future, Get Involved declares:

More than three million NHS patients took part in research over the past five years. Bravo. Now let’s make sure that patients are properly involved, not just as participants but in trial conception, design, and conduct and the analysis, reporting, and dissemination of results.

But in the next sentences, the editorial describes how The BMJ’s laudable efforts to get researchers to demonstrate how patients were involved have not produced impressive results:

man with empty pocketsYou may have noticed the new “patient involvement” box in The BMJ’s research articles. Sadly, all too often the text reads something like, “No patients were involved in setting the research question or the outcome measures; nor were they involved in the design and implementation of the study. There are no plans to involve patients in the dissemination of results.” We hope that the shock of such statements will stimulate change. Examples of good patient involvement will also help: see the multicentre randomised trial on stepped care for depression and anxiety (doi:10.1136/bmj.h6127).

Our plan is to shine a light on the current state of affairs and then gradually raise the bar. Working with other journals, research funders, and ethics committees, we hope that at some time in the future only research in which patients have been fully involved will be considered acceptable.

In their instructions to authors, The BMJ includes a section Reporting patients’ involvement in research which states:

As part of its patient partnership strategy, The BMJ is encouraging active patient involvement in setting the research agenda.

We appreciate that not all authors of research papers will have done this, and we will still consider your paper if you did not involve patients at an early stage. We do, however, request that all authors provide a statement in the methods section under the subheading Patient involvement.

This should provide a brief response to the following questions:

How was the development of the research question and outcome measures informed by patients’ priorities, experience, and preferences?

How did you involve patients in the design of this study?

Were patients involved in the recruitment to and conduct of the study?

How will the results be disseminated to study participants?

For randomised controlled trials, was the burden of the intervention assessed by patients themselves?

Patient advisers should also be thanked in the contributorship statement/acknowledgements.

If patients were not involved please state this.

If this information is not in the submitted manuscript we will ask you to provide it during the peer review process.

Please also note also note that The BMJ now sends randomised controlled trials and other relevant studies for peer review by patients.

Recent events suggest that these instructions should be amended with the following question:

How were patients involved in the interpretation of results?

The instructions to authors should also elaborate that the intent is require description of how results were shared with patients before publication and dissemination to the news media. This process should be interactive with the possibility of corrective feedback, rather than a simple presentation of the results to the patients without opportunity for comment or for suggesting qualification of the interpretations that will be made. This process should be described in the article.

partnering with patientsMaterial offered by The BMJ in support of their initiative include an editorial, Patient Partnership, which explains:

The strategy brings landmark changes to The BMJ’s internal processes, and seeks to place the journal at the forefront of the international debate on the science, art, and implementation of meaningful, productive partnership with patients. It was “co –produced” with the members of our new international patient advisory panel, which was set up in January 2014. It’s members continue to inform our thinking and help us with implementation of our strategy.

patient includedFor its efforts, The BMJ has been the first medical journal to receive the “Patients Included” Certificate from Lucien Engelen’s Radboud REshape Academy. For his part, Lucien had previously announced:

I will ‘NO-SHOW’ at healthcare conferences that do not add patients TO or IN their programme or invite them to be IN the audience. Also I will no longer give lectures/keynotes at ‘NO-SHOW’ conferences.

But strong words need an action plan to become more than mere words. Although laudable exceptions can be noted, they are few and far between.

In Beyond rhetoric: we need a strategy for patient involvement in the health service, NHS user Sarah Thornton has called the UK government to task for being heavy on the hyperbole of empowering patients but lacking a robust strategy for implementing it. The same could be said for the floundering effort of The BMJ to support patient empowerment in research.

So, should patients just remain patient, keep signing up for clinical trials and hope that funders eventually get more patient oriented in the decisions about grants and that researchers eventually become more patient-oriented?

Recent events suggest that is unwise.

The BMJ patient-oriented initiative versus the PACE investigators’ refusal to share data and the vilification of patients who object to their interpretation of the data

As previously detailed here  the PACE investigators have steadfastly refused to provide the data for independent evaluation of claims. In doing so, they are defying numerous published standards from governmental and funding agencies that dictate sharing of data. Ironically, in justifying this refusal, the investigators cite possible repercussions of releasing the data for the ability to conduct future research.

