NJ Psychological Association challenges APA Clinical Practice Guideline for the Treatment of PTSD


quick takes

ptsd guidelinesThe APA guidelines can be found here 

From: Charity Wilkinson <wilkinson.charity@gmail.com>

Subject: [abct-members] APA PTSD Clinical Practice Guideline Being Questioned by NJPA

Date: December 22, 2017 at 7:44:44 PM CST

To: ABCT Member List <abct-members@lists.abct.org>

Reply-To: ABCT Member List <abct-members@lists.abct.org>

Dear Colleagues,

I’m writing to bring to your attention that the NJ Psychological Association issued statement today indicating that they sent a message to the APA expressing concern about the Clinical Practice Guideline for the Treatment of PTSD. This action was taken when a group of over 75 psychologists in NJ signed a letter opposing the Guideline. Though many of us sent statements to the NJPA supporting the Guideline, our statement was ignored.

The NJPA’s statement advocates for psychologists practicing from psychodynamic and other orientations who believe that their work has been wrongfully excluded. They have indicated that they fear the loss of their livelihood, insurance companies not funding their work, and the opportunity for clients to receive psychodynamic and other treatments that were not included. The statement also suggests that all treatments yield results and that RCT’s should not have been as strongly considered in the development of the Guideline.

I would ask that ABCT members and perhaps leadership create a statement in support of the APA PTSD Guideline.

Thank you for your consideration.


Charity Wilkinson-Truong

This is why APA has been so reluctant to take a stand and set guidelines about what is evidence-based psychotherapy and what is not.

See my post of a while ago (2012)

Troubles in the Branding of Psychotherapies as “Evidence Supported”


CBT versus psychodynamic therapy for depression: One sentence changes the whole story

A recent comparative effectiveness study in JAMA Psychiatry of CBT versus psychodynamic psychotherapy for depression was billed as a noninferiority trial.

booby prizeOne sentence in the results section changed the whole significance of the study.

The dodo bird verdict for the study is that everybody gets a booby prize.

The study is currently freely accessed at JAMA Psychiatry, although you may need to register for free to actually download the PDF.


Connolly Gibbons M, Gallop R, Thompson D, et al. Comparative Effectiveness of Cognitive Therapy and Dynamic Psychotherapy for Major Depressive Disorder in a Community Mental Health Setting: A Randomized Clinical Noninferiority Trial. JAMA Psychiatry. Published online August 03, 2016. doi:10.1001/jamapsychiatry.2016.1720.

The moderately sized study compared to active treatments without a nonspecific comparison/control group.

Results.  Among the 237 patients (59 men [24.9%]; 178 women [75.1%]; mean [SD] age, 36.2 [12.1] years) treated by 20 therapists (19 women and 1 man; mean [SD] age, 40.0 [14.6] years), 118 were randomized to DT and 119 to CT. A mean (SD) difference between treatments was found in the change on the Hamilton Rating Scale for Depression of 0.86 (7.73) scale points (95% CI, −0.70 to 2.42; Cohen d, 0.11), indicating that DT was statistically not inferior to CT. A statistically significant main effect was found for time (F1,198 = 75.92; P  = .001). No statistically significant differences were found between treatments on patient ratings of treatment credibility. Dynamic psychotherapy and CT were discriminated from each other on competence in supportive techniques (t120 = 2.48; P = .02), competence in expressive techniques (t120 = 4.78; P = .001), adherence to CT techniques (t115 = −7.07; P = .001), and competence in CT (t115 = −7.07; P = .001).

Conclusions and Relevance.  This study suggests that DT is not inferior to CT on change in depression for the treatment of MDD in a community mental health setting. The 95% CI suggests that the effects of DT are equivalent to those of CT.

In case there is any ambiguity in the message the authors wanted to convey, they reiterated:

Key Points

  • Question Is short-term dynamic psychotherapy not inferior to cognitive therapy in the treatment of major depressive disorder (MDD) in the community mental health setting?

  • Findings In this randomized noninferiority trial that included 237 adults, short-term dynamic psychotherapy was statistically significantly noninferior to cognitive therapy in decreasing depressive symptoms among patients receiving services for MDD in the community mental health setting.

