Amazingly spun mindfulness trial in British Journal of Psychiatry: How to publish a null trial

mindfulness chocolateSince when is “mindfulness therapy is not inferior to routine primary care” newsworthy?

 

Spinning makes null results a virtue to be celebrated…and publishable.

An article reporting a RCT of group mindfulness therapy

Sundquist, J., Lilja, Å., Palmér, K., Memon, A. A., Wang, X., Johansson, L. M., & Sundquist, K. (2014). Mindfulness group therapy in primary care patients with depression, anxiety and stress and adjustment disorders: randomised controlled trial. The British Journal of Psychiatry.

was previously reviewed in Mental Elf. You might want to consider their briefer evaluation before beginning mine. I am going to be critical not only of the article, but the review process that got it into British Journal of Psychiatry (BJP).

I am an Academic Editor of PLOS One,* where we have the laudable goal of publishing all papers that are transparently reported and not technically flawed. Beyond that, we leave decisions about scientific quality to post-publication commentary of the many, not a couple of reviewers whom the editor has handpicked. Yet, speaking for myself, and not PLOS One, I would have required substantial revisions or rejected the version of this paper that got into the presumably highly selective, even vanity journal BJP**.

The article is paywalled, but you can get a look at the abstract here  and write to the corresponding author for a PDF at Jan.sundquist@med.lu.se

As always, examine the abstract carefully  when you suspect spin, but expect that you will not fully appreciate the extent of spin until you have digested the whole paper. This abstract declares

Mindfulness-based group therapy was non-inferior to treatment as usual for patients with depressive, anxiety or stress and adjustment disorders.

“Non-inferior” meaning ‘no worse than routine care?’ How could that null result be important enough to get into a journal presumably having a strong confirmation bias? The logic sounds just like US Senator George Aiken famously proposing getting America out of the war it was losing in Vietnam by declaring America had won and going home.

There are hints of other things going on, like no reporting of how many patients were retained for analysis or whether there were intention-to-treat analyses. And then the weird mention of outcomes being analyzed with “ordinal mixed models.”  Have you ever seen that before? And finally, do the results hold for patients with any of those disorders or only a particular sample of unknown mix and maybe only representing those who could be recruited from specific settings? Stay tuned…

What is a non-inferiority trial and when should one conduct one?

An NHS website explains

The objective of non-inferiority trials is to compare a novel treatment to an active treatment with a view of demonstrating that it is not clinically worse with regards to a specified endpoint. It is assumed that the comparator treatment has been established to have a significant clinical effect (against placebo). These trials are frequently used in situations where use of a superiority trial against a placebo control may be considered unethical.

Noninferiority trials (NIs) have a bad reputation. Consistent with a large literature, a recent systematic review of NI HIV trials  found the overall methodological quality to be poor, with a high risk of bias. The people who brought you CONSORT saw fit to develop special reporting standards for NIs  so that misuse of the design in the service of getting publishable results is more readily detected. You might want to download the CONSORT checklist for NI and apply the checklist to the trial under discussion. Right away, you can see how deficient the the reporting is in the abstract of the paper under discussion.

Basically, an NI RCT commits investigators and readers to accepting null results as support for a new treatment because it is no worse than an existing one. Suspicions are immediately raised as to why investigators might want to make that point.

Conflicts of interest could be a reason. Demonstration that the treatment is as good as existing treatments might warrant marketing of the new treatment or dissemination into existing markets. There could be financial rewards or simply promoters and enthusiasts favoring what they would find interesting. Yup, some bandwagons, some fads and fashions psychotherapy are in large part due to promoters simply seeking the new and different, without evidence that a treatment is better than existing ones.

Suspicions are reduced when the new treatment has other advantages, like greater acceptability or a lack of side effects, or when the existing treatments are so good that an RCT of the new treatment with a placebo-control condition would be unethical.

We should give evaluate whether there is an adequate rationale for authors doing an NI RCT, rather than them relying on the conventional test whether the null hypothesis can be rejected of no differences between the intervention and a control condition. Suitable support would be a strong record of efficacy for a well defined control condition. It would also help if the trial were pre-registered as NI, quieting concerns that it was declared as such after peeking at the data.

net-smart-mindfulnessThe first things I noticed in the methods section…trouble

  • The recruitment procedure is strangely described, but seems to indicate that the therapist providing mindfulness training were present during recruitment and probably weren’t blinded to group assignment and conceivably could influence it. The study thus does not have clear evidence of an appropriate randomization procedure and initial blinding. Furthermore, the GPs administering concurrent treatment also were not blinded and might take group assignment into account in subsequent prescribing and monitoring of medication.
  • During the recruitment procedure, GPs assessed whether medication was needed and made prescriptions before randomization occurred. We will need to see – we are not told in the methods section – but I suspect a lot of medication is being given to both intervention and control patients. That is going to complicate interpretation of results.
  • In terms of diagnosis, a truly mixed group of patients was recruited. Patients experiencing stress or adjustment reactions were thrown in with patients who had mild or moderate depression or anxiety disorders. Patients were excluded who were considered severe enough to need psychiatric care.
  • Patients receiving any psychotherapy at the start of the trial were excluded, but the authors ignored whether patients were receiving medication.

This appears to be a mildly distressed sample that is likely to show some recovery in the absence of any treatment. The authors’ not controlling for the medication was received is going to be a big problem later. Readers won’t be able to tell whether any improvement in the intervention condition is due to its more intensive support and encouragement that results in better adherence to medication.

  • The authors go overboard in defending their use of multiple overlapping
    Play at https://www.google.co.uk/url?sa=t&rct=j&q=&esrc=s&source=web&cd=3&cad=rja&uact=8&ved=0CC4QFjAC&url=https%3A%2F%2Fmyspace.com%2Fkevncoyne%2Fmusic%2Fsong%2Felvis-is-dead-86812363-96247308&ei=GvYYVbegOKTf7AaRzIHoCg&usg=AFQjCNHM4EKRwFYkepeT-yROFk4LOtfhCA&bvm=bv.89381419,d.ZGU

    Play Elvis is Dead at athttp://tinyurl.com/p78pzcn

    measures and overboard in praising the validity of their measures. For instance, The Hospital Anxiety and Depression Scale (HADS) is a fatally flawed instrument, even if still widely used. I considered the instrument dead in terms of reliability and validity, but like Elvis, it is still being cited.

Okay, the authors claim these measures are great, and attach clinical importance to cut points that others no longer consider valid. But then, why do they decide that the scales are ordinal, not interval? Basically, they are saying the scales are so bad that the differences between one number to the next higher or lower for pairs of items can’t be considered equal. This is getting weird. If the scales are as good as the authors claim, why do the authors take the unusual step of considering them as psychometrically inadequate?

I know, I’m getting technical to the point that I risk losing some readers, but the authorsspin no are setting readers up to be comfortable with a decision to focus on medians, not mean scores – making it more difficult to detect any differences between the mindfulness therapy and routine care. Spin, spin!

There are lots of problems with the ill described control condition, treatment as usual (TAU). My standing gripe with this choice is  that TAU varies greatly across settings, and often is so inadequate that at best the authors are comparing whether mindfulness therapy is better than some unknown mix of no treatment and inadequate treatment.