Fortunately, in a decision against the PACE investigators, the UK Information Commissioner’s Office (ICO) rejected this argument because

He is also not convinced that there is sufficient evidence for him to determine that disclosure would be likely to deter significant numbers of other potential participants from volunteering to take part in future studies so as to affect the University’s ability to undertake such research. As a result, the Commissioner is reluctant to accept that disclosure of the withheld information would be likely to have an adverse effect on the University’s future ability to attract necessary funding and to carry out research in this area, with a consequent effect on its reputation and ability to recruit staff and students.

But the PACE investigators have appealed this decision and continue to withhold their data. Moreover in their initial refusal to share the data, they characterized patients who objected to the possible harm of their interpretations as a small vocal minority.

“The PACE trial has been subject to extreme scrutiny and opponents have been against it for several years. There has been a concerted effort by a vocal minority whose views as to the causes and treatment of CFS/ME do not comport with the PACE trial and who, it is QMUL’s belief, are trying to discredit the trial. Indeed, as noted by the editor of the Lancet, after the 2011 paper’s publication, the nature of this comprised not a ‘scientific debate’ but an “orchestrated response trying to undermine the credibility of the study from patient groups [and]… also the credibility of the investigators and that’s what I think is one of the other alarming aspects of this. This isn’t a purely scientific debate; this is going to the heart of the integrity of the scientists who conducted this study.”

Physician Charles Shepherd, himself a sufferer of myalgic encephalomyelitis (ME) notes:

  • Over 10,000 people signed a petition calling for claims of the PACE investigators relating to so-called recovery to be retracted.
  • In a survey of 1,428 people with ME, 73 per cent reported that CBT had no effect on symptoms while 74 per cent reported that GET had made their condition worse.

The BMJ’s position on data sharing

A May 15, 2015 editorial spelled out a new policy at The BMJ concerning data sharing, The BMJ requires data sharing on request for all trials:

Heeding calls from the Institute of Medicine, WHO, and the Nordic Trial Alliance, we are extending our policy

The movement to make data from clinical trials widely accessible has achieved enormous success, and it is now time for medical journals to play their part. From 1 July The BMJ will extend its requirements for data sharing to apply to all submitted clinical trials, not just those that test drugs or devices.1 The data transparency revolution is gathering pace.2 Last month, the World Health Organization (WHO) and the Nordic Trial Alliance released important declarations about clinical trial transparency.3 4

Note that The BMJ was making the data sharing requirement to all trials, not just medical and medical device trials.

But The BMJ was simply following the lead of the family of PLOS journals that made an earlier, broader, and simpler commitment to data from clinical trials being available to others.

plosThe PLOS journals’ policy on data sharing

On December 12, 2013, the PLOS journals scooped other major publishers with:

PLOS journals require authors to make all data underlying the findings described in their manuscript fully available without restriction, with rare exception.

When submitting a manuscript online, authors must provide a Data Availability Statement describing compliance with PLOS’s policy. The data availability statement will be published with the article if accepted.

Refusal to share data and related metadata and methods in accordance with this policy will be grounds for rejection. PLOS journal editors encourage researchers to contact them if they encounter difficulties in obtaining data from articles published in PLOS journals. If restrictions on access to data come to light after publication, we reserve the right to post a correction, to contact the authors’ institutions and funders, or in extreme cases to retract the publication

This requirement took effect on March 1, 2014. However, one of the most stringent of data sharing policies in the industry was already in effect.

Publication is conditional upon the agreement of the authors to make freely available any materials and information described in their publication that may be reasonably requested by others for the purpose of academic, non-commercial research.

Even the earlier requirement for publication in PLOS journals would have forestalled the delays, struggles, and complicated quasi-legal maneuvering to characterized the PACE investigators’ refusing to release their data.