  • Meaning Short-term dynamic psychotherapy and cognitive therapy may be effective in treating MDD in the community.

Despite an accompanying editorial, the study only got a moderate amount of immediate attention in the social media. Here are the altmetrics.views

altmetrics PNG

parroting I examined the 40 tweets available on August 6, 2016 and found only one that went beyond parroting.

good tweets I I suspect that Robert Howard had discovered the one sentence in the results section that I noticed:


Nineteen patients (16.1%) in DT and 26 patients (21.8%) in the CT condition demonstrated response to treatment as measured by a 50% reduction on the HAM-D score across treatment (χ21 = 1.27; P = .32).

Most of the patients assigned to either group in this study failed to respond to treatment. Tipped off by this sentence, I looked for the degree of treatment exposure and found that most patients did not get exposed to sufficient intensity of treatment.

Sixty-three patients (26.6%) attended 1 or fewer sessions of psychotherapy; 122 (51.5%), 5 or fewer sessions; and 187 (78.9%), 11 or fewer sessions. We found no statistically significant difference between treatments in the number of sessions attended (t235 = 1.47; P = .14).

 The title of the JAMA Psychiatry article noted that patients had been recruited from the community mental health center. I interpret this to suggest they were likely to be a low income group who were not previously prepared for psychotherapy.

Before anyone proposes that the solution is simply to offer more therapy, note that the patients were not attending enough sessions of a larger number (16) that were offered. My interpretation is that greater effort may be needed to get such patients to consistently show up for sessions.

My colleagues and I previously conducted an exceptionally well resourced study in in the same low income and socially disadvantaged Philadelphia population. Our intention was to reduce risk factors among recently pregnant, low income women for another low weight birth delivery. We demonstrated that we could recruit and retain these women, but it took an intensive, creative effort.

One of the risk factors that we addressed was depression and we offered antidepressant medication and free treatment at the world-renowned University of Pennsylvania Center For Cognitive Therapy. We provided free transportation and child care. Few women access sufficient therapy or receive sufficient dose of antidepressants. The therapists at the center complained that the women did not seem to have their life in order and did not seem ready for psychotherapy. Personally, I think that the therapist may not have been ready for such women and did not sufficiently engage them.

Back to the study under discussion, it was accompanied by an editorial that parroted the authors’ intended message in its title:

Abbass AA, Town JM. Bona Fide Psychotherapy Models Are Equally Effective for Major Depressive Disorder: Future Research Directions. JAMA Psychiatry. Published online August 03, 2016. doi:10.1001/jamapsychiatry.2016.1916.

But I noticed this in the text:


Among other points, the study by Connolly Gibbons and colleagues raises the ongoing challenge facing all psychiatrists using pharmacotherapy and psychotherapy: how to improve rates of remission in real-world clinical samples. The study found that more than 80% of all participants did not respond to treatment (22% of patients receiving CBT and 16% of patients receiving STPP had response to treatment as measured by a 50% reduction in observer-rated depression). This high rate of nonresponse may be partly explained by inadequate treatment “dose” or number of sessions, clinical sample, therapist expertise, biomedical factors, and sociofamilial factors impeding outcomes

The JAMA Psychiatry article under discussion cited another, similar study conducted in the Netherlands, but did not elaborate on its findings:

Driessen E, Van HL, Don FJ, Peen J, Kool S, Westra D, Hendriksen M, Schoevers RA, Cuijpers P, Twisk JW, Dekker JJ. The efficacy of cognitive-behavioral therapy and psychodynamic therapy in the outpatient treatment of major depression: a randomized clinical trial. American Journal of Psychiatry. 2013 Sep 1.

Unlike the JAMA Psychiatry article, the abstract of the Dutch study qualified its finding of non-inferiority by noting that nether therapy did particularly well:


No statistically significant treatment differences were found for any of the outcome measures. The average posttreatment remission rate was 22.7%. Noninferiority was shown for posttreatment HAM-D and patient-rated depression scores but could not be demonstrated for posttreatment remission rates or any of the follow-up measures.


