A skeptical look at:
Richards DA, Ekers D, McMillan D, Taylor RS, Byford S, Warren FC, Barrett B, Farrand PA, Gilbody S, Kuyken W, O’Mahen H. et al. Cost and Outcome of Behavioural Activation versus Cognitive Behavioural Therapy for Depression (COBRA): a randomised, controlled, non-inferiority trial. The Lancet. 2016 Jul 23.
Were they working below their pay grade? The 14 authors of the study collectively have impressive expertise. They claim to have obtained extensive consultation in designing and implementing the trial. Yet they produced:
- A study doomed from the start by serious methodological problems from yielding any scientifically valid and generalizable results.
- Instead, they produced tortured results that pander to policymakers seeking an illusory cheap fix.
Why the interests of persons with mental health problems are not served by translating the hype from a wasteful project into clinical practice and policy.
Maybe you were shocked and awed, as I was by the publicity campaign mounted by The Lancet on behalf of a terribly flawed article in The Lancet Psychiatry about whether locked inpatient wards fail suicidal patients.
It was a minor league effort compared to the campaign orchestrated by the Science Media Centre for a recent article in The Lancet The study concerned a noninferiority trial of behavioural activation (BA) versus cognitive behaviour therapy (CBT) for depression. The message echoing through social media without any critical response was behavioural activation for depression delivered by minimally trained mental health workers was cheaper but just as effective as cognitive behavioural therapy delivered by clinical psychologists.
Reflecting the success of the campaign, the immediate reactions to the article are like nothing I have recently seen. Here are the published altmetrics for an article with an extraordinary overall score of 696 (!) as of August 24, 2016.
Here is the press release.
Here is the full article reporting the study, which nobody in the Twitter storm seems to have consulted.
Here are supplementary materials.
Here is the well-orchestrated,uncritical response from tweeters, UK academics and policy makers.
The Basics of the study
The study was an open-label two-armed non-inferiority trial of behavioural activation therapy (BA) versus cognitive behavioural therapy (CBT) for depression with no non-specific comparison/control treatment.
The primary outcome was depression symptoms measured with the self-report PHQ-9 at 12 months.
Delivery of both BA and CBT followed written manuals for a maximum of 20 60-minute sessions over 16 weeks, but with the option of four additional booster sessions if the patients wanted them. Receipt of eight sessions was considered an adequate exposure to the treatments.
The BA was delivered by
Junior mental health professionals —graduates trained to deliver guided self-help interventions, but with neither professional mental health qualifications nor formal training in psychological therapies—delivered an individually tailored programme re-engaging participants with positive environmental stimuli and developing depression management strategies.
CBT, in contrast, was delivered by
Professional or equivalently qualified psychotherapists, accredited as CBT therapists with the British Association of Behavioural and Cognitive Psychotherapy, with a postgraduate diploma in CBT.
The interpretation provided by the journal article:
Junior mental health workers with no professional training in psychological therapies can deliver behavioural activation, a simple psychological treatment, with no lesser effect than CBT has and at less cost. Effective psychological therapy for depression can be delivered without the need for costly and highly trained professionals.
A non-inferiority trial
An NHS website explains non-inferiority trials:
The objective of non-inferiority trials is to compare a novel treatment to an active treatment with a view of demonstrating that it is not clinically worse with regards to a specified endpoint. It is assumed that the comparator treatment has been established to have a significant clinical effect (against placebo). These trials are frequently used in situations where use of a superiority trial against a placebo control may be considered unethical.
Noninferiority trials (NIs) have a bad reputation. Consistent with a large literature, a recent systematic review of NI HIV trials found the overall methodological quality to be poor, with a high risk of bias. The people who brought you CONSORT saw fit to develop special reporting standards for NIs so that misuse of the design in the service of getting publishable results is more readily detected.
Basically, an NI RCT commits investigators and readers to accepting null results as support for a new treatment because it is no worse than an existing one. Suspicions are immediately raised as to why investigators might want to make that point.
Noninferiority trials are very popular among Pharma companies marketing rivals to popular medications. They use noninferiority trials to show that their brand is no worse than the already popular medication. But by not including a nonspecific control group, the trialists don’t bother to show that either of the medications is more effective than placebo under the conditions in which they were administered in these trials. Often, the medication dominating the market had achieved FDA approval for advertising with evidence of only being only modestly effective. So, potato are noninferior to spuds.
Compounding the problems of a noninferiority trial many times over
Let’s not dwell on this trial being a noninferiority trial, although I will return to the problem of knowing what would happen in the absence of either intervention or with a credible, nonspecific control group. Let’s focus instead on some other features of the trial that seriously compromised an already compromised trial.