Why medically ill people agree to be in clinical research

Patients are not obligated to participate in research, but should freely choose whether to participate based on a weighing of the benefits and risk. Consent to treatment in clinical research needs to be voluntary and fully informed.

Medically ill patients often cannot expect direct personal benefit from participating in a research trial. This is particularly true when trials involve comparison of a treatment that they want that is not otherwise available, but they risk getting randomized to a poorly defined and inadequate routine care. Their needs continue to be neglected, but now burdened by multiple and sometimes intrusive assessments. This is also the case with descriptive observational research and particularly phase 1 clinical studies that provide no direct benefit to participating patients, only the prospect of improving the care of future patients.

In recognition that many research projects do not directly benefit individual patients, consent forms identify possible benefits to other current and future patients and to society at large.

Protecting the rights of participants in research

The World Medical Association (WMA) Declaration of Helsinki – Ethical Principles for Medical Research Involving Human Subjects spells out a set of principles protecting the rights of human subjects, it includes:

In medical research involving human subjects capable of giving informed consent, each potential subject must be adequately informed of the aims, methods, sources of funding, any possible conflicts of interest, institutional affiliations of the researcher, the anticipated benefits and potential risks of the study and the discomfort it may entail, post-study provisions and any other relevant aspects of the study. The potential subject must be informed of the right to refuse to participate in the study or to withdraw consent to participate at any time without reprisal. Special attention should be given to the specific information needs of individual potential subjects as well as to the methods used to deliver the information.

Can patients pick up the challenge of realizing the promise of The BMJ editorial, Research Is the Future, Get Involved ?

One patient to whom I showed an earlier draft objected that this is just another burden being thrust on medical patients who already have their condition and difficult treatment decisions with which to contend. She pointed out so often patient empowerment strategies ended up leaving patients with responsibilities they could not shoulder and that the medical system should have met for them.

I agree that not every patient can take up this burden of promoting  both more patient involvement in research and data sharing, but groups of patients can. And when individual patients are willing to take on the sacrifice of insisting on these conditions for their consent, they should be recognized and supported by others. This is not a matter for patients with particular illnesses or members of patient organizations organized around a particular illness. Rather, this is a contribution to the well-being of society should be applauded and supported across the artificial boundaries drawn around particular conditions or race or class.

The mere possibility that patients are going to refuse to participate in research that does not have plans for patient involvement or data sharing can have a powerful effect. It is difficult enough for researchers to accrue sufficient numbers of patients for their studies. If the threat is that they will run into problems because they don’t adequately involve patients, they will be proactive in redesigning the research strategies and reflecting it in their consent forms, if they are serious about getting their research done.

just-say-noPatients are looking after the broader society in participating in medical research. However, if researchers do not take steps to ensure that society gets the greatest possible benefit, patients can just say no, we won’t consent to participation.

Acknowledgments: I benefited from discussions with numerous patients and some professionals in writing and revising this blog. Because some of the patients desired anonymity, I will simply give credit to the group. However, I am responsible for any excesses or inaccuracies that may have escaped their scrutiny.


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 ( and also ) 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,

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.


Uninterpretable: Fatal flaws in PACE Chronic Fatigue Syndrome follow-up study

Earlier decisions by the investigator group preclude valid long-term follow-up evaluation of CBT for chronic fatigue syndrome (CFS).

CFS-Think-of-the-worst1At the outset, let me say that I’m skeptical whether we can hold the PACE investigators responsible for the outrageous headlines that have been slapped on their follow-up study and on the comments they have made in interviews.

The Telegraph screamed

Chronic Fatigue Syndrome sufferers ‘can overcome symptoms of ME with positive thinking and exercise’

Oxford University has found ME is not actually a chronic illness

My own experience critiquing media interpretation of scientific studies suggests that neither researchers nor even journalists necessarily control shockingly inaccurate headlines placed on otherwise unexceptional media coverage. On the other hand, much distorted and exaggerated media coverage starts with statements made by researchers and by press releases from their institutions.

The one specific quote attributed to a PACE investigator is unfortunate because of its potential to be misinterpreted by professionals, persons who suffer from chronic fatigue syndrome, and the people around them affected by their functioning.