We know enough about mindfulness therapy at this point to not worry about whether it is better than nothing at all, but should be focusing on whether is better than another active treatment and whether its effectiveness is due to particular factors. The authors state that most of the control patients were receiving CBT, but don’t indicate how they knew that, except for case records. Notoriously, a lot of the therapy done in primary care that is labeled by practitioners as CBT does not pass muster. I would be much more comfortable with some sort of control over what patients were receiving in the control arm, or at least better specification.

Analyses

I’m again trying to avoid getting very technical here, but point out for those who have a developed interest in statistics, that there were strange things going on.

  • Particular statistical analyses (depending on group medians, rather than means are chosen that are less likely to reveal differences between intervention and control group than the parametric statistics that are typically done.
  • Complicated decisions justify throwing away data and then using multivariate techniques to estimate what the data were. The multivariate techniques require assumptions that are not tested.
  • The power analysis is not conducted to detect differences between groups, but to be able to provide a basis for saying that mindfulness does not differ from routine care. Were the authors really interested in that question rather than whether mindfulness is better than routine care in initially designing a study and its analytic plan? Without pre-registration, we cannot know.

Results

There are extraordinary revelations in table 1, baseline characteristics.

Please click to enlarge

Please click to enlarge

  • The intervention and control group initially differed for two of the four outcome variables before they even received the intervention. Thus, intervention and control conditions are not comparable in important baseline characteristics. This is in itself a risk of bias, but also raises further questions about the adequacy of the randomization procedure and blinding.
  • We are told nothing about the distribution of diagnoses across the intervention and control group, which is very important in interpreting results and considering what generalizations can be made.
  • Most patients in both the intervention and control groups were receiving antidepressants and about a third of them either condition were receiving a “tranquilizer” or have missing data for that variable.

Signals that there is something amiss in this study are growing stronger. Given the mildness of disturbance and high rates of prescription of medication, we are likely dealing with a primary care sample where medications are casually distributed and poorly monitored. Yet, this study is supposedly designed to inform us whether adding mindfulness to this confused picture produces outcomes that are not worse.

Table 5 adds to the suspicions. There were comparable, significant changes in both the intervention and control condition over time. But we can’t know if that was due to the mildness of distress or effectiveness of both treatments.

table 5

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Twice as many patients assigned to mindfulness dropped out of treatment, compared to those assigned to routine care. Readers are given some information about how many sessions of mindfulness patients attended, but not the extent to which they practiced mindfulness.

positive spin 2Discussion

We are told

The main finding of the present RCT is that mindfulness group therapy given in a general practice setting, where a majority of patients with depression, anxiety, and stress and adjustment disorders are treated, is non-inferior to individual-based therapy, including CBT. To the best of our knowledge, this is the first RCT performed in a general practice setting where the effect of mindfulness group therapy was compared with an active control group.

Although a growing body of research has examined the effect of mindfulness on somatic as well as psychiatric conditions, scientific knowledge from RCT studies is scarce. For example, a 2007 review…

It’s debatable whether the statement was true in 2007, but a lot has happened since then. Recent reviews suggest that mindfulness therapy is better than nothing and better than inactive control conditions that do not provide comparable levels of positive expectations and support. Studies are accumulating that indicate mindfulness therapy is not consistently better than active control conditions. Differences become less likely when the alternative treatments are equivalent in positive expectations conveyed to patients and providers, support, and intensity in terms of frequency and amount of contact. Resolving this latter question of whether mindfulness is better than reasonable alternatives is now critical in this study provides no relevant data.

An Implications section states

Patients who receive antidepressants have a reported remission rate of only 35–40%.41 Additional treatment is therefore needed for non-responders as well as for those who are either unable or unwilling to engage in traditional psychotherapy.

The authors are being misleading to the point of being irresponsible in making this statement in the context of discussing the implications of their study. The reference is to the American STAR*D treatment study, which dealt with very different, more chronically and unremittingly depressed population.

An appropriately referenced statement about primary care populations like what this study was recruited would point to the lack of diagnosis on which prescription of medicaton was based, unnecessary treatment with medication of patients who would not be expected to benefit from it, and poor monitoring and follow-up of patients who could conceivably benefit from medication if appropriately minutes. The statement would reflect the poor state of routine care for depression in the community, but would undermine claims that the control group received an active treatment with suitable specification that would allow any generalizations about the efficacy of mindfulness.

MY ASSESSMENT

This RCT has numerous flaws in its conduct and reporting that preclude making any contribution to the current literature about mindfulness therapy. What is extraordinary is that, as a null trial, it got published in BJP. Maybe its publication in its present form represents incompetent reviewing and editing, or maybe a strategic, but inept decision to publish a flawed study with null findings because it concerns the trendy topic of mindfulness and GPs to whom British psychiatrists want to reach out.

An RCT of mindfulness psychotherapy is attention-getting. Maybe the BJP is willing to sacrifice trustworthiness of the interpretation of results for newsworthiness. BJP will attract readership it does not ordinarily get with publication of this paper.

What is most fascinating is that the study was framed as a noninferiority trial and therefore null results are to be celebrated. I challenge anyone to find similar instances of null results for a psychotherapy trial being published in BJP except in the circumstances that make a lack of effect newsworthy because it suggests that investment in the dissemination of a previously promising treatment is not justified. I have a strong suspicion that this particular paper got published because the results were dressed up as a successful demonstration of noninferiority.

I would love to see the reviews this paper received, almost as much as any record of what the authors intended when they planned the study.

Will this be the beginning of a trend? Does BJP want to encourage submission of noninferiority psychotherapy studies? Maybe the simple explanation is that the editor and reviewers do not understand what a noninferiority trial is and what it can conceivably conclude.

Please, some psychotherapy researcher with a null trial sitting in the drawer, test the waters by dressing the study up as a noninferior trial and submitted to BJP.

How bad is this study?

The article provides a non-intention-to-treat analysis of a comparison of mindfulness to an ill specified control condition that would not qualify as an active condition. The comparison does not allow generalization to other treatments in other settings. The intervention and control conditions had significant differences in key characteristics at baseline. The patient population is ill-described in ways that does not allow generalization to other patient populations. The high rates of co-treatment confounding due to antidepressants and tranquilizers precludes determination of any effects of the mindfulness therapy. We don’t know if there were any effects, or if both the mindfulness therapy and control condition benefited from the natural decline in distress of a patient population largely without psychiatric diagnoses. Without a control group like a waiting list, we can’t tell if these patients would have improved any way. I could go on but…

This study was not needed and may be unethical

lipstickpigThe accumulation of literature is such that we need less mindfulness therapy research, not more. We need comparisons with well specified active control groups that can answer the question of whether mindfulness therapy offers any advantage over alternative treatments, not only in efficacy, but in the ability to retain patients so they get an adequate exposure to the treatment. We need mindfulness studies with cleverly chosen comparison conditions that allow determination of whether it is the mindfulness component of mindfulness group therapy that has any effectiveness, rather than relaxation that mindfulness therapy shares with other treatments.

To conduct research in patient populations, investigators must have hypotheses and methods with the likelihood of making a meaningful contribution to the literature commensurate with all the extra time and effort they are asking of patients. This particular study fails this ethical test.

Finally, the publication of this null trial as a noninferiority trial pushes the envelope in terms of the need for preregistration of design and analytic plans for trials. If authors of going to claim a successful demonstration of non-inferiority, we need to know that is what they set out to do, rather than just being stuck with null findings they could not otherwise publish.