The findings extend the evidence base of psychodynamic therapy for depression but also indicate that time-limited treatment is insufficient for a substantial number of patients encountered in psychiatric outpatient clinics.

dodo bird verdictI suspect that both of these randomized trials will be cited as evidence of the Dodo Bird Verdict for psychotherapy for depression – everybody’s a winner and everybody gets a prize. However, in both the studies, the cognitive behavior therapy underperformed relative to the efficacy demonstrated in a larger body of studies. The literature for psychodynamic therapy is more limited and of low quality.

Still, I think the messages that when you move into more difficult populations, you can’t expect results obtained with more carefully selected, therapy-ready patient populations who were recruited to more typical studies. But this may reflect on the unrepresentativeness of patients in the larger literature.

Meanwhile, Psychiatrist Erick Turner and I have been having an exchange on Twitter concerning another noninferiority study.

Turner Tweet.PNG

Erick is referring to a perspective he shares with things I’ve been saying regularly about noninferiority trials. They typically don’t include a nonspecific comparison/control group. Without such a group, we can’t evaluate whether either of the active treatments are better than provision of nonspecific treatments with elements of support, positive expectation, and attention.

That is also a limitation of the current study, but by peeking into the actual results, we discover referral to neither of two active treatments left most patients free of depression.

What if there had been a credible attention/support condition in the present study? Would either of these two treatments that were “noninferior” to each other have a clinically significant advantage? What would be the implications, if not? would the report have made it into JAMA Psychiatry?

Experts weigh in on Suzanne O’Sullivan’s commentary on imaginary illness in The Lancet


Google Suzanne O’Sullivan and you will find lots of coverage of her book that won the Wellcome Book Prize, but you will not find peer-reviewed articles that she authored. The same thing will happen if you Google Scholar her, where you just get lots of articles that were not written by her.  As a neurologist in charge of a six-bed unit epilepsy at the Royal London Hospital, she is very well connected, even if not well published.

Launch of her book, It’s All in Your Head in 2015 was coordinated with a keynote address arranged and subsequently praised by Simon Wessely at the Royal College of Psychiatrists International Conference. A laudatory review by another clinician who was not a scientist appeared in The Lancet soon thereafter, followed by Suzanne O’Sullivan’s own editorial commentary.

Her Lancet commentary, like O’Sullivan’s book is notably free of citations (except a single one to her book), despite her dispensing what are meant to be authoritative judgments for which we would expect documentation. These are judgments which could have negative implications for patients, some of them clearly harmful.

I routinely encourage readers of my blog to develop analytical and search tools to apply when they encounter reports about the biomedical and scientific literature that rouse their skepticism. But these tools and skills are not much use when focused on Suzanne O’Sullivan’s work. She does not make her sweeping claims in a way that one can follow back into the peer-reviewed literature unless one is guided by other knowledge. Skeptical readers have to rely on sources that time has proven trustworthy.

Yet, in the UK, where all the fuss is being made, professionals are notably discreetly silent, rather than outspoken, when a colleague misrepresents the literature or commits outright fraud. Stay tuned for my forthcoming blog about Hans Eysenck’s blatantly fraudulent data concerning alleged dramatic effects of cognitive behavior therapy on death from cancer, as well as the carcinogenic effects of psychoanalysis.

Suzanne O’Sullivan’s commentary in The Lancet shows no trappings of having been peer-reviewed. But it does have some statements for which I could call in some recognized authorities, with relevant clinical and medical expertise.

This blog post contains their evaluations of the claims in Suzanne O’Sullivan’s The Lancet article. For the first commentary I have the honor of presenting Professor Edward Shorter. For the second, I have Professor Ronald Pies.

shorterIntroducing Professor Edward Shorter, PhD, FRSC

Dr. Shorter is

Jason A. Hannah Professor of the History of Medicine in the Faculty of Medicine and is cross-appointed Professor of Psychiatry. His past research interests include a two-volume history of psychosomatic illness, “From Paralysis to Fatigue” (1992) and “From the Mind Into the Body” (1994). Since the mid-1990s he has emerged as an internationally recognized historian of psychiatry, with numerous publications to his credit. His “History of Psychiatry” (1997) has become the standard text in the field, joined in 2005 by “A Historical Dictionary of Psychiatry” and in 2009 by “Before Prozac”. This volume argues for a reassessment of diagnoses and treatments for mood and anxiety disorders that have been set aside in favour of patent-protected remedies and diagnoses promulgated by the DSM series. He further explores these themes in his latest book, “How Everyone Became Depressed: The Rise and Fall of the Nervous Breakdown” (Oxford University Press, 2013).

