Consistently poor coverage of mental health issues in The Guardian

Issuing a readers’ advisory: The Guardian provides misleading, badly skewed coverage of mental health issues vitally important to mental health service users.

Guardian PulitzerStories in The Guardian can confuse and disempower mental health service users seeking information for difficult decisions about choosing and sticking to treatments. Articles labeled Psychology and Health and sometimes Science don’t adhere to the quality that earned The Guardian a Pulitzer Prize.

In this issue of Mind the Brain, I show why there should be a formal readers advisory for mental health information appearing in The Guardian. The excellent watchdog of faulty health coverage in the media, NIH Choices: Behind the Headlines  should routinely monitor stories appearing in The Guardian and provide more balanced analyses.

NHS choices





You can compare my assessments to your own evaluation with the links I provide to the stories in The Guardian.

Some recent examples:

At last, a promising alternative to antipsychotics for schizophrenia

Imagine that, after feeling unwell for a while, you visit your GP. “Ah,” says the doctor decisively, “what you need is medication X. It’s often pretty effective, though there can be side-effects. You may gain weight. Or feel drowsy. And you may develop tremors reminiscent of Parkinson’s disease.” Warily, you glance at the prescription on the doctor’s desk, but she hasn’t finished. “Some patients find that sex becomes a problem. Diabetes and heart problems are a risk. And in the long term the drug may actually shrink your brain.”

It is insulting to those who suffer from schizophrenia to have their life-altering experience trivialized and domesticated as simply “feeling unwell for a while.”

The article provides a fright-mongering depiction of the difficult choice that patients with schizophrenia face. Let’s give a critical look at the authors’ claim about drugs shrinking the brain. The sole citation is a PLOS One article. Authors of that article provided a carefully worded press release:

A study published today has confirmed a link between antipsychotic medication and a slight, but measureable, decrease in brain volume in patients with schizophrenia. For the first time, researchers have been able to examine whether this decrease is harmful for patients’ cognitive function and symptoms, and noted that over a nine year follow-up, this decrease did not appear to have any effect.

The UK senior author of the study further clarified:

doesn't appear





The study is not a randomized trial in which the amount of antipsychotic medication that patients received was manipulated. It is a small observational study comparing 33 patients with schizophrenia to 71 controls. Causal interpretation depends on statistical manipulation of correlational data. Yet a group of only 33 (!) patients with schizophrenia does not allow reliable multivariate analysis to explore alternative interpretations of the data. One plausible interpretation is that the amount of medication particular patients received is tied to severity of course of their schizophrenia. This would be a classic example of confounding by indication. The authors acknowledge this possibility:

It is conceivable that patients with the most severe illness lose more brain volume over time, reflecting intrinsic aspects of the pathology of schizophrenia, and the fact that severely ill patients receive higher doses of medication.

They further note:

Whilst it is extremely important to determine the causes of loss of brain volume in schizophrenia, an equally important question concerns its clinical significance. Loss of brain volume occurs throughout the majority of adult life in the healthy population, and whilst it might seem trivial that this would be disadvantageous, in some periods of development loss of brain tissue appears to be potentially beneficial [43]*.

Yes, antipsychotic medication poses serious side effects, doesn’t cure schizophrenia, and there are problems with adherence. But The Guardian article fails to note that the longer an episode of schizophrenia goes untreated, the less likelihood that a patient will ever resume a semblance of a normal life. And schizophrenia is associated with a 10% rate of suicide. What alternative does The Guardian article suggest?

A team led by Professor Anthony Morrison at the University of Manchester randomly assigned a group of patients, all of whom had opted not to take antipsychotics, to treatment as usual (involving a range of non-pharmaceutical care) or to treatment as usual plus a course of cognitive therapy (CT). Drop-out rates for the cognitive therapy were low, while its efficacy in reducing the symptoms of psychosis was comparable to what medication can achieve.

You can compare this summary to my critiques [1,2].

  • “Drop out rates..,were low?” The study retained fewer participants receiving cognitive therapy at the end of the study than there were authors.
  • The comparison treatment was ill-defined, but for some patients meant no treatment because they were kicked out of routine care for refusing medication.
  • A substantial proportion of patients assigned to cognitive therapy began taking antipsychotic medication by the end of the study.
  • There was no evidence that the response to cognitive therapy was comparable to that achieved with antipsychotic medication alone in clinical trials.

The authors of the study backed down from this last claim in an exchange of letters [1 and 2] at the Lancet with myself and others. BBC News dropped that claim after initially making it in coverage of the study.

as effective




moderately effective



Don’t settle for my interpretation of the literature concerning cognitive therapy for psychosis (CBTp), go to a summary of available evidence in a blog post by Clive Adams, Chair of Mental Health Services Research and Co-Ordinating Editor of the Cochrane Schizophrenia Group at the University of Nottingham.

Adams wraps up with

Where does this leave CBTp?

In the opinion of this writer, having read and thought about the reviews (and others in some detail) it is time to move on.

It is great that there are data for questions around this potentially potent intervention for people with schizophrenia (for many treatments there are no data at all). I just cannot see that this approach (CBTp), on average, is reaping enough benefits for people.

Adams cites

Jones C, Hacker D, Cormac I, Meaden A, Irving CB. Cognitive behavioural therapy versus other psychosocial treatments for schizophrenia. Cochrane Database of Systematic Reviews 2012, Issue 4. Art. No.: CD008712.

Which concludes

Trial-based evidence suggests no clear and convincing advantage for cognitive behavioural therapy over other – and sometime much less sophisticated – therapies for people with schizophrenia.

Mark Taylor chaired the Scottish Intercollegiate Guidelines Network (SIGN) committee that produced the Scottish Guidelines for the Management of Schizophrenia. SIGN is the equivalent to the British National Initiative for Clinical Excellence (NICE). In an editorial in British Journal of Psychiatry he commented on the NICE guidelines’ favoring of cognitive behavioral therapy:

NICE has also taken the bold step of recommending CBT and family therapy alone for people with first-episode psychosis who wish it. The guideline acknowledges that psychosocial interventions are more effective in conjunction with antipsychotic medication, but still suggests this intervention alone for one month or less. This is controversial in view of the lack of robust supportive evidence and could potentially worsen outcomes. A related point is that in the guideline NICE seem oblivious to the fact that many patients with acute schizophrenia have impaired insight into their illness and health needs,5 and thus may not have capacity to consent to their treatment.

And finally, there is a Keith Laws’ carefully documented Science & Politics of CBT for Psychosis.

A Guardian story on mindfulness: New study shows mindfulness therapy can be as effective as antidepressants

Glass half-full readers, of course, will see that the trial results demonstrate that we actually have two similarly effective treatment options for recurrent depression: one involves eight weeks of a psychological therapy, the other relies on taking medication for two years. The challenge now is to make both equally available in treatment services.