*DISCLAIMER: This blog post presents solely the opinions of the author, and not necessarily PLOS. Opinions about the publishability of papers reflect only the author’s views and not necessarily an editorial decision for a manuscript submitted to PLOS One.

**I previously criticized the editorial process at BJP, calling for the retraction of a horribly flawed meta-analysis of the mental health effects of abortion written by an American antiabortion activist. I have pointed out how another flawed review of the efficacy of long-term psychodynamic psychotherapy represented duplicate publication . But both of these papers were published under the last editor. I still hope that the current editor can improve the trustworthiness of what is published at BJP. I am not encouraged by this particular paper, however.

Category: antidepressants, depression, mental health care, mindfulness, primary care, psychotherapy, Publication bias | Tagged , , , , , | Leave a comment

Repost: Claire Underwood From Netflix’s House of Cards: Narcissistic Personality Disorder?

Last month, Netflix released Season 3 of House of Cards. In light of this, I am reposting a blog I wrote about the second season of the series last year: “Claire Underwood From Netflix’s House of Cards: Narcissistic Personality Disorder?”

 

Last month I used the character of Frank Underwood as a “case study” to illustrate the misunderstood psychiatric diagnosis of Antisocial Personality Disorder, and many of you asked: Well, what about his wife, Claire?

Good question!  You asked, and so today I will do my best to  answer.

 

SPOILER ALERT: For those of you who have not yet watched all of Season 2 yet, consider yourself warned. 

 

Image: Netflix

Image: Netflix

Clinical lore would certainly support that Claire, herself, must have a personality disorder of some kind – a sort of fatal attraction, where a couple is drawn to each other because there is something in their personality patterns which is complementary and reciprocal.

She does appear to have mastered the art of turning a blind eye to Frank’s more antisocial exploits.  She is a highly intelligent woman, and she must have some inkling that her husband may be involved in the death of Zoe Barnes and Peter Russo.  But if she has an inkling, she does not show it.

Claire, from what we know, does not engage in outright antisocial behavior.  Unlike Frank, she has not murdered anyone and we have not seen her engage in very reckless or impulsive outbursts.

However, she rarely shows emotion—her smiles seem fake, her laugh empty, and her expressions are bland.  She is more restrained and guarded than Frank, and she does not reveal her inner thoughts to the viewer the way Frank does so it is much harder to know what could be going on in her mind.

Still, I think I have seen enough to venture forth with an assertion that she may have a Narcissistic Personality Disorder.

 

What is Narcissistic Personality Disorder?

 

A pervasive pattern of grandiosity, need for admiration, and lack of empathy beginning by early adulthood and present in a variety of contexts, as indicated by five (or more) of 9 criteria.

 

Below are the five criteria that I think apply to Claire:

 

1) Has a sense of entitlement (i.e. unreasonable expectations of especially favorable treatment or automatic compliance with his or her expectations)

 

Image: Netflix

Image: Netflix

She expected Galloway to take the blame for the photos that were leaked and eventually claim it was all a “publicity stunt,” thus ruining his own reputation and image.  She expressed no regret that her ex-lover was cornered into having to do this, on her behalf, and no remorse that it almost ruined his life and his relationship with his fiancé. She was entitled to this act because she is “special” and expects that people will “fall on their swords” for her.

 

2) Is interpersonally exploitative (i.e. takes advantage of others to achieve his or her own ends)

 

Claire manipulates the first lady, Tricia Walker, into believing Christina (a White House aide) is interested in the president. She pretends to be a friend, wangles her way into becoming the first lady’s confidant, and persuades her to enter couples therapy with the president.  All of this is actually part of an elaborate plan to help Frank take the President down so that he can become president and she (Claire) can usurp Tricia as first lady.

Another example: Claire is pressured by the media into revealing that she once had an abortion, but she lies and states that the unborn child was a result of rape (presumably to save political face).  Again, she shows no remorse about her lie and instead profits from it, gaining much sympathy and public support.

 

3) Lacks empathy: is unwilling to recognize or identify with the feelings and needs of others

 

Image: Netflix

Image: Netflix

This was best seen in the way Claire deals with her former employee Gillian Cole’s threat of a lawsuit –  she pulls a few strings and threatens the life of Gillian’s unborn baby.  In fact, in addition to the obvious lack of empathy was the simmering rage she had toward Gillian for daring to cross her.  Again, entitlement, narcissistic rage, and a lack of empathy would explain that evil threat she made, to Gillian’s face, about the baby.

 

4) Is often envious of others or believes that others are envious of him or her

 

I think part of the reason Claire was so angry at Gillian was because, deep down, she was envious of her pregnancy.  We know that, in parallel, Claire is consulting a doctor about becoming pregnant and is told that her chances are slim.  This is such a narcissistic injury to Claire that she directs her rage at Gillian.  I don’t think she was even consciously aware of how envious she is of Gillian for being pregnant.

Another example would be the look on her face when Galloway indicates he is madly in love with his fiancé and wishes to make a life with her.  For a second her face darkens – a flash of jealous rage – which then translates to indifference and almost pleasure at his eventual public humiliation.

 

5) Shows arrogant, haughty behaviors or attitudes 

 

Image: Netflix

Image: Netflix

Correct me if I am wrong, but Claire just does not appear to be that warm or genuine and has an almost untouchable air about her. Furthermore, we only ever see her with people who work for her (i.e. have less power than her) or with people more powerful than her (i.e. whose power she wants for herself). Other than Frank, where are her equals? Her oldest friends and colleagues? Her family? People who might not be influenced by her title or power?

 

One last comment – in Season 2 Claire certainly comes across as more ruthless and power hungry than the Claire in Season 1—whether she is now showing her true colors and is dropping her facade or just becoming more lost in Frank’s world and hence looking more like him is unclear to me…

 

I suppose we will find out in Season 3!

 

Category: Commentary, Psychiatry, Uncategorized | Tagged , , , , , | Leave a comment

BMC Medicine gets caught up in Triple P Parenting promoters’ war on critics and null findings

Undeclared conflicts of interest constitute scientific misconduct.

Why we should be as concerned about conflicts of interest in evaluations of nonpharmacological treatments, like psychotherapy.

whackWhack! Triple P promoters (3P) Cassandra L Tellegen and Kate Sofronoff struck again against critics and null findings, this time in BMC Medicine. As usual, there was an undisclosed financial conflict of interest.

Until recently, promoters of the multimillion-dollar enterpriseNothing_to_Declare controlled perception of their brand of treatment. They authored most reports of implementations and also systematic reviews and meta-analyses. They did not report financial conflicts of interest and denied any conflict when explicitly queried.

The promoters were able to insist on the official website:

No other parenting program in the world has an evidence base as extensive as that of Triple P. It is number one on the United Nations’ ranking of parenting programs, based on the extent of its evidence base.

At least two of the developers of 3P and others making money from it published a systematic review and meta-analysis they billed as comprehensive:

Sanders, M. R., Kirby, J. N., Tellegen, C. L., & Day, J. J. (2014). The Triple P-Positive Parenting Program: A systematic review and meta-analysis of a multi-level system of parenting support. Clinical Psychology Review, 34(4), 337-357.

Promoters of 3P are still making extravagant claims, but there has been noticeable change in the view from elsewhere. An independently conducted meta-analyses in BMC Medicine  demonstrated that previous evaluations depended heavily on flawed, mostly small studies that very often had undeclared conflicts of interest. I echoed and amplified the critique of the 3P Parenting literature, first in blog posts [1 , 2]  and then in an invited commentary in BMC Medicine.