Professor Shorter also has a readily accessible blog. See, for instance, Why Don’t Doctors Want to Hear About Psychosomatic Problems?

ron-pies-photo-2-1.jpgIntroducing Professor Ronald Pies, MD

Dr Pies is Editor in Chief Emeritus of Psychiatric Times, and a Professor in the Psychiatry Departments of SUNY Upstate Medical University, Syracuse, NY, and Tufts University School of Medicine, Boston. Dr Pies is author, most recently, of Psychiatry on the Edge, a collection of essays drawn from Psychiatric Times (Nova Publishing); and a novel, The Director of Minor Tragedies (iUniverse); and The Myeloma Year, a chapbook of poems and essays.

Professor Pies’ article in Psychiatric Times are readily accessible, but so are his excellent guest blog posts, like Why Psychiatry Needs to Scrap the DSM System: An Immodest Proposal  With more patience than I have, Dr. Pies notably engages in dialogue with critical psychiatry.

Professor Shorter’s Commentary on Suzanne O’Sullivan’s article in The Lancet.

[All quotes are from Suzanne O’Sullivan’s commentary in The Lancet.]

 James, thank you for giving us an opportunity to comment on this interesting paper.  It does indeed contain several questionable assertions.

  1. “Psychiatrists and psychologists are those best placed to help people with psychosomatic disorders.”

No, internists and neurologists are, because they can maintain a therapeutic alliance intact, while these patients look askance at referrals to psychiatrists and psychologists:  They are convinced they are organically ill!   The only treatment, really, is the gift of time, letting the patients tell, and if necessary re-tell, their stories to a clinician who nods sympathetically while not necessarily endorsing the patients’ supposed etiologies.

  1.  “To tell somebody their medical complaint might have an emotional cause is often met with anger.”

Right.  You don’t tell them that.  You assure them that their subjective perceptions of their symptoms are very real, and let’s see if we can’t get to the bottom of this.  Then you let them talk.  This can be very time-consuming.

  1.  “If our subconscious has chosen to mask . . . “

The patient’s subconscious may not have chosen the symptoms.  It’s really the culture that choses them, and patients get from the culture an idea of what is medically “credible.”  Patients strive to produce symptoms that are medically believable, that cannot be disproven, in other words.  This is why the hysterical gait paralyses of the nineteenth century have largely disappeared: The Babinski test “disproved” them.  But you cannot prove that someone is not fatigued or in pain, which is why we see so much of that today.

Re EEGs as a gold standard of epilepsy:  I believe that about 50 percent of interictal EEGs in patients with real epilepsy are normal.

The illustration shows Charcot’s “hysteria,”  not a psychosomatic affection but an iatrogenic one.

My two cents.

Cheers to all,


Professor Pies’ Commentary on Suzanne O’Sullivan’s article in The Lancet.

Thanks for the paper, James. I’m generally in agreement with Ned’s comments, and have decidedly mixed reactions to O’Sullivan’s editorial. On the one hand, in my experience, it’s true that many medical personnel feel that “disability that occurs for psychological reasons [is] less deserving of our attention than other forms of disability”, leading to discrimination against “psych” patients, who are often dismissed as “crocks” or “malingerers.” O’Sullivan rightly notes (or at least implies) that persons with so-called psychogenic seizures (or non-epileptic seizures) are not deliberately producing these manifestations; i.e., they are not malingering or doing what Munchhausen patients do (i.e., dissociative seizures are not diagnosed as a “factitious disorder”). Thus, it goes without saying that patients with non-epileptic seizures and related syndromes deserve our compassion, understanding and help.