“It’s wrong to say people don’t want to get better, but they get locked into a pattern and their life constricts around what they can do. If you live within your limits that becomes a self-fulfilling prophesy.”

It suggests that willfulness causes CFS sufferers’ impaired functioning. This is ridiculous as application of the discredited concept of fighting spirit to cancer patients’ failure to triumph against their life altering and life-threatening condition. Let’s practice the principle of charity and assume this is not the intention of the PACE investigator, particularly when there is so much more for which we should give them responsibility.

Go here for a fuller evaluation that I endorse of the Telegraph coverage of PACE follow-up study.

Having read the PACE follow-up study carefully, my assessment is that the data presented are uninterpretable. We can temporarily suspend critical thinking and some basic rules for conducting randomized trials (RCTs), follow-up studies, and analyzing the subsequent data. Even if we do, we should reject some of the interpretations offered by the PACE investigators as unfairly spun to fit what has already a distorted positive interpretation oPACE trial HQf the results.

It is important to note that the PACE follow-up study can only be as good as the original data it’s based on. And in the case of the PACE study itself, a recent longread critique by UC Berkeley journalism and public health lecturer David Tuller has arguably exposed such indefensible flaws that any follow-up is essentially meaningless. See it for yourself [1, 2, 3 ].

This week’s report of the PACE long term follow-up study and a commentary  are available free at the Lancet Psychiatry website after a free registration. I encourage everyone to download a copy before reading further. Unfortunately, some crucial details of the article are highly technical and some details crucial to interpreting the results are not presented.

I will provide practical interpretations of the most crucial technical details so that they are more understandable to the nonspecialist. Let me know where I fail.

1When Cherished Beliefs Clash with EvidenceTo encourage proceeding with this longread, but to satisfy those who are unwilling or unable to proceed, I’ll reveal my main points are

  • The PACE investigators sacrificed any possibility of meaningful long-term follow-up by breaking protocol and issuing patient testimonials about CBT before accrual was even completed.
  • This already fatal flaw was compounded with a loose recommendation for treatment after the intervention phase of the trial ended. The investigators provide poor documentation of which treatment was taken up by which patients and whether there was crossover in the treatment being received during follow up.
  • Investigators’ attempts to correct methodological issues with statistical strategies lapses into voodoo statistics.
  • The primary outcome self-report variables are susceptible to manipulation, investigator preferences for particular treatments, peer pressure, and confounding with mental health variables.
  • The Pace investigators exploited ambiguities in the design and execution of their trial with self-congratulatory, confirmatory bias.

The Lancet Psychiatry summary/abstract of the article

Background. The PACE trial found that, when added to specialist medical care (SMC), cognitive behavioural therapy (CBT), or graded exercise therapy (GET) were superior to adaptive pacing therapy (APT) or SMC alone in improving fatigue and physical functioning in people with chronic fatigue syndrome 1 year after randomisation. In this pre-specified follow-up study, we aimed to assess additional treatments received after the trial and investigate long-term outcomes (at least 2 years after randomisation) within and between original treatment groups in those originally included in the PACE trial.

Findings Between May 8, 2008, and April 26, 2011, 481 (75%) participants from the PACE trial returned questionnaires. Median time from randomisation to return of long-term follow-up assessment was 31 months (IQR 30–32; range 24–53). 210 (44%) participants received additional treatment (mostly CBT or GET) after the trial; with participants originally assigned to SMC alone (73 [63%] of 115) or APT (60 [50%] of 119) more likely to seek treatment than those originally assigned to GET (41 [32%] of 127) or CBT (36 [31%] of 118; p<0·0001). Improvements in fatigue and physical functioning reported by participants originally assigned to CBT and GET were maintained (within-group comparison of fatigue and physical functioning, respectively, at long-term follow-up as compared with 1 year: CBT –2·2 [95% CI –3·7 to –0·6], 3·3 [0·02 to 6·7]; GET –1·3 [–2·7 to 0·1], 0·5 [–2·7 to 3·6]). Participants allocated to APT and to SMC alone in the trial improved over the follow-up period compared with 1 year (fatigue and physical functioning, respectively: APT –3·0 [–4·4 to –1·6], 8·5 [4·5 to 12·5]; SMC –3·9 [–5·3 to –2·6], 7·1 [4·0 to 10·3]). There was little evidence of differences in outcomes between the randomised treatment groups at long-term follow-up.