The sordid history of the promoters’ “comprehensive” meta-analysis was revealed  and its overwhelming flaws were scrutinized.

Over 30 errata, addenda, and  corrigenda have been attached to previously published 3P articles and more keep accumulating. Just try Google scholar with “triple P parenting” and “erratum” or “addendum” or “corrigendum.” We will be seeing more errata as more editors are contacted.

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There were reports in social media of how studies with null findings have been previously sandbagged in anonymous peer review or how authors were pressured by peer reviewers to spin results. Evidence surfaced of 3P founder Matt Sanders attempting to influence the reporting of a supposedly independently conducted evaluation. It is unclear how frequently this occurs, but represents a weakening of the important distinction between independent evaluations and those with conflicts of interest.

The Belgian government announced defunding of 3P programs. Doubts whether 3P was the treatment of choice were raised in 3P’s home country. 3p is a big ticket item in Australia, with New South Wales alone spending $6.6 million on it.

A detailed critique called into question the positive results claimed for one of the largest and influential population-based 3P interventions, and the non-disclosed conflicts of interest of the authors and the editorial board of the journal in which it appeared – Prevention Sciencewere exposed.

Are we witnessing the decline effect  in the evaluation of 3P? Applied to intervention studies, the term refers to the recurring pattern when weaker results accumulate from larger, more sophisticated studies not conducted by promoters of the intervention who initially had produced glowing reports of efficacy and effectiveness.

But the 3P promoters viciously and unethically fought back. Paid spokespersons took to the media to denounce independently conducted negative evaluations. Critics were threatened in their workplace, letters of complaint were written to their universities. Programs threatened with withdrawal of 3P resources if the critics weren’t silenced. Publications with undisclosed conflicts of interest authored by paid promoters of 3P continue to appear, despite the erratum and addendum apologizing for what had occurred in the past.

In this issue of Mind the Brain, I review the commentary in BMC Medicine. I raise the larger issue of whether the promoters of 3P’s recurring undeclared conflicts of interests represents actionable scientific misconduct. And I deliver a call to action.

My goal is to get BMC Medicine to change its policies concerning disclosure of conflict of interest and its sanctions for nondisclosure. I am not accusing the editorial board of BMC Medicine of wrongdoing.

The journal was the first to publish serious doubts about the effectiveness of 3P. Scottish GP  Phil Wilson and colleagues went there after his meta analysis was trashed in anonymous peer review at Elsevier’s Clinical Psychology Review (CPR). He faced retaliation from the workplace after he was contacted directly by the founder of 3P immediately after his submission to CPR. Matt Sanders sent him papers published after the end date Wilson had set for the papers included in his meta analysis. Bravo for BMC Medicine for nevertheless getting Wilson’s review into print. But the BMC Medicine editors have been repeatedly duped by 3P promoters and they now have the opportunity to serve as a model for academic publishing in mounting an effective response.

Stepping Stones Triple P: the importance of putting the findings into context

The BMC Medicine commentary by Tellegen and Sofronoff  is available here. The commentary first appeared without a response from the authors who were being criticized, but that has now been rectified.

Tellegen and Sofronoff chastised  the authors of a recent randomized trial [d], also published in BMC Medicine that evaluated the interventions with parents of children with Borderline to Mild Intellectual Ability (BMD).

Firstly, the authors present a rationale for conducting the study that does not accurately represent the current state of evidence for SSTP. Secondly, the authors present an impoverished interpretation of the findings within the paper.

The “current state of evidence for SSTP” about which Tellegen and Sofronoff complain refers to a systematic review and meta-analysis authored by Tellegen and Matt Saunders. I previously told how

  • An earlier version of this review was circulated on the Internet labeled as under review at Monographs of the Society of Research in Child Development. It’s inappropriate to distribute manuscripts indicating that they are “under review” at particular journals. APA guidelines explicitly forbid it. This may have led to the manuscript’s rejection.
  • The article nonetheless soon appeared in Clinical Psychology Review in a version that differed little from the manuscript previously available on the Internet, suggesting weak peer-review.
  • The article displays numerous instances of meta analysis malpractice. It is so bad and violates so many standards, that I recommend its use in seminars as an example of bad practices.
  • This article had no declared conflicts of interests.

Tellegen and Sofronoff’s charge of ”impoverished interpretation of the findings within the paper” refers to the investigators failing to cite 4 quite low quality studies that were not randomized trials but were treated as equivalent to RCTs in Tellegen and Sanders own meta-analyses.

In their response to the commentary from 3P, three of the authors – Sijmen A Reijneveld, Marijke Kleefman, and Daniëlle EMC Jansen of the original trial calmly and effectively dismissed these criticisms. They responded a lot more politely than I would have.

is youThe declarations of conflict of interest of 3P promoters in BMC Medicine: Is you is or ain’t you is making money?

An earlier commentary in BMC Medicine whose authors included 3P developer Matt Sanders and Kate Sofronoff – an author of the commentary under discussion – stated in the text:

Triple P is not owned by its authors, but by The University of Queensland. Royalty payments from dissemination activities, principally the sale of books, are paid by the publisher (Triple P International) to the University of Queensland’s technology transfer company (UniQuest), and distributed to the university’s Faculty of Social and Behavioural Sciences, School of Psychology, Parenting and Family Support Centre and contributory authors in accordance with the university’s intellectual property policy. None of the program authors own shares in Triple P International, the company licensed by the University of Queensland to disseminate the program worldwide.

What is one to make of this? It seems to answer “no” to the usual question of whether authors own stock or share ownership in a company. It doesn’t say directly about what happens to the royalties from the sale of books. Keep in mind, that the multimillion dollar enterprise of 3P involves selling lots of books, training materials, workshops, and government contracts. But a reader would have to go to the University of Queensland’s intellectual property policy to make sense of this disclaimer.

The formal COI statement in the article does not clarify much, but should arouse curiosity and skepticism –

…Royalties stemming from this dissemination work are paid to UniQuest, which distributes payments to the University of Queensland Faculty of Social and Behavioural Sciences, School of Psychology, Parenting and Family Support Centre, and contributory authors in accordance with the University’s intellectual property policy.

No author has any share or ownership in Triple P International. MS is the founder and lead author of the Triple P-Positive Parenting Program, and is a consultant to Triple P International. JP has no competing interests. JK is a co-author of Grandparent Triple P. KT is a co-author of many of the Triple P interventions and resources for families of children up to 12 years of age. AM is a co-author of several Triple P interventions for young children including Fuss-Free Mealtime Triple P. TM is a co-author of Stepping Stones Triple P for families of children with disabilities. AR is a co-author of Teen Triple P for parents of adolescents, and is Head of Training at Triple P International. KS has no competing interests.

omgThe authors seem to be acknowledging receiving money as “contributory authors” but there is still a lot of beating around the bush. Again, one needs to know what more about the university’s intellectual properties policy. Okay, take the trouble to go to the website for the University of Queensland to determine just how lucrative the arrangements are. You will surely say “Wow!” If you keep in mind the multimillion dollar nature of the 3P enterprise.