I provided a detailed critique of this study. You would never guess from The Guardian article that mindfulness therapy used in this study was not designed to treat depression, only to prevent relapse in patients who had recovered in treatment by other means. And there was no assessment of whether patients assigned maintenance antidepressants were actually adhering to them or receiving adequate, guideline congruent care. You can see my comments on this study at PubMed Commons and leave your own as well.

The lead author of the study who is a colleague of the author of The Guardian went to the trouble of modifying the study registration to clarify that the trial was not designed to compare mindfulness therapy antidepressants for depression.

Feeling paranoid? Your worries are justified but can be helped

In this article The Guardian authors present as mainstream their unconventional views of what “feeling paranoid” represents. One of the authors promotes his own treatment for which he conducts workshops tied to his self-help books about worrying.

The fog machine gets going when the authors merge colloquial use of paranoid with the psychotic symptom. Many people, especially the young use “paranoid” in every speech in a way far removed from professionals discussing the psychotic symptom. Most endorsements of “feeling paranoid” on a checklist would not represent a psychiatric symptom. Even when present, the psychiatric symptom of paranoid is neither necessary nor sufficient for a diagnosis of schizophrenia.

When occurring in the context of a diagnosis of schizophrenia, however, paranoid delusions can be strongly held convictions accompanied by other lack of insight and thought disorder. I know of no evidence that everyday suspiciousness turns into psychotic persecutory delusions in persons who are not otherwise at risk for psychosis.

Think of someone insisting on shifting a conversation about skin cancer to talking about moles. Dropping lung cancer and chronic obstructive pulmonary disease for a more inclusive, but nonspecific “cough.” These are silly moves in a language game that prevent evaluation of health problems in terms of available evidence of necessity tied to more precise language.

The Guardian authors propose:

As we’ve noted previously on Guardian Science, anti-psychotics don’t work for everyone. And their side effects can be so unpleasant that many people refuse to take them. Moreover, there’s compelling evidence to suggest that the concept of “schizophrenia” doesn’t stand up scientifically, operating instead as a catch-all for a variety of distinct and frequently unrelated experiences.

What compelling evidence? Says who? I doubt that the one of these authors who is in the Psychology at Oxford would make such a statement in a formal presentation to his colleagues. But apparently it suffices for a lay audience including mental health services users seeking information about their condition and available treatments.

In general, readers should beware of authors making such sweeping statements in the media without identifying specific sources, degree of scientific consensus, or grade of evidence. The Guardian authors require readers to turn off critical skills and trust them.

This is why scientists have increasingly focused on understanding and treating those experiences in their own right, rather than assuming they’re simply symptoms of some single (albeit nebulous) underlying illness. So what have we discovered by applying this approach to paranoia?

Which “scientists”? Where? Readers are again left trusting the expertise of The Guardian authors.

The authors are getting set to promote the treatment developed by one them for “worry” in patients with paranoid delusions, which is marketed in his workshops, using his self-help book. I previously reviewed this study in detail.

I concluded

  • The treatment was a low intensity variation of a self-help exercise using excerpts from The Guardian authors’ book.
  • The treatment of the control group was ill-defined routine care. Relying on this control group as the only comparison precluded evaluating whether the intervention was any better than a non-branded similar amount of attention and support.
  • The primary outcome was hopelessly confounded with nonspecific worrying or anxiety and inadequate to assess clinically significant changes in psychotic symptoms of paranoid delusions.

I could go on with examples from other articles in The Guardian. But I think these suffice to establish that mental health service users seeking reliable information can find themselves misled by stories in The Guardian. Readers who don’t have the time or feel up to the task of checking out what they read against what is available in the literature would do well to simply ignore what is said in The Guardian about serious mental disorder and its treatment.

insect parts-page-0Readers advisory

Despite The Guardian having won the Pulitzer Prize for science reporting, readers may find stories about mental health that are seriously misleading and of little use in making choices about mental health problems and treatments. Information about these issues are not responsibly vetted or fact checked.

Whatever happened to responsible journalism at The Guardian?

in April 2015,The Guardian announced a Live Question and Answer Session.

How can academics help science reporters get their facts straight?

Academics have never been under more pressure to engage with the public and show the impact of their work. But there’s a problem. The media, one of the key channels for communicating with people outside academia, has a reputation for skewing or clumsily confusing scientific reports.

The session was in response to larger concerns about the accuracy of health and science journalism. With serious cutbacks in funding and layoffs of experienced professional journalists, the media increasingly rely upon copy/pasting exaggerated and inaccurate press releases generated by self-promoting researchers in the universities. What has been lost is the important filter function by which journalists offer independent evaluation of what they are fed by researchers’ public relations machines.

Many readers of The Guardian probably did notice a profound shift from reliance on professional journalists to to blogging provided free by academics. Accessing a link to The Guardian provided by a Google Search or Twitter, readers are given no indication that they will be reading a blog.

A blog post last year by Alastair Taylor identified the dilemma –

Media outlets, such as the Guardian Science Blogs, can present the science direct (and without paying for it) from the experts themselves. Blogging also opens up the potential for the democratisation of science through online debates, and challenges established hierarchies through open access and public peer review. At the same time, can scientists themselves offer the needed reflection on their research that an investigative journalist might do?

In the case of these  authors appearing in The Guardian, apparently not.

The new system has obvious strengths. I look forward to reading regular blog posts by academic sources who have proved trustworthy such as Suzi Gage, Chris Chambers, or many others. They have earned my trust sufficiently for me to recommend them. But unfortunately, appearing in The Guardian no longer necessarily indicates that stories are scientificially accurate and helpful to consumers. We must suspend our trust in The Guardian and be skeptical when encountering stories there about mental health.

I sincerely hope that this situation changes.


*The authors of the PLOS One article cite a Nature article for this point, which states

More intelligent children demonstrate a particularly plastic cortex, with an initial accelerated and prolonged phase of cortical increase, which yields to equally vigorous cortical thinning by early adolescence. This study indicates that the neuroanatomical expression of intelligence in children is dynamic [bolding added].


Category: antipsychotics, Cochrane Collaboration, cognitive behavioral therapy, evidence-supported, mental health care, National Institute for Health and Care Excellence, Psychiatry, psychosis, psychotherapy, schizophrenia | Tagged , , , , | Leave a comment

Developments in the Treatment of PTSD Nightmares

What Dreams May Come: Treating the Nightmares of PTSD” was a blog post I published in November 2013. It remains a very popular post, which continues to receive many views and comments. Since publishing that post, I have received multiple questions from readers about treatments for nightmares. These queries reinforce, for me, just how distressing this symptom of nightmares is for individuals who live with PTSD.

In light of this, on 5/22/2015 I interviewed Dr. Murray Raskind about his pioneering work in the field of PTSD and the treatment of nightmares.

Murray A. Raskind, MD, is Director of the VA Northwest Network Mental Illness Research, Education and Clinical Center (MIRECC). He is also Professor and Vice-Chairman in the Department of Psychiatry and Behavioral Sciences at the University of Washington School of Medicine and Director of the University of Washington Alzheimer’s Disease Research Center.