On the other hand, having come from a consultation-liaison background, I am more inclined to take Eliot Slater’s view that many patients diagnosed with a “psychosomatic” disorder—or, in the old terminology, “hysteria”—often prove to have an “organic” (e.g., neurological, endocrine, autoimmune) disorder underlying their problem. The statistic cited by O’Sullivan–that “only” 4% of cases wind up with an “organic” diagnosis–should really not be of much comfort to doctors, even if it is correct: imagine seeing 100 “psych” patients in a year with unexplained somatic symptoms, and eventually learning that 4 of them were not “hysterical” at all, but suffered from multiple sclerosis, systemic lupus, or had auto-antibodies against NMDA receptors producing their “psychiatric” problem [see: http://www.ncbi.nlm.nih.gov/pmc/articles/PMC3563251/]

My C-L supervisor used to say, “Hysteria is the last diagnosis a patient will ever receive”, simply because once “hysteria” is in the medical record, nobody will ever take the patient seriously again. Also, the O’Sullivan fails to note that in a substantial percentage of cases, a patient may have both “psychogenic” and epileptic seizures—and that sometimes, the latter is overlooked merely because the former is present. (I know that Al Frances and I have both expressed concern that the new DSM-5 category of “Somatic Symptom Disorders” may promote overlooking such underlying neurological disorders because the criteria are so broad).

My heavy use of quotation marks in this message also signals my uneasiness with terms like “psychogenic” and “psychological.” The best people in neuropsychiatry, like Michael Trimble, have urged a less Cartesian (mind vs. brain) and more integrative approach; e.g.,

“Whitlock 34 and Ludwig 35 have suggested that the primary pathophysiological mechanism involved in the creation and maintenance of dissociative (or “hysterical”) symptoms is an attentional dysfunction resulting from an increase in the corticofugal inhibition of afferent stimulation. As a result of this inhibition, partially processed stimulus information fails to be integrated into ongoing awareness, generating dissociative symptoms as a consequence. Some studies have provided empirical support for this account of dissociation.36 37 Part of the appeal of the approach advocated by investigators such as Ludwig is their emphasis on integrating research and theory from neurology, psychiatry, and psychology in a bid to understand the mechanisms of dissociation.  http://jnnp.bmj.com/content/69/3/285.full#ref-4

Best regards,




Is psychodynamic therapy an evidence-supported treatment? Critical look at a systematic review raises doubts.

Sometimes authors misapply principles of evidence-based medicine appraisal when their interests and livelihood depend on getting it wrong. This could serve as an example.

Leichsenring, F., Luyten, P., Hilsenroth, M. J., Abbass, A., Barber, J. P., Keefe, J. R., … & Steinert, C. (2015). Psychodynamic therapy meets evidence-based medicine: a systematic review using updated criteria. The Lancet Psychiatry, 2(7), 648-660

freudFalk Leichsenring and Sven Rabung have trying for years to get the “evidence supported” label attached to psychodynamic psychotherapy (PP), especially long term psychodynamic psychotherapy (LTPP). They have received surprising assists from editors of prestigious journals like JAMA  and British Journal of Psychiatry. They have also faced some withering criticisms of their breaking of basic rules in conducting and interpreting meta analyses and systematic reviews.

I teamed up with Aaron T. Beck and others in a detailed critique entitled Is Longer-Term Psychodynamic Psychotherapy More Effective than Shorter-Term Therapies? of their earlier efforts in JAMA. We faulted the meta-analysis and systematic review for its

  • Computational mistakes.
  • Improbably large effect sizes.
  • Integration of randomized and nonrandomized trials.
  • Ignoring of the uniformly poor quality of the studies included in the review.

Some of the studies involved comparing PP to conditions in which patients did not receive therapy of any kind.

For another succinct methodological critique see

 Littell, J. H., & Shlonsky, A. (2011). Making sense of meta-analysis: A critique of “effectiveness of long-term psychodynamic psychotherapy”. Clinical Social Work Journal, 39(4), 340-346.