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The present commentary in BMC Medicine seems to improve transparency –

The Triple P – Positive Parenting Program is owned by The University of Queensland (UQ). The University through its main technology transfer company, UniQuest Pty Ltd, has licensed Triple P International Pty Ltd to publish and disseminate the program worldwide. Royalties stemming from published Triple P resources are distributed to the Faculty of Health and Behavioural Sciences at UQ, Parenting and Family Support Centre, School of Psychology at UQ, and contributory authors. No author has any share or ownership in Triple P International Pty Ltd. Cassandra Tellegen and Kate Sofronoff are employees of the UQ and members of the Triple P Research Network

But the disclosure remains evasive and misleading. One has to look elsewhere to find out that there is only a single share of Triple P International Pty Ltd, owned by Mr Des McWilliam. He was awarded a 2009 honorary doctorate by the University of Queensland in 2009. The citation … acknowledged that

Mr McWilliam’s relationship with Triple P had provided grant leveraging, both nationally and internationally, for ongoing research by the PFSC and had supported ongoing international trials of the program.

another wedding photoInteresting, but there is still an undeclared COI that is required for adherence to the International Committee of Medical Journal Editors (ICMJE) to which BMC Medicine subscribes. Just as Matt Sanders is married to Patricia Sanders, Cassandra L Tellegen is married to James Kirby, a psychologist who has written at least 12 articles with Sanders on 3 P and a 3P workbook for grandparents. Aha, both Sanders and Tellegen are married to persons financially benefiting from 3P programs. All in the family. And spousal relationships are reportable conflicts of interest.

I don’t know about you, but I’m getting damn sick and tired of all the shuck ‘n jiving from triple P parenting when they’re required to disclose conflicts of interest.

shark-life-guardWhy get upset about conflict of interests in evaluations of nonpharmacological trials and reviews?

My colleagues and I played a role in improving the tracking of conflicts of interest going from industry-supported clinical trials to inclusion in meta-analyses. Our criticism prompted Cochrane Collaboration to close a loophole in investigator conflict of interest not having been identified as a formal risk of bias. Prior to the change, results of an industry sponsored pharmacological trial could be entered into a meta-analysis where the origins were no longer apparent. The collaboration awarded us the Bill Silverman Award for pointing out the problem.

It’s no longer controversial that in the evaluation of pharmacological interventions involving financial conflicts of interest are associated with inflated claims for efficacy. But the issue is ignored in evaluating nonpharmacological interventions, like psychotherapies or social programs like 3P.

Undeclared conflicts of interest in nonpharmacological trials threaten the trustworthiness of the psychological literature.

Readers are almost never informed about conflicts of interest in the trials evaluating psychotherapy evaluations and their integration in meta-analyses. Yet, “investigator allegiance” a.k.a. undeclared conflict of interest is one of the most robust predictors of effect size. Indeed, knowing the allegiance of an investigator more reliably predicts the direction of results than the particular psychotherapy being evaluated.

As reviewed in my numerous blog posts  [1,2,3], there are no doubts that evaluations of 3P are inflated with a strong confirmation bias associated with undeclared complex of interest.

But the problem is bigger than that when it comes to 3P. Millions of dollars are being invested in on claims that improvement in parenting skills resulting from parents’ participation in 3P are a solution for pressing larger social problems. The money that could be being wasted on 3P is diverted from other solutions. And participation of parents in 3P programs is often not voluntary. They participate to avoid other adverse outcomes like removal of the children from their home by enrollment in 3P. That’s not a fair choice, when 3P may not provide them any other benefit and certainly not what it is advertised as providing.

HMarriage-image2We should learn from the results of President George W. Bush committing hundreds of millions of dollars to promote stable and healthy marriages. The evidence for the programs selected for implementation were almost entirely from small-scale, methodologically flawed studies conducted by their developers who typically did not publish with declared conflicts of interest. Later evaluations showed the programs to be grossly ineffective. An independent evaluation  showed positive findings of the particular programs did not occurred more than would be expected by chance. What a waste, but I doubt President Bush cared. As part of a larger package, he was able to slash welfare payments to the poor and shorten the allowable time for unemployment payments.

Politicians will accept ineffective social programs if they are in the service of being able to claim that they are not just doing nothing, they are offering solutions. And the ineffective social programs are particularly attractive when they cost less than a serious effort to address the social problems.

must declare

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goods to declare2pgWhat I’m asking of BMC Medicine: A model response

  • Consistent with Committee on Publication Ethics (COPE) recommendations, persons with conflict of interest should not be invited to write commentaries. I’m not sure that wanting to respond to null findings for their prized product is a justifiable override of this restriction. But if a commentary is deemed justified, there needs to be no ambiguity about the declaration of conflict of interest by the authors.
  • If journals have a policy of commentaries not undergoing peer review, it should be indicated at each and every commentary that is the case. That would be consistent with COPE recommendations concerning non-peer-reviewed papers in journals identifying themselves as peer-reviewed.
  • Consistent with the opinion of many universities, failure to declare conflicts of interest constitutes scientific misconduct.
  • Scientific misconduct is grounds for retraction. Saying “Sorry, we forgot” in an erratum is an inadequate response. We need some sort of expanded pottery barn rule by which journals don’t just allow author to publish an apology when the journal discovers an undeclared conflict of interest.
  • Articles for which authors declare conflicts of interest should be subject to particular editorial scrutiny, given the common association of conflicts of interest and spinning of results and other confirmatory bias.
  • Obviously, 3P promoters have had problems figuring out what conflicts of interest they have to declare. How about requiring all articles to require a statement that I first saw in a BMJ article, something like

I have read all ICMJE standards and on that basis declare the following:

If authors are going to lie, let’s make it obvious and more actionable.

Please listen Up, PLOS One

I am grateful to PLOS One for carefully investigating my charges that the authors of an article had substantial undeclared conflicts of interest.

The situation was outrageous. Aside from the conflicts of interest, the article was – as I documented in my blog post – neurobalm. The appearance of positive results was obtained by selective reporting of the data from analyses redone after previous analyses did not produce positive results. A misleading video was released on the internet accompanied by soft music and claims to demonstrate scientific evidence in PLOS One that a particular psychotherapy “soothed the threatened brain.” Yup, that was also in the title of the PLOS One article. The highly spun article was part of a marketing of workshops to psychotherapists who likely had little or no research training.

I volunteer as an Academic Editor for PLOS One and I resent the journal being caught up in misleading clinicians – and the patients they treat.

Upon investigation, the journal added an elaborate conflict of interest statement to the article. I’m impressed with the diligence with which the investigation was conducted.

Yet, the absence of a previous statement meant that the authors had denied any conflicts of interest in response to a standard query from the journal during the submission process.I think their failure to make an appropriate disclosure is scientific misconduct. Retraction should be considered.

Given the strong association between conflicts of interests or investigator allegiance in outcomes of psychosocial research, revelation of the undisclosed conflict of interest should have at least precipitated a careful re-review with heightened suspicion of spin and bias. And not by an editor who had not been informed of the conflict of interest and had missed the flaws the first time the article was reviewed. Editors are humans, they get defensive when embarrassed.

Disclaimer: The opinions I express here are my own, and not necessarily those of the PLOS One or other members of the editorial board. Thankfully, at Mind the Brain, bloggers are free to speak out for themselves without censorship or even approval from the sponsoring journal. Remember what happened at Psychology Today and how I came to blog here.

 

 

Category: Cochrane Collaboration, Conflict of interest, evidence-supported, meta analysis, parenting | Tagged , , , | Leave a comment

Repost: Francis “Frank” J. Underwood From Netflix’s House of Cards: A Textbook Case of Antisocial Personality Disorder

Last week, Netflix released Season 3 of House of Cards. In light of this, I am reposting a blog I wrote about the second season of the series last year: “Frank” J. Underwood From Netflix’s House of Cards: A Textbook Case of Antisocial Personality Disorder.” 