In the late 1990’s, Dr. Raskind pioneered the use of prazosin for nightmares, by giving it to some of his veteran patients with PTSD. What started as clinical innovation eventually morphed into an important research question, and in 2013 Dr. Raskind and his group reported on an encouraging scientific development. They conducted a fifteen week randomized controlled trial of prazosin that involved sixty-seven active duty soldiers with PTSD. The medicine was titrated up based on the participant nightmare response over a period of six weeks. Prazosin was found to be effective in improving PTSD nightmares and sleep quality in two thirds of the sample. It was also associated with the study participants reporting a reduction in PTSD symptoms and an improvement in their overall global functioning.


I started my interview by asking Dr. Raskind about any other scientific findings that have emerged from that trial since his 2013 publication.




Dr. Raskind: We did an interesting secondary analysis, which we are writing up for publication now, of that sample of 60 or so active duty Iraq/Afghanistan soldiers with PTSD. When we analyze the response to prazosin, prazosin worked a lot better than placebo, but not in everybody. Approximately 2/3 of the soldiers were moderately improved globally, but there were 1/3 who just did not respond even though there were no differences in their symptom severity as measured by the CAPS (The Clinician-Administered PTSD Scale). With just looking at the psychiatric symptomatology, we really could not differentiate why one person would respond and another would not. We started thinking about it and we thought it would be nice to know something about the level of activation in the brain of the alpha 1 receptor for norepinephrine, which is the target of . (Prazosin is an alpha 1 norepinephrine receptor blocker or antagonist.)

We were thinking maybe you had to have a lot of alpha 1 receptor stimulation by norepinephrine to be a responder and maybe there are different underlying biologies to the PTSD symptoms. Unfortunately, there is no way, using imaging technology or anything else, to directly measure the alpha 1 receptor for norepinephrine. But it occurred to me, having been interested in effects on blood pressure of norepinephrine, that the central norepinephrine system and the peripheral sympathetic nervous system, which uses norepinephrine as its neurotransmitter, are often co-regulated. Blood pressure particularly is affected strongly by stimulation of the alpha 1 receptor on the arterial blood vessels that regulate blood pressure.

We hypothesized that soldiers with PTSD who have higher standing systolic blood pressure would have a better response to prazosin than the ones with lower baseline standing systolic blood pressure. We did this before we started them on prazosin, because we were looking for a biomarker of response to prazosin or a predictor of response to prazosin. We just did a straight forward statistical analysis and, lo and behold, the prediction was strongly supported by the data. These are young men and their mean age is 29 and they were in good shape, because they were still in the army, so they have to keep physically fit. We did not have people with a systolic of 180, but if you just compare it, in the statistical model, a person who had a slightly elevated systolic blood pressure of 130, those folks have a big prazosin response. A big improvement. Whereas if you have a baseline standing systolic of 110, your response to prazosin did not differ at all from placebo.


Dr. Jain: So you are starting to paint a profile of what kind of patient would respond well to prazosin?


Dr. Raskind: Right, which goes to our clinical experience….I often get referred the most agitated, aggravated, and upset combat veterans with PTSD who are having sleep disruption. When they wake up from a nightmare, or even without a nightmare, the bed is wet from sweat and their heart is racing and they cannot get back to sleep. During the day they are hyper vigilant and irritable. The ones I see, the ones who are good prazosin responders, almost always have some degree of elevated blood pressure. When someone comes in to my office with the same clinical picture but their blood pressure is below normal, I say, “I do not think that prazosin is going to work particularly well for this veteran.” I made that observation clinically, but I did not know whether it was valid until we did the study. It is actually sort of exciting. We have to do it prospectively, but I think it will hold up. Even without measuring blood pressures, other indications of increased sympathetic arousal such as sweating when you wake up at night or during sleep is another factor that I think would be a good biomarker, but it is not so easy to quantify.


Dr. Jain: That is pretty exciting, because, as far as I know, when we look at medications for PTSD, I do not think we have other biological predictors of response.


Dr. Raskind: Right. We do not. That is correct. We presented the data at two places so far. At this year’s Biological Psychiatry meeting and also at ACNP (American College of Neuropsychopharmacology) last December.


Dr. Jain: How do you see prazosin being used in the clinical setting 5-10 years from now?


Dr. Raskind: Well, I think that I would like to see it being used for people in whom there is a good chance that it would work. It’s not for everybody. Fortunately, it is a pretty easy medication to tolerate and the side effects are relatively uncommon, provided that you start at a low dose and titrate it upwards. The titration should be based both on the target symptoms going away and if there are any adverse effects on blood pressure. Usually, adverse effects are relatively uncommon. The major problem with prazosin is that providers don’t titrate to a high enough dose. If you look nationally, there are about 100,000 veterans with a PTSD diagnosis in the VA who, last year, were prescribed prazosin. About, one out of six. But the downside is that the mean dose is about 4 milligrams.


Dr. Jain: Is that sub-therapeutic in your mind?


Dr. Raskind: It works for some people, but some people need more. They also often need smaller daytime doses. Either one in the mid-morning and another one at around mid-afternoon somewhere, in addition to the night time dose, because prazosin only has a duration of action of about 6-8 hours. There is no magic number of milligrams. In the 2013 study, we titrated it up to a maximum dose of 20 milligrams at night and 5 milligrams mid-morning. You could go that high. Rules were you titrate it up until all nightmares were gone in the previous week. It took a lot of prazosin. We got up to about a little over 15 milligrams at night and about 4 milligrams mid-morning until we reach that criterion. That suggests that 4 milligrams is too low. On the other hand, some people get better with 2 milligrams. Sleeping great and nightmares are gone. That is the dose for them.


Dr. Jain: It sounds like you would like to see prazosin used in a more tailored fashion in people who have a profile which suggests it is more likely to work for them.


Dr. Raskind: Exactly. There are other disorders for which it appears that prazosin will also play a therapeutic role.


Dr. Jain: Like what?


Dr. Raskind: Well, there are three. The first is alcohol use disorder. Second is post mild traumatic brain injury or post-concussion migraine headache. The third is agitation aggression in Alzheimer’s disease and probably dementia in general.


Dr. Jain: Alright. Other than prazosin, what else do you like to use for nightmares? Are there any other things you have come across that you are particularly impressed by, non-pharmacological as well as pharmacological?


Dr. Raskind: The literature on nightmare psychotherapy is mostly from civilian trauma populations. I don’t know how well it translates over to (veterans)… There are specific nightmare psychotherapies, that I am frankly not terribly familiar with, e.g. imagery rehearsal. Changing the nature of the dream while you are awake and then seeing if that helps. Again, it helps in civilian trauma populations. The nice thing about psychotherapy, in my opinion, is if it is done well with a compassionate and interested person, they all work to some degree and their side effects are pretty low. In general, the psychotherapy along with rational pharmacotherapies is probably the way to go.