Interpretation The beneficial effects of CBT and GET seen at 1 year were maintained at long-term follow-up a median of 2·5 years after randomisation. Outcomes with SMC alone or APT improved from the 1 year outcome and were similar to CBT and GET at long-term follow-up, but these data should be interpreted in the context of additional therapies having being given according to physician choice and patient preference after the 1 year trial final assessment. Future research should identify predictors of response to CBT and GET and also develop better treatments for those who respond to neither.

fem imageNote the contradiction here which will persist throughout the paper, the official Oxford University press release, quotes from the PACE investigators to the media, and media coverage. On the one hand we are told:

Improvements in fatigue and physical functioning reported by participants originally assigned to CBT and GET were maintained…

Yet we are also told:

There was little evidence of differences in outcomes between the randomised treatment groups at long-term follow-up.

Which statement is to be given precedence? To the extent that features of a randomized trial have been preserved in the follow-up (which we will see, is not actually the case), a lack of between group differences at follow-up should be given precedence over any persistence of change within groups from baseline. That is a not controversial point for interpreting clinical trials.

A statement about group differences at follow up should proceed and qualify any statement about within-group follow up. Otherwise why bother with a RCT in the first place?

The statement in the Interpretation section of the summary/abstract has an unsubstantiated spin in favor of the investigators’ preferred intervention.

Outcomes with SMC alone or APT improved from the 1 year outcome and were similar to CBT and GET at long-term follow-up, but these data should be interpreted in the context of additional therapies having being given according to physician choice and patient preference after the 1 year trial final assessment.

If we’re going to be cautious and qualified in our statements, there are lots of other explanations for similar outcomes in the intervention and control groups that are more plausible. Simply put and without unsubstantiated assumptions, any group differences observed earlier have dissipated. Poof! Any advantages of CBT and GET are not sustained.

How the PACE investigators destroyed the possibility of an interpretable follow-up study

imagesNeither the Lancet Psychiatry article nor any recent statements by the PACE investigators acknowledged how these investigators destroyed any possibility of analyses of meaningful follow-up data.

Before the intervention phase of the trial was even completed, even before accrual of patients was complete, the investigators published a newsletter in December 2008 directed at trial participants. An article appropriately reminds participants of the upcoming two and one half year follow-up. But then it acknowledges difficulty accruing patients, but that additional funding has been received from the MRC to extend recruiting. And then glowing testimonials appear on p. 3 of the newsletter about the effects of their intervention.

“Being included in this trial has helped me tremendously. (The treatment) is now a way of life for me, I can’t imagine functioning fully without it. I have nothing but praise and thanks for everyone involved in this trial.”

“I really enjoyed being a part of the PACE Trial. It helped me to learn more about myself, especially (treatment), and control factors in my life that were damaging. It is difficult for me to gauge just how effective the treatment was because 2007 was a particularly strained, strange and difficult year for me but I feel I survived and that the trial armed me with the necessary aids to get me through. It was also hugely beneficial being part of something where people understand the symptoms and illness and I really enjoyed this aspect.”

These testimonials are a horrible breach of protocol. Taken together with the acknowledgment of the difficulty accruing patients, the testimonials solicit expression of gratitude and apply pressure on participants to endorse the trial by providing a positive of their outcome. Some minimal effort is made to disguise the conditions from which the testimonials come. However, references to a therapist and, in the final quote above, to “control factors in my life that were damaging” leave no doubt that the CBT and GET favored by the investigators is having positive results.

Probably more than in most chronic illnesses, CFS sufferers turn to each other for support in the face of bewildering and often stigmatizing responses from the medical community. These testimonials represent a form of peer pressure for positive evaluations of the trial.