Leichsenring and Rabung’s reply was not responsive to our critique, but they charged I had not disclosed a conflict of interest:

[This] critique reveals a bias that is obviously related to their own approach, although they do not disclose their conflicts of interest. One wonders whether CBT advocates who have a large financial stake in propagating the view that their treatment is superior, or the only evidence-based approach, can be objective about these scientific issues. Thus, the paper by Bhar et al. [7] may serve as an excellent example of an investigator allegiance effect. We regret that in this discussion, research is in danger of being used as a weapon to defeat a real or imagined rival. Although directed against and psychodynamic psychotherapy, such a misuse can do harm to the public image of psychotherapy in general.

Yup, Falk and Sven, I spend all my time writing CBT self-help books and doing workshops, when I am not, I do what I can to harm the public image of psychotherapy.

Actually, while I consider Dr. Beck a friend, he considers me one of his most persistent critics.

dead_dodo_200Like other psychotherapies, PP seeks the label of “evidence-based” in order to secure third-party payments. The problem is that PP is longer term and more intensive than other psychotherapies claiming that label. The added length and intensity may not be cost-effective. For some conditions, such as eating disorders, the dodo bird verdict may not actually hold for PP. For instance, cognitive behavioral therapy that is less intensive but more goal- rather than insight- oriented may be more effective than PP for bulimia.

A larger issue however is that practitioners of PP have historically tended toward suspicion and even hostility toward attempts to fit their approach into the rigor (that they consider false rigor) of a randomized trial. They tend to favor psychodynamic formulations over the formal diagnostic categories and standardized measurements used in research. PP does not have a strong research tradition. So, the quantity and quality of evidence that can be mustered for its efficacy is less than for other therapies

Bambi-meets-Godzilla-513d504906daa_hires-218x300Leichsenring and Rabung’s systematic review and meta-analysis in JAMA was accompanied by a guardedly positive editorial entitled Psychodynamic Psychotherapy and Research Evidence: Bambi Survives Godzilla?

The opening of the editorial explained

In a now classic 1982 article, Parloff surveyed the results of psychotherapy research evidence and its relevance for policy makers and treatment reimbursement decisions, characterizing that encounter as “Bambi meets Godzilla.” He concluded that although research evidence in psychotherapy outcome at that time was “extensive and positive,” it was not responsive to the policy makers’ central question, “What kinds of psychotherapy are most effective for what kinds of problems?”

The editorial concluded:

For now, the question is: Does this new meta-analysis mean that LTPP has survived the Godzilla of the demand for empirical demonstration of its efficacy? The answer is a qualified yes. The meta-analysis was carefully performed and yielded a within-group effect size of 0.96 (95% confidence interval [CI], 0.87-1.05) for pretreatment-postreatment overall outcomes, which would be considered a large effect.

Dear JAMA editorialist, you don’t use within-group effect sizes in meta-analyses and you shouldn’t use them to evaluate psychotherapies. Everyone knows that they uniformly inflate estimates of efficacy over more appropriate between-group effect sizes. Tsk, Tsk.

After the critical response to their JAMA article, Leichsenring and Rabung published a redoing of it in British Journal of Psychiatry. They justified this redundant publication as being an update. Actually, nine of the ten studies reviewed in the BJP article were included in the previous JAMA paper. The tenth study was irrelevant to the evaluation of LTPP versus other psychotherapies and, besides, its publication was early enough to be included in the JAMA review.

How did Leichsenring and Rabung get their terribly flawed article into JAMA with an accompanying editorial? How did such an overlapping article then get into BJP? A little help from friends?

Leichsenring and Rabung have just published another review in The Lancet Psychiatry. Its title suggests an echoing of the JAMA editorial’s Bambi meets Godzilla theme Psychodynamic therapy meets evidence-based medicine.

Leichsenring, F., Luyten, P., Hilsenroth, M. J., Abbass, A., Barber, J. P., Keefe, J. R., … & Steinert, C. (2015). Psychodynamic therapy meets evidence-based medicine: a systematic review using updated criteria. The Lancet Psychiatry, 2(7), 648-660.