Dr. Jain: Please offer your perspectives re: clinical innovation in the 21st century? Is it harder for today’s physicians to innovate at the bedside? (too much regulation, oversight, paperwork, legal implications)


Dr. Raskind: And these guidelines, which are really, mostly, guesses.


Dr. Jain: You mean the clinical practice guidelines?


Dr. Raskind: Right. If you do not follow them, people worry that they are going to be called on it and I have seen it happen. The prazosin thing—what happened there was I was working with this Vietnam veterans group in 1995. From their descriptions of their symptoms it was clear that they were having an adrenaline storm at night. So I said, “What do people use to calm excess norepinephrine in the brain?” Block the beta receptor with propranolol! (It has been used for social anxiety, public speaking anxiety, or for performers who get nervous about a performance.) So I gave my first veteran propranolol—I was pretty safe in doing that because he had some hypertension too. He came in and said, “I am getting worse. My nightmares are even more intense.” I looked at the PDR and saw that Beta blockers do intensify dreams!

I did know, from some of the neuroendocrine work that I have been doing in Alzheimer’s, that the beta receptor for norepinephrine and the alpha 1 receptor sometimes had opposite effects, when stimulated or blocked, on various neuroendocrine systems. So I said, “Well if he is getting worse by blocking the beta receptor, maybe he will get better if I block the alpha 1 receptors.” I looked at the available alpha 1 receptor antagonists. Prazosin was the only one that had reasonable penetrance into the brain by its lipid solubility. So I said, “Let’s try prazosin.” The veteran gets better. He got better and dramatically improved. The second one dramatically improved too.


Dr. Jain: That’s a great story. That happened in 1995, do you see that happening nowadays?


Dr. Raskind: I think it can, if people have open minds. We are not going to change the bureaucratic system, but we need to be observing things rather than saying, “This expert says this and this one says that.” I mean, though it is all well and good and we have studies which demonstrate this and that, it is very important for us to remember our experience with the individual patient. What we thought, a guess of what might help and if we have some rational for doing it. People are so afraid to deviate from what someone says is the right thing to do that it (clinical innovation) may be happening less and less.


Dr. Jain: Yes. Keeping an open mind and, like you said, focusing on the individual patient experience.


Dr. Raskind: And talking to your colleagues. Anyway, I agree with you that we are tending to under appreciate the ability of clinical observation to give us productive leads in drug development.

Category: mental health care, Psychiatry, PTSD, research | Tagged , , , | Leave a comment

Is mindfulness-based therapy ready for rollout to prevent relapse and recurrence in depression?

Doubts that much of clinical or policy significance was learned from a recent study published in Lancet

Dog-MindfulnessPromoters of Acceptance and Commitment Therapy (ACT) notoriously established a record for academics endorsing a psychotherapy as better than alternatives, in the absence of evidence from adequately sized, high quality studies with suitable active control/comparison conditions. The credibility of designating a psychological interventions as “evidence-based” took a serious hit with the promotion of ACT, before its enthusiasts felt they attracted enough adherents to be able to abandon claims of “best” or “better than.”

But the tsunami of mindfulness promotion has surpassed anything ACT ever produced, and still with insufficient quality and quantity of evidence.

Could that be changing?

Some might think so with a recent randomized controlled trial reported in the Lancet of mindfulness-based cognitive therapy (MBCT) to reduce relapse and recurrence in depression. The headline of a Guardian column  by one of the Lancet article’s first author’s colleagues at Oxford misleadingly proclaimed that the study showed

freeman promoAnd that misrepresentation was echoed in the Mental Health Foundation call for mindfulness to be offered through the UK National Health Service –

calls for NHS mindfulnessThe Mental Health Foundation is offering a 10-session online course  for £60 and is undoubtedly prepared for an expanded market.


Patient testimonial accompanying Mental Health Foundation’s call for dissemination.




The Declaration of Conflict of Interest for the Lancet article mentions the first author and one other are “co-directors of the Mindfulness Network Community Interest Company and teach nationally and internationally on MBCT.” The first author notes the marketing potential of his study in comments to the media.

revising NICETo the authors’ credit, they modified the registration of their trial to reduce the likelihood of it being misinterpreted.

Reworded research question. To ensure that readers clearly understand that this trial is not a direct comparison between antidepressant medication (ADM) and Mindfulness-based cognitive therapy (MBCT), but ADM versus MBCT plus tapering support (MBCT-TS), the primary research question has been changed following the recommendation made by the Trial Steering Committee at their meeting on 24 June 2013. The revised primary research question now reads as follows: ‘Is MBCT with support to taper/discontinue antidepressant medication (MBCT-TS) superior to maintenance antidepressant medication (m-ADM) in preventing depression over 24 months?’ In addition, the acronym MBCT-TS will be used to emphasise this aspect of the intervention.

1792c904fbbe91e81ceefdd510d46304I would agree and amplify: This trial adds nothing to  the paucity of evidence from well-controlled trials that MBCT is a first-line treatment for patients experiencing a current episode of major depression. The few studies to date are small and of poor quality and are insufficient to recommend MBCT as a first line treatment of major depression.

I know, you would never guess that from promotions of MBCT for depression, especially not in the current blitz promotion in the UK.

The most salient question is whether MBCT can provide an effective means of preventing relapse in depressed patients who have already achieved remission and seek discontinuation.

Despite a chorus of claims in the social media to the contrary, the Lancet trial does not demonstrate that

  • Formal psychotherapy is needed to prevent relapse and recurrence among patients previously treated with antidepressants in primary care.
  • Any less benefit would have been achieved with a depression care manager who requires less formal training than a MBCT therapist.
  • Any less benefit would have been achieved with primary care physicians simply tapering antidepressant treatment that may not even have been appropriate in the first place.
  • The crucial benefit to patients being assigned to the MBCT condition was their acquisition of skills.
  • That practicing mindfulness is needed or even helpful in tapering from antidepressants.

We are all dodos and everyone gets a prize

dodosSomething also lost in the promotion of the trial is that it was originally designed to test the hypothesis that MBCT was better than maintenance antidepressant therapy in terms of relapse and recurrence of depression. That is stated in the registration of the trial, but not in the actual Lancet report of the trial outcome.

Across the primary and secondary outcome measures, the trial failed to demonstrate that MBCT was superior. Essentially the investigators had a null trial on their hands. But in a triumph of marketing over accurate reporting of a clinical trial, they shifted the question to whether MBCT is inferior to maintenance antidepressant therapy and declared the success demonstrating that it was not.

We saw a similar move in a MBCT trial  that I critiqued just recently. The authors here opted for the noninformative conclusion that MBCT was “not inferior” to an ill-defined routine primary care for a mixed sample of patients with depression and anxiety and adjustment disorders.

An important distinction is being lost here. Null findings in a clinical trial with a sample size set to answer the question whether one treatment is better than another is not the same as demonstrating that the two treatments are equivalent. The latter question requires a non-inferiority design with a much larger sample size in order to demonstrate that by some pre-specified criteria two treatments do not differ from each other in clinically significant terms.