Any investigator group that would deliberately violate protocol in this manner deserves further scrutiny for other violations and threats to the validity of their results. I challenge defenders of the PACE study to cite other precedents for this kind of manipulation of clinical trials participants. What would they have thought if a drug company had done this for the evaluation of their medication?

The breakdown of randomization as further destruction of the interpretability of follow-up results

Returning to the Lancet Psychiatry article itself, note the following:

After completing their final trial outcome assessment, trial participants were offered an additional PACE therapy if they were still unwell, they wanted more treatment, and their PACE trial doctor agreed this was appropriate. The choice of treatment offered (APT, CBT, or GET) was made by the patient’s doctor, taking into account both the patient’s preference and their own opinion of which would be most beneficial. These choices were made with knowledge of the individual patient’s treatment allocation and outcome, but before the overall trial findings were known. Interventions were based on the trial manuals, but could be adapted to the patient’s needs.

Readers who are methodologically inclined might be interested in a paper in which I discuss incorporating patient preference in randomized trials, as well as another paper describing clinical trial conducted with German colleagues  in which we incorporated patient preference in evaluation of antidepressants and psychotherapy for depression in primary care. Patient preference can certainly be accommodated in a clinical trial in ways that preserve the benefits of randomization, but not as the PACE investigators have done.

Following completion of the treatment to which particular patients were randomly assigned, the PACE trial offered a complex negotiation between patient and trial physician about further treatment. This represents a thorough breakdown of the benefits of a controlled randomized trial for the evaluation of treatments. Any focus on the long-term effects of initial randomization is sacrificed by what could be substantial departures from that randomization. Any attempts at statistical corrections will fail.

Of course, investigators cannot ethically prevent research participants from seeking additional treatment. But in the case of PACE, the investigators encouraged departures from the randomized treatment yet did not adequately take into account the decisions that were made. An alternative would have been to continue with the randomized treatment, taking into account and quantifying any cross over into another treatment arm.

2When Cherished Beliefs Clash with EvidenceVoodoo statistics in dealing with incomplete follow-up data.

Between May 8, 2008, and April 26, 2011, 481 (75%) participants from the PACE trial returned questionnaires.

This is a very good rate of retention of participants for follow-up. The serious problem is that neither

  • loss to follow-up nor
  • whether there was further treatment, nor
  • whether there was cross over in the treatment received in follow-up versus the actual trial

is random.

Furthermore, any follow-up data is biased by the exhortation of the newsletter.

No statistical controls can restore the quality of the follow-up data to what would’ve been obtained with preservation of the initial randomization. Nothing can correct for the exhortation.

Nonetheless, the investigators tried to correct for loss of participants to follow-up and subsequent treatment. They described their effort in a technically complex passage, which I will subsequently interpret:

We assessed the differences in the measured outcomes between the original randomised treatment groups with linear mixed-effects regression models with the 12, 24, and 52 week, and long-term follow-up measures of outcomes as dependent variables and random intercepts and slopes over time to account for repeated measures.

We included the following covariates in the models: treatment group, trial stratification variables (trial centre and whether participants met the international chronic fatigue syndrome criteria,3 London myalgic encephalomyelitis criteria,4 and DSM IV depressive disorder criteria),18,19 time from original trial randomisation, time by treatment group interaction term, long-term follow-up data by treatment group interaction term, baseline values of the outcome, and missing data predictors (sex, education level, body-mass index, and patient self-help organisation membership), so the differences between groups obtained were adjusted for these variables.

Nearly half (44%; 210 of 479) of all the follow-up study participants reported receiving additional trial treatments after their final 1 year outcome assessment (table 2; appendix p 2). The number of participants who received additional therapy differed between the original treatment groups, with more participants who were originally assigned to SMC alone (73 [63%] of 115) or to APT (60 [50%] of 119) receiving additional therapy than those assigned to GET (41 [32%] of 127) or CBT (36 [31%] of 118; p<0·0001).