 

I always like to take the opportunity to explain misunderstood psychiatric concepts or diagnoses, and to clarify when a psychiatric term is used incorrectly or prone to misinterpretation.  In today’s blog, I aim to do both of these things.

 

First, I’ll use the character of Frank Underwood as a “case study” to illustrate the misunderstood psychiatric diagnosis of Antisocial Personality Disorder.

 

Kevin Spacey in House of Cards, Image: Netflix

Kevin Spacey in House of Cards, Image: Netflix

While enjoying the second season of House of Cards, I could not help but notice how Kevin Spacey’s character, Frank Underwood, meets a textbook definition of Antisocial Personality Disorder (ASPD).  Inspired by Spacey’s tremendous performance, I thought I would venture forth and use this example of a central character in a drama to illustrate this misunderstood and, often, underestimated psychiatric disorder.

Individuals with antisocial personality disorder (or sociopaths) are difficult and dangerous; they deny, lie, and contribute to all manner of mayhem in our communities and societies. They know full well what is going on around them and know the difference between right and wrong (and hence are fully responsible for their own behaviors) yet are simply unconcerned about such moral dilemmas.

Below is the “textbook” definition of ASPD interspersed with examples from the life of Frank Underwood, which perfectly illustrate the elements of this disorder.

 

SPOILER ALERT: For those of you who have not watched all of Season 2 yet, consider yourself warned.

 

Antisocial Personality Disorder 301.7 (From the DSM V): 

A) A pervasive pattern of disregard for and violation of the rights of others,  occurring since age 15 years, as indicated by three (or more) of the following

1) Failure to conform to social norms with respect to lawful behaviors, as indicated by repeatedly performing acts that are grounds for arrest.

 

Image: Netflix

Image: Netflix

Murder. Not once, but at least two times (that we know of).  He swiftly pushed Zoe Barnes into the path of an oncoming metro train. Let’s not forget this was a woman with whom he had had a physical relationship with and a (sort of) emotional intimacy.  No doubt, this personal history contributed to Barnes’ poor judgment and her letting down her guard; she suspected he was a murderer but still underestimated what he was truly capable of. Frank leveraged her miscalculation to his favor.

In addition to murder, let’s not forget the unlawful behaviors carried out, on his orders, by those who work for him – e.g. vanquishing the remaining reporters who tried to expose him for what he truly is.

 

2)  Deceitfulness, as indicated by repeated lying, use of aliases, or conning others for personal profit or pleasure

 

Image: Netflix

Image: Netflix

Honestly, I found it hard to keep track of the web of lies Frank wove during Season 2. What was notable was the sincerity with which he told many of these lies, almost as though in the moment he believed them himself. He repeatedly lied so he could drive a wedge in the previously tight relationship between the Billionaire, Raymond Tusk, and the President – a wedge he created, on purpose (and at much cost and hassle to the American tax payer!) to further his own goal of becoming President. 

 Then there was the web of lies told to cover the fact that his wife Claire’s (played by Robin Wright) abortion had nothing to do with her alleged rape by General McGinnis, but more to do with the inconvenience of Underwood’s political campaign timings.

A final example is the strategic drama he created (along with Claire) to cover her affair with Galloway.  Again, there was no inkling of any remorse or feelings that they should be held accountable for their actions.  Instead there was only a rigid entitlement:  How dare anyone get in the way of me becoming president?

 

3)  Impulsivity or failure to plan ahead

 

Underwood has a degree of impulse control.  In fact, his ability to plot, scheme, and plan has served him well with regards to his political posturing and career.  This is not the case for many with ASPD.  Those without means, education, or status can be dangerously impulsive, and this behavior often leaves them in jail, prison, or dead.

 

4)  Irritability and aggressiveness, as indicated by repeated physical fights or assaults

 

Image: Netflix

Image: Netflix

See point #3.  He is aggressive and violent but has probably learnt, over time, to become more measured in his actions.  Repeated irritable outbursts and acts of physical aggression are not compatible with life in political office.

 

5)  Reckless disregard for safety of self or others

 

 See point #1.

 

6)  Consistent irresponsibility, as indicated by repeated failure to sustain consistent work behavior or honor financial obligations

 

 Did Frank Underwood honor any of his obligations or duties associated with being the Vice President of the United States of America?  Did he use his powers to be of service to the American people or to his country?  No.  His days and nights appeared to be utterly consumed with one goal…to become president of the United States.  At any cost.

 

7)  Lack of remorse, as indicated by being indifferent to or rationalizing having hurt, mistreated or stolen from another.

 

Image: Netflix

Image: Netflix

This was best illustrated in his reaction to the murder of  Zoe Barnes.  It was business as usual.  Not a hair out of place, no loss of appetite or sleep.  No remorse, no guilt or angst. She was getting in his way as he tried to forge a path to the presidency, so he got rid of her and never thought about it again. Her murder was no more of an incident than flicking lint from his jacket lapel.  In fact, he was so cool after the event that it makes me wonder about his psychopathic tendencies, but that would be a whole other blog for another day.

 

B) Individual is at least 18 years old

 

C) There is evidence of conduct disorder with onset before age 15 years

 

Who knows what skeletons lie in the Frank Underwood closet?

 

D) The occurrence of antisocial behavior is not exclusively during the course of schizophrenia or bipolar disorder.

 

One final point that is not done justice in the brief description above (more details can be found here) – those with ASPD are able to be utterly charismatic, charming, and almost bewitching. This characteristic is one Spacey has down to a tee in his performance.

Image Credit: Melinda Sue Gordon

Image Credit: Melinda Sue Gordon

When Frank wants something or needs to manipulate someone, he is able to “switch on” the charm in an instant.  He conveys to others that he cares deeply about them by flashing an infectious smile and being gracious and attentive.

And, as season 2 showed, there were many who fell prey to his deceit…not least of all the President of the free world.  Perhaps nowhere is his charisma more evident that in the perverse loyalty of those in his inner circle; all turn a blind eye to what he is capable of and appear to be utterly captivated by his personality and presence.

 

My second point: The term “antisocial” is used incorrectly or prone to misinterpretation. 

 

The seriousness of ASPD leads me to my next point – the confusing usage of the term “antisocial.” Antisocial is often used in lay language to indicate someone who is shy and unwilling or unable to associate in a normal or friendly way with other people. While this is a legitimate definition of the word, I have never been a fan of how this one word can be used in such opposing ways. I would advocate that we reserve this word for individuals with personality disorders associated with the features described above. People who are described as “antisocial” because they are shy are (typically) not dangerous.  This is in sharp contrast to the definition of antisocial widely used in mental health terminology. In this context antisocial goes hand in hand with being “antisociety” and is a disorder associated with much more sinister and outright dangerous and reckless behavior.

 

At this point, many of you might be saying, well who cares about these individuals?  They are just evil, so why bother to make a psychiatric case about them?  Just lock them up and throw away the key!

 

But the situation is vastly more complicated than that.

 

ASPD is common.  For the reasons outlined above (their lies, deception, and charm) sociopaths are not always easy to detect, yet ASPD is associated with huge costs to our society that extend well beyond the individual who has the disorder. We have to stay curious about ASPD – about how the disorder develops, how to detect it, how to manage it – as our societies pay for its consequences on many levels, economically, socially, and emotionally.