Consider this analogy: we want to test whether yogurt is better than aspirin for a headache. So we do a power analysis tailored to the null hypothesis of no difference between yogurt and aspirin, conduct a trial, and find that yogurt and aspirin do not differ. But if we were actually interested in the question whether yogurt can be substituted for aspirin in treating headaches, we would have to estimate what size of a study would leave us comfortable with that conclusion the treating aspirin with yogurt versus aspirin makes no clinically significant difference. That would require a much larger sample size, typically several times the size of a clinical trial designed to test the efficacy of an intervention.

The often confusing differences between standard efficacy trials and noninferiority and superiority trials are nicely explained here.

Do primary care patients prescribed an antidepressant need to continue?

Patients taking antidepressants should not stop without consulting their physician and agreeing on a plan for discontinuation.

NICE Guidelines, like many international guidelines, recommend that patients with recurrent depression continue their medication for at least two years, out of concerned for a heightened risk of relapse and recurrence. But these recommendations are based on research in specialty mental health settings conducted with patients with an established diagnosis of depression. The generalization to primary care patients may not be appropriate best evidence.

Major depression is typically a recurrent, episodic condition with onset in the teens or early 20s. Many currently adult depressed patients beyond that age would be characterized as having a recurrent depression. In a study conducted at primary care practices associated with the University of Michigan, we found that most patients in waiting rooms identified as depressed on the basis of a two stage screening and formal diagnostic interview had recurrent depression, with the average patient having over six episodes before our point of contact.

However, depression in primary care may have less severe symptoms in a given episode and an overall less severe course then the patients who make it to specialty mental health care. And primary care physicians’ decisions about placing patients on antidepressants in primary care are typically not based upon a formal, semi structured interview in which there are symptom counts to ascertain whether patients have the necessary number of symptoms (5 for the Diagnostic and Statistical Manual-5) to meet diagnostic criteria.

My colleagues in Germany and I conducted another relevant study in which we randomized patients to either antidepressant, behavior therapy, or the patient preference of antidepressant versus behavior therapy. However, what was unusual was that we relied on primary care physician diagnosis, not our formal research criteria. We found that many patients enrolling in the trial would not meet criteria for major depression and, at least by DSM-IV-R criteria, would be given the highly ambiguous diagnosis of Depression, Not Otherwise Specified. The patients identified by the primary care physicians as requiring treatment for depression were quite different than those typically entering clinical trials evaluating treatment options. You can find out more about the trial here .

It is thus important to note that patients in the Lancet study were not originally prescribed antidepressants based on a formal, research diagnosis of major depression. Rather, the decisions of primary care physicians to prescribe the antidepressants, are not usually based on a systematic interview aimed at a formal diagnosis based on a minimal number of symptoms being present. This is a key issue.

The inclusion criteria for the Lancet study were that patients currently be in full or partial remission from a recent episode of depression and have had at least three episodes, counting the recent one. But their diagnosis at the time they were prescribed antidepressants was retrospectively reconstructed and may have biased by them having received antidepressants

Patients enrolled in the study were thus a highly select subsample of all patients receiving antidepressants in the UK primary care. A complex recruitment procedure involving not only review of GP records, but advertisement in the community means that we cannot tell what the overall proportion of patients receiving antidepressants and otherwise meeting criteria would have agreed to be in the study.

The study definitely does not provide a basis for revising guidelines for determining when and if primary care physicians should raise the issue of tapering antidepressant treatment. But that’s a vitally important clinical question.

skeptical-cat-is-fraught-with-skepticismQuestions not answered by the study:

  • We don’t know the appropriateness of the prescription of antidepressants to these patients in the first place.
  • We don’t know what review of the appropriateness of prescription of antidepressants had been conducted by the primary care physicians in agreeing that their patients participate in the study.
  • We don’t know the selectivity with which primary care physicians agreed for their patients to participate. To what extent are the patients to whom they recommended the trial representative of other patients in the maintenance phase of treatment?
  • We don’t know enough about how the primary care physicians treating the patients in the control groups reacted to the advice from the investigator group to continue medication. Importantly, how often were there meetings with these patients and did that change as a result of participation in this trial? Like every other trial of CBT in the UK that I have reviewed, this one suffers from an ill defined control group that was nonequivalent in terms of the contact time with professionals and support.
  • The question persists whether any benefits claimed for cognitive behavior therapy or MBCT from recent UK trials could have been achieved with nonspecific supportive interventions. In this particular Lancet study, we don’t know whether the same results could been achieved by simply tapering antidepressants assisted by a depression care manager less credentialed than what is required to provide MBCT.

The investigators provided a cost analysis. They concluded that there were no savings in health care costs of moving patients in full or partial remission off antidepressants to MBCT. But the cost analysis did not take into account the added patient time invested in practicing MBCT. Indeed, we don’t even know whether the patients assigned to MBCT actually practiced it with any diligence or will continue to do after treatment.

The authors promise a process analysis that will shed light on what element of MBCT contributed to the equivalency of outcomes with the maintenance of antidepressant medication.

But this process analysis will be severely limited by the inability to control for nonspecific factors such as contact time with the patient and support provided to the primary care physician and patient in tapering medication.

The authors seem intent on arguing that MBCT should be disseminated into the UK National Health Services. But a more sober assessment is that this trial only demonstrates that a highly select group of patients currently receiving antidepressants within the UK health system could be tapered without heightened risk of relapse and recurrence. There may be no necessity or benefit of providing MBCT per se during this process.

The study is not comparable to other noteworthy studies of MBCT to prevent remission, like Zindel Segal’s complex study . That study started with an acutely depressed patient population defined by careful criteria and treated patients with a well-defined algorithm for choosing and making changes in medications. Randomization to continued medication, MBCT, or pill placebo occurred on in the patients who remitted. It is unclear how much the clinical characteristics of the patients in the present Lancet study overlapped with those in Segal’s study.

What would be the consequences of disseminating and implementing MBCT into routine care based on current levels of evidence?

There are lots of unanswered questions concerning whether MBCT should be disseminated and widely implemented in routine care for depression.

One issue is where would the resources come from for this initiative? There already are long waiting list for cognitive behavior therapy, generally 18 weeks. Would disseminating MBCT draw therapists away from providing conventional cognitive behavior therapy? Therapists are often drawn to therapies based on their novelty and initial, unsubstantiated promises rather than strength of evidence. And the strength of evidence for MBCT is not such that we could recommend substituting it for CBT for treatment of acute, current major depression.

Another issue is whether most patients would be willing to commit not only the time for sessions of training and MBCT but to actually practicing it in their everyday life. Of course, again, we don’t even know from this trial whether actually practicing MBCT matters.

There hasn’t been a fair comparison of MBCT to equivalent time with a depression manager who would review patients currently receiving antidepressants and advise physicians has to whether and how to taper suitable candidates for discontinuation.

