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.

andrea-on-mindfulness
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.

15 thoughts on “Is mindfulness-based therapy ready for rollout to prevent relapse and recurrence in depression?”

  1. i think mindfulness is just as effective or better than antidepressants. i quit taking the drugs two months ago and embraced meditation i think am recovering faster without the sideffects of the drugs

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  2. We wish that James Coyne would have checked our website before seeking to set out the Mental Health Foundation’s position.

    In response to the media coverage of the Lancet report (which elicted the Guardian headline) we said:

    “The media reports today are slightly skewed in that in some quarters it is being seen as a way to treat depression. This is not the case: what this research shows is the effectiveness of mindfulness based cognitive therapy (MBCT) in terms of prevention or recurrence. Be that as it may, it is good to see mental health being talked about in a more positive way and that more and more people are beginning to take an interest in what they can do to maintain good mental health.”

    In our press release for Mental Health Awareness Week we made it crystal clear that NICE recommends Mindfulness Based Cognitive Therapy for defined circumstances, and that when relevant, it should be available and accessible for people who meet those criteria.

    Both statements are available from our website:

    http://www.mentalhealth.org.uk/our-news/news-archive/2015/2015-05-11-mental-health-awareness-week-2015/
    http://www.mentalhealth.org.uk/our-news/news-archive/2015/2015-04-21-mindfulness-depression/

    In praising the Guardian for correcting its copy when made aware of the facts, we hope that Mr Coyne takes a similar approach.

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    1. Thank you for the clarification, but actually I did check your website and found statements consistent with my representations. For instance,

      http://www.mentalhealth.org.uk/our-news/news-archive/2015/2015-05-11-donate-free-mindfulness-course/

      Mindfulness is an integrative, mind–body-based training that helps people to change the way they think and feel about their experiences – especially stressful experiences – and is recommended as a treatment for some people with mental health problems including stress, anxiety, and depression. The Be Mindful course was created so that anyone, anywhere, can easily and effectively learn to practise mindfulness in daily life and enjoy the benefits.

      http://www.mentalhealth.org.uk/our-news/news-archive/2015/2015-05-11-mental-health-awareness-week-2015/
      Commenting, our CEO Jenny Edwards CBE said:
      “We have just had a General Election where for the first time mental health was a key issue addressed in the manifestos of the major parties. The public are calling for practical action. It’s now time to hold the new Conservative Government to commit to significant steps. Of course adequate funding of mental health services is vital, but we also need a national prevention strategy for mental health to help prevent mental health problems from developing wherever possible. We need to tackle the causes that increase the risks of mental ill health and to equip people with practical tools that help prevent stress, anxiety and depression, and build resilience.

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  3. I definitely do think there’s something to mindfulness therapy, but every person is different. It might work for some people but I think we should keep all sorts of treatment options open for those who it doesn’t work for. Thanks for sharing this!

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  4. Thanks, James, for a rigorous and edifying post as always. I chose to analyse this article for a CAT exercise for one of my classes and still think it’s a generally well-done study (possibly one of the most rigorous and highly-powered mindfulness trials out there), so I think the authors deserve some more credit there. Nonetheless, I appreciated your insights into the limitations of how we can interpret these findings, and how much we still don’t know.

    I do need to point out a possible misrepresentation however. You say:

    However, I don’t believe that the authors tried to spin it into a non-inferiority trial in the Lancet report (maybe this is the case in media reports, but at least not in the original article); in fact, they make it very clear that it’s a superiority trial:

    (Abstract)

    (p. 2)

    (p. 9)

    In sum–regardless of media misrepresentations, I think the authors accurately reported this trial in the article.

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    1. Looks like the HTML didn’t work — here are the quotes:

      You say: “Something 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.”

      Quotes from the article emphasising focus on superiority:

      “We aimed to see whether MBCT with support to taper or discontinue antidepressant treatment (MBCT-TS) was superior to maintenance antidepressants for prevention of depressive relapse or recurrence over 24 months.” (Abstract)

      “we tested whether MBCT with support to taper or discontinue antidepressant treatment (MBCT-TS) was better than maintenance antidepressants” (p. 2)

      “We noted no evidence for the superiority of MBCT-TS compared with maintenance antidepressants for patients with recurrent depression in terms of the primary outcome of time to depressive relapse or recurrence over 24 months or any of the secondary outcomes.” (p. 9)

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    2. Thanks for your careful read and I am pleased to see you found use of this blog in your Critical Appraisal Course. But I think we disagree on authors’ responsibilities in reporting a null efficacy trial designed to test whether one treatment is superior to a control group. One would expect the author to explain why the expected findings were not obtained. However, when a trial is designed to test noninferiority and therefore has a much larger sample size, the author is entitled to explain the lack of difference with a lot more confidence. Furthermore, these authors had a quite ill-defined control group in which they did not even assess adherence to either medication or appointment keeping. So, we don’t even know what precisely they failed to find mindfulness superior.

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  5. I’ve just checked the acknowledgements in the 2011 PACE trial paper, and I counted roughly sixty names listed. And the trial protocol lists roughly 33 names under the ‘Trial Management Group’. And the 2011 paper lists roughly 19 names under ‘PACE Trial Group’, which includes the trial steering committee. And then there are the trial authors for the protocol and the 2011 paper, and further trial authors and acknowledgements across at least another six published papers.

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  6. Hi there

    I read your recent post about the BJPsych paper and that brought me here.

    Jessie Sun raised this issue back in June 2015 (above) and you gave her a complicated answer.

    Can we keep it simple this time?

    You state the following:

    “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.

    I used control F search the paper and the words superior / superiority are used 8 times.

    Are you willing to admit that your statement is just plain wrong?

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    1. Perhaps there is something wrong with your search strategy: I went to the corrected registration of the trial. It clearly states

      This trial asks the policy research question; is MBCT with support to taper/discontinue antidepressant medication (MBCT-TS) superior to m-ADM in terms of: a primary outcome of preventing depressive relapse/recurrence over 24 months; and secondary outcomes of (a) depression free days, (b) residual depressive symptoms, (c) antidepressant medication (ADM) usage, (d) psychiatric and medical co-morbidity, (e) quality of life, and (f) cost effectiveness?

      So, the authors were not merely claiming superiority of mindfullness for one primary outcome, they were making claims for five different outcomes, not of which panned out. But they failed to disclose this in their article. But more importantly they make deceptive claims about equivalency of mindfulness and antidepressants in the abstract, elsewhere in the article, and in a huge publicity campaign.

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  7. Thanks.

    Can we keep this simple?

    Your statement (I’ve put it below again) concerns the Lancet report of the trial outcome (your words).

    “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.”

    The Lancet report is easily accessible here in full.

    http://www.thelancet.com/journals/lancet/article/PIIS0140-6736(14)62222-4/abstract

    The Lancet report makes it repeatedly clear that this was a superiority trial.

    You state that the report does not.

    Are you prepared to admit that your statement about the Lancet report is factually incorrect?

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    1. The Lancet requires clinical trials to be registered ahead of time and declare their hypotheses and outcomes. A superiority trial, as noted in the present blog post, is a different design than a test of the null hypothesis of no differences ThE LANCET did not have sufficient power to test superiority, but ignored its registration in what is reported in this article, as in the abstract:

      However, when considered in the context of the totality of randomised controlled data, we found evidence from this trial to support MBCT-TS as an alternative to maintenance antidepressants for prevention of depressive relapse or recurrence at similar costs.

      That is a distortion but was used to promote mindfulness in an impressive publicity campaign.

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