And when someone with ASPD ends up in a position of unparalleled power? Well, who knows what the consequences could be.

 

Category: Commentary, mental health care, Psychiatry, Uncategorized | Tagged , , , , , , | Leave a comment

How Understanding Psychosis could have been more credible and trustworthy

hanging out the truth

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As promised, this issue of Mind the Brain explains how the British Psychological Society Division of Clinical Psychology ’s Understanding Psychosis could have been much more credible and trustworthy.

I point to well-founded skepticism about like-minded, self-selected groups representing single professions lacking any cultural diversity trying to tell clinicians and policymakers about how health services ought be re-organized. The folly of Division of Clinical Psychology’s way of doing things is compounded by excluding key consumer stakeholders. I will provide some standards and procedures that were blatantly ignored in the writing and dissemination of their recommendations.

The Division of Clinical Psychology is preparing a companion document about depression. I hope there is time for their adopting international standards. But they would have to open themselves to diversity and desegregate, allowing ethnic minorities, especially African and British Blacks a seat at the table. I will explain why their systematic exclusion of this group from the deliberations is particularly egregious, given gross inequalities in the services they receive, often from almost uniformly white clinical psychologists.

I take seriously the authors claim that they wanted to be provide an authoritative source of information for to mental health service users, their family members, and other professionals and policymakers and members of the community attempting to decide what the best policies for dealing with persons described as suffering from psychosis or schizophrenia. But I don’t accept the document simply because the authors claim they are experts or that they are creating a paradigm shift.

Skepticism should be raised when professional groups crow too loudly about their expertise and creating a shift in paradigm. Rhetorically, professionals fare better when they show what they have to offer and leave for others to decide whether they should be labeled “experts” or that they are causing a paradigm shift.

paradigm-shift-cartoon

I recall Dan Haller, former editor of Journal of Clinical Oncology poking fun at authors submitting manuscripts that they claimed represented paradigm shifts. Maybe in hindsight, Galileo, and, over Einstein deserve that label, but no paper he had ever reviewed about chemotherapy, radiation treatment, for immunotherapy earned it. Haller felt authors’ claim of making a paradigm shift simply embarrassed themselves.

When I subjected the 180 page document to my usual skeptical, critical scrutiny, its credibility and trustworthiness simply didn’t hold up. It seemed to be a collection of carefully selected and edited quotes and minimal, but unsystematic reference to the literature. It seemed to crassly sacrifice the well-being of persons with psychosis and schizophrenia – white, African and British black, and other groups – to professional self-interests of a small group of psychologists.

To an American like me, Understanding Psychosis seems like a bit of old-fashionedBengal-governor-during-British-rule colonial administratorBritish colonial administration. Clad in pith helmets, the British clinical psychologists went out and recruited a few supporters who shared their views and suppressed silenced the rest of service users and their families – pretending they don’t even exist – who would be so affected by their proposals. And as I noted in my last blog post, there are grounds to doubt that a good proportion of the supporters whom they quote are even service users.

When I raised the issues of consensus and process in Understanding Psychosis on Twitter in November 2014, I got an immediate response from the official Division of Clinical Psychology Twitter account

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To which I replied

Please click to enlarge

My “debunking” – if that’s what@DCP wants to call it – involves systematic gathering relevant evidence and evaluating it by transparent standards that others have agreed upon. When I formally do this in peer-reviewed articles, I typically involve other people as a check on my biases, as well as procedures by which readers can decide for themselves on the validity of my conclusions. When I am flying solo, that needs to be taken into account, and readers should start with greater skepticism. I am more dependent on sufficiently documenting my evidence in order to persuade them.

Some questions are clearly defined enough to proceed with a systematic search for relevant evidence: “the screening for psychological distress improves patient outcomes?”

But many questions like “do we abandon psychiatric diagnosis” or “how do we best organize services to ensure better patient outcomes?” involve potentially controversial decisions about how to sharpen the questions in order to gather relevant evidence. It’s best to get a diversity of opinions of both professionals and service consumers to define the range of possibilities. There need to be some checks on biases, with the hope that these can be overcome by some consensus process among people starting with clear differences of opinion. That is not just an ideal, that’s a necessity if some professional group is going to claim authority for its recommendations. I am typically not operating in that context, and so the credibility of what I in my co-authors come up with the strength of evidence, and we leave for others decisions about how or whether  recommendations will be implemented.

There are some widely accepted standards for bringing relevant stakeholders together, reviewing available evidence, and formulating recommendations. There is lots of evidence about the consequences when these procedures are followed.

But before getting into them, let me describe how I came to be appreciative of both the necessity for the standards for professional organizations formally making policy recommendations and the existence of rules by which they should proceed and be evaluated.

Our 2008 JAMA systematic review and meta-analysis of screening for depression in cardiac patients and reactions from the American Psychiatric Association.

Our paper was

Thombs, B. D., de Jonge, P., Coyne, J. C., Whooley, M. A., Frasure-Smith, N., Mitchell, A. J., … & Ziegelstein, R. C. (2008). Depression screening and patient outcomes in cardiovascular care: a systematic review. JAMA, 300(18), 2161-2171.

Our international group of authors had published key papers and chapters in a book onscreening for depression the topic of screening for depression, as well as the role of depression in cardiovascular disease (CVD). We neither proclaimed ourselves “experts” nor had the endorsement of a professional organization backing up our conclusions. But we identified and followed well defined standards for turning clinical and policy issues into topics for systematic review and meta-analysis. And we were quite transparent in what we did and how it conformed to international standards.

Our conclusion was

The high prevalence of depression in patients with CVD, the adverse health care outcomes associated with depression, and the availability of easy-to-use case-finding instruments make it tempting to endorse widespread depression screening in cardiovascular care. However, the adaptation of depression screening in cardiovascular care settings would likely be unduly resource intensive and would not be likely to benefit patients in the absence of significant changes in current models of care.

The JAMA editors liked the paper enough to invite some of the authors to participate in a live webinair with participants able to telephone and email questions.. The editors of BMJ nominated the paper is one of the eight top papers of the year to be considered in a competition for the top paper.

I was caught off guard when just a few weeks later a paper appeared on the Internet labeled as a American Heart Association Science Advisory with a list of impressive committees signing on to its conclusions and the American Psychiatric Association prominently listed as endorsing the advisory.

The recommendations directly contradicted ours:

Although there is currently no direct evidence that screening for depression leads to improved outcomes in cardiovascular populations, depression has been linked to increased morbidity and mortality, poorer risk factor modification, lower rates of cardiac rehabilitation, and reduced quality of life.  Therefore, it is important to assess depression in cardiac patients with the goal of targeting those most in need of treatment and support services.

And

In summary, the high prevalence of depression in patients with CHD supports a strategy of increased awareness and screening for depression in patients with CHD.

Politics versus rules of making evidence-based decisions

Our conclusions were based on best evidence and transparent rules for evaluating that evidence. The AHA Science Advisory was based on a consensus of professionals – psychologists and psychiatrists – who had vested interests in promoting screening because it would increase their professional opportunities in cardiology settings.

Although publicity for our article had some momentum, the promoters of the AHA Science Advisory jumped into the media with a lot of political power to counter our conclusions, while usually failing to acknowledge who we were and where we had published. The American Psychiatric Association actually assigned a pediatric psychiatrist to become a media contact for their point of view.