If I were distributing scarce resources to research to reduce unnecessary treatment with antidepressants, I would focus on a descriptive, observational study of the clinical status of patients currently receiving antidepressants, the amount of contact time their receiving with some primary health care professional, and the adequacy of their response in terms of symptom levels, but also adherence. Results could establish the usefulness of targeting long term use of antidepressants and the level of adherence of patients to taking the medication and to physicians monitoring their symptom levels and adherence. I bet there is a lot of poor quality maintenance care for depression in the community

When I was conducting NIMH-funded studies of depression in primary care, I never could get review committees interested in the issue of overtreatment and unnecessarily continued treatment. I recall one reviewer’s snotty comment that that these are not pressing public health issues.

That’s too bad, because I think they are key in considering how to distribute scarce resources to study and improve care for depression in the community. Existing evidence suggest a substantial cost of treatment of depression with antidepressants in general medical care is squandered on patients who do not meet guideline criteria for receiving antidepressants or who do not receive adequate monitoring.

Category: antidepressants, depression, mindfulness, National Institute for Health and Care Excellence, primary care, psychotherapy, treatment as usual | Tagged , , , | 8 Comments

Delusional? Trial in Lancet Psychiatry claims brief CBT reduces paranoid delusions

lancet psychiatryIn this issue of Mind the Brain, I demonstrate a quick assessment of the conduct and reporting of a clinical trial.  The authors claimed in Lancet Psychiatry a “first ever” in targeting “worries” with brief cognitive therapy as a way of reducing persistent persecutory delusions in psychotic persons. A Guardian article written by the first author claims effects were equivalent to what is obtained with antipsychotic medication. Lancet Psychiatry allowed the authors a sidebar to their article presenting glowing testimonials of 3 patients making extraordinary gains. Oxford University lent its branding* to the first author’s workshop promoted with a video announcing a status of “evidence-based” for the treatment.

There is much claiming to be new here. Is it a breakthrough in treatment of psychosis and in standards for reporting a clinical trial? Or is what is new not praiseworthy?

I identify the kinds of things that I sought in first evaluating the Lancet Psychiatry article and what additional information needed to be consulted to assess the contribution to the field and relevance to practice.

The article is available open access.

Its publication was coordinated with the first author’s extraordinarily self-promotional elarticle in The Guardian

The Guardian article makes the claim that

benefits were what scientists call “moderate” – not a magic bullet, but with meaningful effects nonetheless – and are comparable with what’s seen with many anti-psychotic medications.

The advertisement for the workshop is here


The Lancet Psychiatry article also cites the author’s self-help book for lay persons. There was no conflict of interest declared.

Probing the article’s Introduction

Reports of clinical trials should be grounded in a systematic review of the existing literature. This allows readers to place the study in the context of existing research and the unsolved clinical and research problems the literature poses. This background prepares the reader to evaluate the contribution the particular trial can make.

Just by examining the references for the introduction, we can find signs of a very skewed presentation.

The introduction cites 13 articles, 10 of which are written by the author and an eleventh is written by a close associate. The remaining 2 citations are more generic, to a book and an article about causality.

Either the author is at the world center of this kind of research or seriously deficient in his attention to the larger body of evidence. At the outset, the author announces a bold reconceptualization of the role of worry in causing psychotic symptoms:

Worry is an expectation of the worst happening. It consists of repeated negative thoughts about potential adverse outcomes, and is a psychological component of anxiety. Worry brings implausible ideas to mind, keeps them there, and increases the level of distress. Therefore we have postulated that worry is a causal factor in the development and maintenance of persecutory delusions, and have tested this theory in several studies.

This is controversial, to say the least. The everyday experience of worrying is being linked to persecutory delusions. A simple continuum seems to be proposed – people can start off with everyday worrying and end out with a psychotic delusion and twenty years of receiving psychiatric services. Isn’t this too simplistic or just plain wrong?

Has no one but the author done relevant work or even reacted to the author’s work? The citations provided in the introduction suggest the author’s work is all we need in order to interpret this study in the larger context of what is known about psychotic persecutory delusions.

Contrast my assessment with the author’s own:

Panel 2: Research in context
Systematic review We searched the ISRCTN trial registry and the PubMed database with the search terms “worry”,“delusions”. “persecutory”,“paranoia”,and “schizophrenia”without date restrictions, for English-language publications of randomised controlled trials investigating the treatment of worry in patients with persecutory delusions. Other than our pilot investigation12 there were no other such clinical trials in the medical literature. We also examined published meta-analyses on standard cognitive behavioural therapy (CBT) for persistent delusions or hallucinations, or both.

The problem is that “worry” is a nonspecific colloquial term, not a widely used scientific one. For the author to require that studies have “worry” as a keyword in order to be retrieved is a silly restriction.

PubMedI welcome readers to redo the PubMed search dropping this term. Next replace “worry” with “anxiety.” Furthermore, the author makes unsubstantiated assumptions about a causal role for worry/anxiety in development of delusions. Drop the “randomized controlled trial” restriction from the PubMed search and you find a large relevant literature. Persons with schizophrenia and persecutory delusions are widely acknowledged to be anxious. But you won’t find much suggestion in this literature that the anxiety is causal or that people progress from worrying about something to developing schizophrenia and persecutory delusions. This seems a radical version gone wild of the idea that normal and psychotic experiences are on a continuum, concocted with a careful avoidance of contrary evidence.

Critical appraisal of clinical trials often skips examination of whether the background literature cited to justify the study is accurate and balanced. I think this brief foray has demonstrated that it can be important in establishing whether an investigator is claiming false authority for a view with cherry picking and selective attention to the literature.

Basic design of the study

The 150 patients randomized in this study are around 40 years old. Half of the sample of has been in psychiatric services for 11 or more years, with 29% of the patients in the intervention group and 19% in the control group receiving services for more than 20 years. The article notes in passing that all patients were prescribed antipsychotic medication at the outset of the study except 1 in the intervention group and 9 in the control group – 1:9? It is puzzling how such differences emerged if randomization was successful in controlling for baseline differences. Maybe it demonstrates the limitations of block randomization.

The intervention is decidedly low intensity for what is presumably a long standing symptom in chronically psychotic population.

We aimed to provide the CBT worry-reduction intervention in six sessions over 8 weeks. Each session lasted roughly an hour and took place in NHS clinics or at patients’ homes.

The six sessions were organized around booklets shared by the patient and therapist.

The main techniques were psychoeducation about worry, identification and reviewing of positive and negative beliefs about worry, increasing awareness of the initiation of worry and individual triggers, use of worry periods, planning activity at times of worry (which could include relaxation), and learning to let go of worry.

Patients were expected to practice exercises from the author’s self-help book for lay persons.

The two main practical techniques to reduce worry were then introduced: the use of worry periods (confining worry to about a 20 minute set period each day) and planning of activities at peak worry times. Worry periods were implemented flexibly. For example, most patients set up one worry period a day, but they could choose to have two worry periods a day or, in severe instances, patients instead aimed for a worry-free period. Ideally, the worry period was then substituted with a problem-solving period.