In the trial analysis plan we defined an adequate number of therapy sessions as ten of a maximum possible of 15. Although many participants in the follow-up study had received additional treatment, few reported receiving this amount (table 2). Most of the additional treatment that was delivered to this level was either CBT or GET.

The “linear mixed-effects regression models” are rather standard techniques for compensating for missing data by using all of the available data to estimate what is missing. The problem is that this approach assumes that any missing data are random, which is an untested assumption that is unlikely to be true in this study.

3aWhen Cherished Beliefs Clash with Evidence-page-0The inclusion of “covariates” is an effort to control for possible threats to the validity of the overall analyses by taking into account what is known about participants. There are numerous problems here. We can’t be assured that the results are any more robust and reliable than what would be obtained without these efforts at statistical control. The best publishing practice is to make the unadjusted outcome variables available and let readers decide. Greatest confidence in results is obtained when there is no difference between the results in the adjusted and unadjusted analyses.

Methodologically inclined readers should consult an excellent recent article by clinical trial expert, Helene Kraemer, A Source of False Findings in Published Research Studies Adjusting for Covariates.

The effectiveness of statistical controls depends on certain assumptions being met about patterns of variation within the control variables. There is no indication that any diagnostic analyses were done to determine whether possible candidate control variables should be eliminated in order to avoid a violation of assumptions about the multivariate distribution of covariates. With so many control variables, spurious results are likely. Apparent results could change radically with the arbitrary addition or subtraction of control variables. See here for a further explanation of this problem.

We don’t even know how this set of covariate/control variables, rather than some other set, was established. Notoriously, investigators often try out various combinations of control variables and present only those that make their trial looked best. Readers are protected from this questionable research practice only with pre-specification of analyses before investigators know their results—and in an unblinded trial, researchers often know the result trends long before they see the actual numbers.

See JP Simmons’  hilarious demonstration that briefly listening to the Beatles’ “When I’m 64” can be leave research participants a year and a half older younger than listening to “Kalimba” – at least when investigators have free reign to manipulate the results they want in an study without pre-registration of analytic plans.

Finally, the efficacy of complex statistical controls is widely overestimated and depends on unrealistic assumptions. First, it is assumed that all relevant variables that need to be controlled have been identified. Second, even when this unrealistic assumption has been met, it is assumed that all statistical control variables have been measured without error. When that is not the case, results can appear significant when they actually are not. See a classic paper by Andrew Phillips and George Davey Smith for further explanation of the problem of measurement error producing spurious findings.

What the investigators claim the study shows

In an intact clinical trial, investigators can analyze outcome data with and without adjustments and readers can decide which to emphasize. However, this is far from an intact clinical trial and these results are not interpretable.

The investigators nonetheless make the following claims in addition to what was said in the summary/abstract.

In the results the investigators state

The improvements in fatigue and physical functioning reported by participants allocated to CBT or GET at their 1 year trial outcome assessment were sustained.

This was followed by

The improvements in impairment in daily activities and in perceived change in overall health seen at 1 year with these treatments were also sustained for those who received GET and CBT (appendix p 4). Participants originally allocated to APT reported further improvements in fatigue, physical functioning, and impairment in daily activities from the 1 year trial outcome assessment to long-term follow-up, as did those allocated to SMC alone (who also reported further improvements in perceived change in overall health; figure 2; table 3; appendix p 4).

If the investigators are taking their RCT design seriously, they should give precedence to the null findings for group differences at follow-up. They should not be emphasizing the sustaining of benefits within the GET and CBT groups.

The investigators increase their positive spin on the trial in the opening sentence of the Discussion

The main finding of this long-term follow-up study of the PACE trial participants is that the beneficial effects of the rehabilitative CBT and GET therapies on fatigue and physical functioning observed at the final 1 year outcome of the trial were maintained at long-term follow-up 2·5 years from randomisation.

This is incorrect. The main finding   is that any reported advantages of CBT and GET at the end of the trial were lost by long-term follow up. Because an RCT is designed to focus on between group differences, the statement about sustaining of benefits is post-hoc.