I had naïvely thought that best evidence would trump consensus of professionals with obvious self-interests at stake. The weight of evidence was clearly on our side. But one of our cardiologist co-authors, Roy Zigelstein was not at all surprised by the carefully orchestrated reaction.

Roy negotiated us an opportunity with American Heart Journal and Journal of the American Academy of Cardiology to explain the differences between us and the AHA Science Advisory. Although we were up against strong vested interests, cardiologists themselves were not necessarily in agreement with the science advisory.  Actually, the American Heart Association continually updates its evaluations of factors correlated with cardiovascular outcomes as causal factors. To this day, it still has not accepted depression as a causal factor, only a risk marker. The implication is that making changes in depression may not necessarily affect cardiac outcomes.

In our commentary at American Heart Journal, we noted the discrepancy between the results of our meta-analysis and systematic review versus the conclusions of the AHA Science Advisory. We also noted that we were not alone in expressing concern about guidelines issued by the American Heart Association increasingly being based on simple professional consensus and not a systematic review of the evidence. Consequently many of them were not “best evidence.”

“In guidelines we cannot trust”

Our skirmishing with the AHA Science Advisory and American Psychiatric Association occurred at a time when recognition was already growing that the recommendations of professional organizations were untrustworthy. There was documentation of numerous instances in which they were often not evidence-based, but served their self-interests, often at the expense of patient outcomes. Many of the recommendations were for billable procedures from the professional groups who created them that were unnecessary and even harmful to patients.

The title of a later article captured the rampant skepticism of the time:

Shaneyfelt T. In guidelines we cannot trust. Arch Intern Med 2012;172:1633-1634.

There were lots of proposals for reform, like a series that included

Fretheim A, Schunemann HJ, Oxman AD. Improving the use of research evidence in guideline development: 5. Group processes. Health Res Policy Syst 2006;4:17.

guidelines we can trustBut discontent gut all the way to the U.S. Congress, which authorized that the Institute of Medicine (IOM) be given the resources to organize a panel with wide representation to come up with, as the final 250 page document was titled, Clinical Guidelines We Can Trust. You can download a free PDF here.

The rationale for specific procedures spelled out, but in terms of the final product:

To be trustworthy,  guidelines should

  • Be based on a systematic review of the existing evidence.
  • Be developed by a knowledgeable, multidisciplinary panel of experts and representatives from key affected groups.
  • Consider important patient subgroups and patient preferences, as appropriate.
  • Be based on an explicit and transparent process that minimizes distortions, biases, and conflicts of interest.
  • Provide a clear explanation of the logical relationships between alternative care options and health outcomes, and provide ratings of both the quality of evidence and the strength of the recommendations.
  • Be reconsidered and revised as appropriate when important new evidence warrants modifications of recommendations.

understand coverThe standards seem eminently reasonable in the deliberations by which they were reached is carefully documented. Yet Understanding Psychosis fails miserably as a set of credible policy recommendations by not meeting any of them. It’s because the process of writing the document was so flawed:

  • The British Psychological Society Division of Clinical Psychology professionals did not engage other professionals with complementary viewpoints and expertise.
  • Key stakeholders were simply excluded – primary care physicians, social workers, psychiatrists, , police and corrections personnel who must make decisions about how to deal with disturbed behavior,  and –most importantly- the family members of persons with severe disturbance.
  • There was no clear explicit process to minimize bias and distortion and no transparency as to how the group arrived at particular conclusions.
  • There was no check on the psychologists simply slanting the document to conform to their own narrow professional self-interests.
  • Recommendations were presented without clear grading of the quality of available evidence or strength of recommendations.
  • While there was a carefully orchestrated “show and tell” rollout, it did not involve any opportunities for feedback and modification of recommendations.

In one of a number of passages plagiarized from an earlier paper, Peter Kinderman recently told clinicians from other disciplines to adopt the recommendations of Understanding Psychosis

To return, then, to the issue of communication between professionals; for clinicians, working in multidisciplinary teams, the most useful approach would be to develop individual formulations; consisting of a summary of an individual’s problems and circumstances, hypothesis about their origins and possible therapeutic solutions. As with direct clinical work, such an approach would yield all the benefits of the traditional ‘diagnosis, treatment’ approach without its many inadequacies and dangers. This would require all clinicians— doctors, nurses and other professionals—to adopt new ways of thinking.

Why should these professionals do the bidding of a small group of self-serving psychologists? They were not involved in the process of constructing these recommendations and the psychologists failed to provide appropriate evidence. There is no evidence that this would improve patient outcomes.

A special pleading for marginalized and silenced Black African clients who were getting poor care.

Enter “African” as a search term in the 180 page Understanding Psychosis and you come up with only a brief mention on page 46 that fails to acknowledge the poor outcomes that tradition African Black are disproportionately achieving in outpatient care. Even if there are few, if any black members of the BPS Diision of Psychology and even if there were no blacks involved in the writing of Understanding Psychosis, surely there was some awareness of the gross disparities in outcomes that are achieved in outpatient care for psychosis and schizophrenia. A recent paper added further evidence to what was already known:

  • Early Intervention Services (EIS) have little effect on the much higher admission and retention rates of Black African clients.
  • There are low rates of GP involvement and high rates of police detention.
  • Poor outcomes were most marked in Black African women (7-8x  greater odds than White British women).
  • A post-hoc analysis showed that pathways to care and help-seeking behavior partially explained these differences.

Overall

In an increasingly outcome-driven and evidence-based era, EIS need to demonstrate a significant positive impact on detecting and treating psychosis early, across all groups. Our findings, when compared with UK studies from the pre-EIS era [5], suggest no improvement in the inequality between Black African patients with FEP and White British patients in terms of experiences of admission and detention. The high rates of detention and hospital admission overall are likely to have substantial implications for continuing engagement. The rate of detention is particularly elevated in Black African patients at 60% (Table 2). A disconcerting finding is of even higher rates in certain groups than prior to introduction of EIS, especially in women. While there is overall evidence that the EIS model is a cost-effective [31] means of engaging hard-to-reach young people, it would seem not all groups are being reached in ways that minimise stigma and trauma. Of note, a recent systematic review of initiatives to shorten DUP [32] concluded that establishing dedicated services for people with FEP does not in itself reduce DUP. This is despite evidence that longer DUP is associated with poorer outcomes [33],[34].

“In an increasingly outcome-driven and evidence-based era,” the British Psychological Society Division of Clinical Psychology had better involve a broader and more ethnically diverse range of opinions and more careful consideration of available evidence if they are going to be taking seriously.

Counterpoint from Richard Pemberton, UK Chair of the British Psychological Society Division of Clinical Psychology:

Your approach to debate and tendency to personalise professional differences however means that many senior people don’t take you seriously and/or aren’t willing to get in the same room as you. Describing the very senior and prestigious group of researchers who were co-authors of our recent psychosis publication as either ‘stoned or drunk’ is a case in point? Doing this in private would be testing but putting this out into the public domain certainly breaches UK professional ethical codes. I am sure that you sincerely believe that the report is deeply flawed and highly problematic but I doubt that you actually believe that we are all sitting around under the influence of drugs and alcohol producing 180 page publications.

Category: antipsychotics, evidence-supported, professional organizations, psychosis, psychotherapy, schizophrenia | Tagged , , , , | 4 Comments