Compared to what?

The treatment of the control group was ill-defined routine care “delivered according to national and local service protocols and guidelines.” Readers are not told how much treatment the patients received or whether their care was actually congruent with these guidelines. Routine care of mental health patients in the community is notoriously deficient. That over half of these patients had been in services for more than a decade suggests that treatment for many of them had tapered off and was being delivered with no expectation of improvement.

To accept this study as an evaluation of the author’s therapy approach, we need to know how much in the way of other treatment was received by patients in both the intervention and control group. Were patients in the routine care condition, as I suspect, largely being ignored? The intervention group got 6 sessions of therapy over 8 weeks. Is that a substantial increase in psychotherapy or even in time to talk with a professional over what they would otherwise receive? Did being assigned to the intervention also increase patients’ other contact with mental health services? If the intervention therapists heard that patients was having problems with medication or serious unmet medical needs, how did they respond?

The authors report collecting data concerning receipt of services with the Client Service Receipt Inventory, but nowhere is that reported.

Most basically, we don’t know what elements the comparison/control group controlled. We have no reason to presume that the amount of contact time and basic relationship with a treatment provider was controlled.

As I have argued before, it is inappropriate and arguably unethical to use ill defined routine care or treatment-as-usual in the evaluation of a psychological intervention. We cannot tell if any apparent benefits to patients having been assigned to the intervention are due to correcting the inadequacies of routine care, including its missing of basic elements of support, attention, and encouragement. We therefore cannot tell if there are effective elements to the intervention other than  these nonspecific factors.

We cannot tell if any positive results to this trial suggest encourage dissemination and implementation or only improving likely deficiencies in the treatment received by patients in long term psychiatric care.

In terms of quickly evaluating articles reporting clinical trials, we see that imply asking “compared to what” and jumping to the comparison/control condition revealed a lot of deficiencies at the outset in what this trial could reveal.

Measuring outcomes

Two primary outcomes were declared – changes in the Penn State Worry Questionnaire and the Psychotic Symptoms Rating Scale- Delusion (PSYRATS-delusion) subscale. The authors use multivariate statistical techniques to determine whether patients assigned to the intervention group improved more on either of these measures, and whether specifically reduction in worry caused reductions in persecutory delusions.

Understand what is at stake here: the authors are trying to convince us that this is a groundbreaking study that shows that reducing worry with a brief intervention reduces long standing persecutory delusions.

The authors lose substantial credibility if we look closely at their primary measures, including their items, not just the scale names.

what-me-worry-715605The Penn State Worry Questionnaire (PSWQ) is a 16 item questionnaire widely used with college student, community and clinical samples. Items include

When I am under pressure I worry a lot.

I am always worrying about something.

And reverse direction items scored so greater endorsement indicates less worrying –

I do not tend to worry about things.

I never worry about anything.

I know, how many times does basically the same question have to be asked?

The questionnaire is meant to be general. It focuses on a single complaint that could be a symptom of anxiety. While the questionnaire could be used to screening for anxiety disorders, it does not provide a diagnosis of a mental disorder, which requires other symptoms be present. Actually, worry is only one of three components of anxiety. The others are physiological – like racing heart, sweating, or trembling – and behavioral – like avoidance or procrastination.

But “worry” is also a feature of depressed mood. Another literature discusses “worry” as “rumination.” We should not be surprised to find this questionnaire functions reasonably well as a screen for depression.

But past research has shown that even in nonclinical populations, using a cutpoint to designate high versus low worriers results in unstable classification. Without formal intervention, many of those who are “high” become  “low” over time.

In order to be included in this study, patients had to have a minimum score of 44 on the PSWQ. If we skip to the results of the study we find that the patients in the intervention group dropped from 64.8 to 56.1 and those receiving only routine care dropped from 64.5 to 59.8. The average patient in either group would have still qualified for inclusion in the study at the end of follow up.

The second outcome measure, the Psychotic Symptoms Rating Scale- Delusion subscale has six items: duration and frequency of preoccupation; intensity of distress; amount of distressing content; conviction and disruption. Each item is scored 0-4, with 0 = no problem and 4 = maximum severity.

The items are so diverse that interpretation of a change in the context of an intervention trial targeting worry becomes difficult. Technically speaking, the lack of comparability among items is so great that the measure cannot be considered an interval scale for which conventional parametric statistics could be used. We cannot reasonably assume changes in one item is equivalent to changes in other items.

It would seem, for instance, that amount of preoccupation with delusions, amount and intensity of distress, and amount of preoccupation with delusions are very different matters. The intervention group changed from a mean of 18.7 on a scale with a possible score of 24 to 13.6 at 24 weeks; the control group from 18.0 to 16.4. This change could simply represent reduction in the amount and intensity of distress, not in patients’ preoccupation with the delusions, their conviction that the delusions are true, or the disruption in their lives. Overall, the PSYRATS-delusion subscale is not a satisfactory measure on which to make strong claims about reducing worry reducing delusions. The measure is too contaminated with content similar to the worries questionnaire. We might only be finding ‘changes in worries results in changes in worries.”

Checking primary outcomes is important in evaluating a clinical trial, but in this case, it was crucial to examine what the measures assessed at an item content level. Too often reviewers uncritically accept the name of an instrument as indicating what it validly measures when used as an outcome measure.

The fancy multivariate analyses do not advance our understanding of what went on in the study. The complex statistical analyses might simply be demonstrating patients were less worried as seen in questionnaires and interview ratings based on what patients say when asked whether they are distressed.

My summary assessment is that a low intensity intervention is being evaluated against an ill-defined treatment as usual. The outcome measures are too nonspecific and overlapping to be helpful. We may simply be seeing effects of contact and reassurance among patients who are not getting much of either. So what?

testimonialsBring on the patient endorsements

Panel 1: Patient comments on the intervention presents glowing endorsements from 3 of the 73 patients assigned to the intervention group. The first patient describes the treatment as “extremely helpful” and as providing a “breakthrough.” The second patient suggests describing starting treatment being lost and without self-confidence but now being relaxed at times of the day that had previously been stressful. The third patient declared

“The therapy was very rewarding. There wasn’t anything I didn’t like. I needed that kind of therapy at the time because if I  didn’t have that therapy at that time, I wouldn’t be here.

Wow, but these dramatic gains seem inconsistent with the modest gains registered with the quantitative primary outcome measures. We are left guessing how these endorsements were elicited – where they obtained in a context where patients were expected to express gratitude for the extra attention they received? –  and the criteria by which the particular quotes were selected from what is presumably a larger pool.

Think of the outcry if Lancet Psychiatry extended this innovation to reporting of clinical trials to evaluations of medications by their developers. If such side panels are going to be retained in the future in the reporting of a clinical trial, maybe it would be best that they be marked “advertisement” and accompanied by a declaration of conflict of interest.