The abstract suggests past problems have been overcome:

Psychodynamic therapy (PDT) is an umbrella concept for treatments that operate on an interpretive-supportive continuum and is frequently used in clinical practice. The use of any form of psychotherapy should be supported by sufficient evidence. Efficacy research has been neglected in PDT for a long time. In this review, we describe methodological requirements for proofs of efficacy and summarise the evidence for use of PDT to treat mental health disorders. After specifying the requirements for superiority, non-inferiority, and equivalence trials, we did a systematic search using the following criteria: randomised controlled trial of PDT; use of treatment manuals or manual-like guidelines; use of reliable and valid measures for diagnosis and outcome; adults treated for specific mental problems. We identified 64 randomised controlled trials that provide evidence for the efficacy of PDT in common mental health disorders. Studies sufficiently powered to test for equivalence to established treatments did not find substantial differences in efficacy. These results were corroborated by several meta-analyses that suggest PDT is as efficacious as treatments established in efficacy. More randomised controlled trials are needed for some mental health disorders such as obsessive-compulsive disorder and post-traumatic stress disorder. Furthermore, more adequately powered equivalence trials are needed.

PubMed CommonsBut, alas, post publication peer review to the rescue. The credibility of this article was demolished in a brief, but effective PubMed Commons commentary by Stefan G. Hofmann, Nora Esser, and Giovanbattista Andreoli.

The study by Leichsenring and colleagues highlights the importance of considering the quality of the studies that are included in a meta-analysis when evaluating the results. The Cochrane Collaboration’s Tool (Higgins et al., 2011) is a commonly-used instrument to quantify the risk of bias using the following criteria: allocation sequence concealment, blinding of participants and personnel, blinding of outcome assessment, incomplete outcome data, and selective outcome reporting. We analyzed the 64 randomized controlled trials of manual-guided PDT for specific mental disorders that were used in the review by Leichsenring et al (see Table 1). Thirty studies showed risk biases in sequence generation, 54 in allocation concealment, and 31 in the blinding conditions. Only one of the studies showed no obvious biases. Our results suggest that the studies included in Leichsenring’s meta-analysis were of poor quality, essentially invalidating the authors’ results and making the findings meaningless. Table 1: http://issuu.com/gvand/docs/quality_ratings_of_studies_in_leich/1 Table 2: http://issuu.com/gvand/docs/description_and_results_of_studies/1 References: Higgins, J.P., Altman, D.G., Gøtzsche, P.C., Jüni, P., Moher, D., Oxman, A.D., Savovic, J., Schulz, K.F., Weeks, L., Sterne, A.C., Cochrane Bias Methods Group, Cochrane Statistical Methods Group (2011). The Cochrane Collaboration´s tool for assessing risk of bias in randomised trials. RESEARCH METHODS & REPORTING, 343.)

We should always skeptical when authors clearly with a dog in the fight undertake systematic reviews and meta-analyses evaluating their favorite treatments. It’s best to get a couple of degrees of separation. A group that included John Ioannidis is provided such a review of LTPP. The results were not favorable:

The recovery rate of various mental disorders was equal after LTPP or various control treatments, including treatments without a specialized psychotherapy component. Similarly, no statistically significant differences were found for the domains target problems, general psychiatric problems, personality pathology, social functioning, overall effectiveness or quality of life.

And furthermore,

Control conditions were heterogeneous and frequently of low quality, e.g. without a specialized psychotherapy component. If anything, this suggests that LTPP is often compared against relatively ineffective “straw man” comparator… LTPP comparisons to specialized non-psychodynamic treatments, like dialectical behavior therapy and schema-focused therapy, suggest that LTPP might not be particularly effective.

 My past blog posts about Leichsenring and Rabung’s systematic reviews and meta analyses

Flawed, Biased Review Article in British Journal of Psychiatry. December 16, December 16, 2011

Is Long-Term Psychodynamic Psychotherapy Worthwhile?  January 14, 2012

Psychoanalysts claim long-term psychoanalytic psychotherapy more effective than shorter therapies.  February 4, 2014

Bambi meets Godzilla: Independent evaluation of the superiority of long-term psychodynamic therapy  May 24, 2014