The Discussion further states

In so far as the need to seek additional treatment is a marker of continuing illness, these findings support the superiority of CBT and GET as treatments for chronic fatigue syndrome.

This makes unwarranted and self-serving assumptions that treatment choice was mainly driven by the need for further treatment, when decision-making was contaminated by investigative preference, as stated in the newsletter. Note also that CBT is a novel treatment for research participants and more likely to be chosen on the basis of novelty alone in the face of overall modest improvement rates for the trial and lack of improvements in objective measures. Whether or not the investigators designate a limited range of self-report measures as primary, participant decision-making may be driven by other, more objective measures.

Regardless, investigators have yet to present any data concerning how decisions for further treatment were made, if such data exist.

The investigators further congratulate themselves with

There was some evidence from an exploratory analysis that improvement after the 1 year trial final outcome was not associated with receipt of additional treatment with CBT or GET, given according to need. However this finding must be interpreted with caution because it was a post-hoc subgroup analysis that does not allow the separation of patient and treatment factors that random allocation provides.

However, why is this analysis singled out has exploratory and to be interpreted with caution because it is a post-hoc subgroup analysis when similarly post-hoc subgroup analyses are recommended without such caution?

The investigators finally get around to depicting what should be their primary finding, but do so in a dismissive fashion.

Between the original groups, few differences in outcomes were seen at long-term follow-up. This convergence in outcomes reflects the observed improvement in those originally allocated to SMC and APT, the possible reasons for which are listed above.

The discussion then discloses a limitation of the study that should have informed earlier presentation and discussion of results

First, participant response was incomplete; some outcome data were missing. If these data were not missing at random it could have led to either overestimates or underestimates of the actual differences between the groups.

This minimizes the implausibility of the assumption of random missing variables, as well as the problems introduced by the complex attempts to control confounds statistically.

And then there is an unsubstantiated statement that is sure to upset persons who suffer from CFS and those who care for them.

the outcomes were all self-rated, although these are arguably the most pertinent measures in a condition that is defined by symptoms.

I could double the length of this already lengthy blog post if I fully discussed this. But let me raise a few issues.

  1. The self-report measures do not necessarily capture subjective experience, only forced choice responses to a limited set of statements.
  2. One of the two outcome measures, the physical health scale of the SF-36  requires forced choice responses to a limited set of statements selected for general utility across all mental and physical conditions. Despite its wide use, the SF-36 suffers from problems in internal consistency and confounding with mental health variables. Anyone inclined to get excited about it should examine  its items and response options closely. Ask yourself, do differences in scores reliably capture clinically and personally significant changes in the experience and functioning associated with the full range of symptoms of CHF?
  3. The validity other primary outcome measure, the Chalder Fatigue Scale depends heavily on research conducted by this investigator group and has inadequate validation of its sensitivity to change in objective measures of functioning.
  4. Such self-report measures are inexorably confounded with morale and nonspecific mental health symptoms with large, unwanted correlation tendency to endorse negative self-statements that is not necessarily correlated with objective measures.

Although it was a long time ago, I recall well my first meeting with Professor Simon Wessely. It was at a closed retreat sponsored by NIH to develop a consensus about the assessment of fatigue by self-report questionnaire. I listened to a lot of nonsense that was not well thought out. Then, I presented slides demonstrating a history of failed attempts to distinguish somatic complaints from mental health symptoms by self-report. Much later, this would become my “Stalking bears, finding bear scat in the woods” slide show.

you can't see itBut then Professor Wessely arrived at the meeting late, claiming to be grumbly because of jet lag and flight delays. Without slides and with devastating humor, he upstaged me in completing the demolition of any illusions that we could create more refined self-report measures of fatigue.

I wonder what he would say now.

But alas, people who suffer from CFS have to contend with a lot more than fatigue. Just ask them.

borg max[To be continued later if there is interest in my doing so. If there is, I will discuss the disappearance of objective measures of functioning from the PACE study and you will find out why you should find some 3-D glasses if you are going to search for reports of these outcomes.]