A missed opportunity to put the authors’ intervention to a fair test

In the Discussion section the authors state

although we think it highly unlikely that befriending or supportive counselling [sic] would have such persistent effects on worry and delusions, this possibility will have to be tested specifically in this group.

Actually, the authors don’t have much evidence of anything but a weak effect that might well have been achieved with befriending or supportive counseling delivered by persons with less training. We should be careful of accepting claims of any clinically significant effects on delusions. At best, the authors have evidence that distress associated with delusions was reduced and that in any coordination in scores between the two measurs may simply reflect confounding of the two outcome measures.

It is a waste of scarce research funds, an unethical waste of patients willingness to contribute to science to compare this low intensity psychotherapy to ill-described, unquantified treatment as usual. Another low intensity treatment like befriending or supportive counseling might provide sufficient elements of attention, support, and raised expectations to achieve comparable results.

Acknowledging the Supporting Cast

In evaluating reports of clinical trials, it is often informative to look to footnotes and acknowledgments, as well as the main text. This article acknowledges Anthony Morrison as a member of the Trial Steering Committee and Douglas Turkington as a member of the Data Monitoring and Ethics Committee. Readers of Mind the Brain might recognize Morrison as first author of a Lancet trial that I critiqued for exaggerated claims and Turkington as the first author of a trial that became an internet sensation when post-publication reviewers pointed out fundamental problems in the reporting of data.  Turkington and an editor of the journal in which the report of the trial was published counterattacked.

All three of these trials involve exaggerated claims based on a comparison between CBT and an ill-defined routine care. Like the present one, Morrison’s trial failed to report data concerning collected receipt of services. And in an interview with Lancet, Morrison admitted to avoiding a comparison between CBT and anything but routine care out of concern that differences might not be found with any treatment providing a supportive relationship, even basic supportive counseling.

MRCA note to funders

This project (09/160/06) was awarded by the Efficacy and Mechanism Evaluation (EME) Programme, and is funded by the UK Medical Research Council (MRC) and managed by the UK NHS National Institute for Health Research (NIHR) on behalf of the MRC-NIHR partnership.

Really, UK MRC, you are squandering scarce funds on methodologically poor, often small trials for which investigators make extravagant claims and that don’t include a comparison group allowing control for nonspecific effects. You really ought to insist on better attention to the existing literature in justifying another trial and adequate controls for amount of contact time, attention and support.

Don’t you see the strong influence of investigator allegiance dictating reporting of results consistent with the advancement of the investigators’ product?

I don’t understand why you allowed the investigator group to justify the study with such idiosyncratic, highly selective review of the literature driven by substituting a colloquial term “worry” for more commonly used search terms.

Do you have independent review of grants by persons who are more accepting of the usual conventions of conducting and reporting trials? Or are you faced with the problems of a small group of reviewers giving out money to like-minded friends and family? Note that the German Federal Ministry of Education and Research (BMBF) has effectively dealt with inbred old boy networks by excluding Germans from the panels of experts reviewing German grants. Might you consider the same strategy in getting more seriously about funding projects with some potential for improving patient care? Get with it, insist on rigor and reproducibility in what you fund.

*We should make too much of Oxford lending its branding to this workshop. Look at the workshops to which Harvard Medical School lends its labels.

Category: cognitive behavioral therapy, Conflict of interest, psychosis, psychotherapy, schizophrenia, Uncategorized | Tagged , , , , , , | Leave a comment

What the pot and pain pill overdose study teaches us about ecological fallacies

I am delighted to offer Mind the Brain readers a guest blog written by Keith Humphreys, Ph.D., John Finney, Ph.D., Alex Sox-Harris, Ph.D., and Daniel Kivlahan, Ph.D. Drs. Humphreys, Sox-Harris, and Finney are at the Palo Alto VA and Stanford University. Dr. Kivlahan is at the Seattle VA and the University of Washington.

Follow Professor Humphreys on Twitter @KeithNHumphreys.


Image Credit: Bogdan, Wikimedia Commons

Image Credit: Bogdan, Wikimedia Commons

A team of scientists recently reported that states with laws permitting medical marijuana had lower rates of opioid overdose than states without such laws. In a New York Times essay, two members of the team suggested this state-level association between medical marijuana access and deaths reflects the behavior of individuals in pain:


If enough people opt to treat pain with medical marijuana instead of prescription painkillers in states where this is legal, it stands to reason that states with medical marijuana laws might experience an overall decrease in opioid painkiller overdoses and deaths.


At first blush, saying it “stands to reason” seems, well, reasonable. But in the current issue of the journal in which the study appeared, we point out that the assumption that associations based on aggregations of people (e.g., counties, cities and states) must reflect parallel relationships for individuals is a seductive logical error known as the “ecological fallacy.”


Once you understand the ecological fallacy, you will recognize it in many interpretations of and media reports about science.   Here are some examples that have been reported over the years:



Such differences are counter-intuitive and therefore a bit baffling. If individuals having heart attacks who receive high quality care are far more likely to survive, doesn’t it follow that hospitals that provide higher quality care to larger percentages of their heart attack patients would have substantially lower mortality rates? (Answer: No, their results are barely better). Why don’t patterns we see in the aggregate always replicate themselves with individuals, and vice versa?


The mathematical basis for the ecological fallacy has multiple and complex aspects (our detailed explanation here), but most people find it easiest to understand when presented with a simple example. Imagine two states with 100 people each residing in them, with each state population including a comparable proportion of people in pain. Potsylvania has a loosely regulated medical marijuana system that 25% of residents access. Alabstentia, in contrast, limits access to medical marijuana so only 15% of residents can obtain it.



Medical Marijuana User Medical Marijuana Non-User Totals
Died of Opioid Overdose 2 3 5
Did Not Die of Overdose 23 72 95
Totals 25 75 100




Medical Marijuana User Medical Marijuana Non-User Totals
Died of Opioid Overdose 4 6 10
Did NotDie of Overdose 11 79 90
Totals 15 85 100


Ganja-loving Potsylvania has a lower opioid overdose death rate (5%) than more temperate Alabstentia (10%).   Does this prove that individuals in those states who use medical marijuana lower their risk of opioid overdose death? Nope. In both states, medical marijuana-users are more likely to die of a pain medication overdose than are non-users: 2 of 25 (8%) of marijuana users dying versus 3 of 75 (4%) marijuana non-users dying in Potsylvania; 4 of 15 (26.6%) of marijuana users dying versus 6 of 85 (7.1%) of non-users dying in Alabstentia!


Embracing the ecological fallacy is tempting, even to very bright people, but it must be resisted if we want to better understand the world around us. So, the next time you see a study saying, for example, that politically conservative states have higher rates of searching for sex and pornography on line and want to immediately speculate about why conservative individuals are so hypocritical, pause and remember that what applies at the aggregate level does not necessarily apply to individuals. For all we know, alienated liberals in red states may just be feeling lonely and frustrated.

Related Posts Plugin for WordPress, Blogger...
Category: Commentary, News, Psychiatry, Uncategorized | Tagged , , | Leave a comment