Essentially, we will see that the investigators reached out to primary care patients who were mostly already receiving treatment with antidepressants, but unlikely with the support and positive expectations or even adherence necessary to obtain benefit. By providing these nonspecific factors, any psychological intervention would likely to prove effective in the short run.
The total amount of treatment offered substantially exceeded what is typically provided in clinical trials of CBT. However, uptake and actual receipt of treatment is likely to be low in such a population recruited by outreach, not active seeking treatment. So, noise is being introduced by offering so much treatment.
A considerable proportion of primary care patients identified as depressed won’t accept treatment or will not accept the full intensity available. However, without careful consideration of data that are probably not available for this trial, it will be ambiguous whether the amount of treatment received by particular patients represented dropping out prematurely or simply dropping out when they were satisfied with the benefits they had been received. Undoubtedly, failures to receive minimal intensity of treatment and even the overall amount of treatment received by particular patients are substantial and complexly determined, but nonrandom and differ between patients.
Dropping out of treatment is often associated with dropping out of a study – further data not being available for follow-up. These conditions set the stage for considerable challenges in analyzing and generalizing from whatever data are available. Clearly, the assumption of data being missing at random will be violated. But that is the key assumption required by multivariate statistical strategies that attempt to compensate for incomplete data.
12 months – the time point designated for assessment of primary outcomes – is likely to exceed the duration of a depressive episode in a primary care population, which is approximately 9 months. In the absence of a nonspecific active comparison/control or even a waitlist control group, recovery that would’ve occurred in the absence of treatment will be ascribed to the two active interventions being studied.
12 months is likely to exceed substantially the end of any treatment being received and so effects of any active treatments are likely to dissipate. The design allowed for up to four booster sessions. However, access to booster sessions was not controlled. It was not assigned and access cannot be assumed to be random. As we will see when we examined the CONSORT flowchart for the study, there was no increase in the number of patients receiving an adequate exposure to psychotherapy from 6 to 12 months. That is likely to indicate that most active treatment had ended within the first six months.
Focusing on 12 months outcomes, rather than six months, increases the unreliability of any analyses because more 12 month outcomes will be missing than what were available at six months.
Taken together, the excessively long 12 month follow-up being designated as primary outcome and the unusually amount of treatment being offered, but not necessarily being accepted, create substantial problems of missing data that cannot be compensated by typical imputation and multivariate methods; difficulties interpreting results in terms of the amount of treatment actually received; and comparison to the primary outcomes typical trials of psychotherapy being offered to patients seeking psychotherapy.
The authors’ multivariate analysis strategy was inappropriate, given the amount of missing data and the violation of data being missing at random..
Surely the more experienced of the 14 authors of The Lancet should have anticipated these problems and the low likelihood that this study would produce generalizable results.
Recruitment of patients
The article states:
We recruited participants by searching the electronic case records of general practices and psychological therapy services for patients with depression, identifying potential participants from depression classiﬁcation codes. Practices or services contacted patients to seek permission for researcher contact. The research team interviewed those that responded, provided detailed information on the study, took informed written consent, and assessed people for eligibility.
Eligible participants were adults aged 18 years or older who met diagnostic criteria for major depressive disorder assessed by researchers using a standard clinical interview (Structured Clinical Interview for the Diagnostic and Statistical Manual of Mental Disorders, Fourth Edition [SCID]9). We excluded people at interview who were receiving psychological therapy, were alcohol or drug dependent, were acutely suicidal or had attempted suicide in the previous 2 months, or were cognitively impaired, or who had bipolar disorder or psychosis or psychotic symptoms.
Table 3 Patient Characteristics reveals a couple of things about co-treatment with antidepressants that must be taken into consideration in evaluating the design and interpreting results.
So, investigators did not wait for patients to refer themselves or to be referred by physicians to the trial, they reached out to them. Applying their exclusion criteria, the investigators obtained a sample that mostly had been prescribed antidepressants, with no indication that the prescription had ended. The length of time which 70% patients had been on antidepressants was highly skewed, with a mean of 164 weeks and a median of 19. These figures strain credibility. I have reached out to the authors with a question whether there is an error in the table and await clarification.
We cannot assume that patients whose records indicate they were prescribed an antidepressant were refilling their prescriptions at the time of recruitment, were faithfully adhering, or were even being monitored. The length of time since initial prescription increases skepticism whether there was adequate exposure to antidepressants at the time of recruitment to the study..
The inadequacy of antidepressant treatment in routine primary care
Refilling of first prescriptions of antidepressants in primary care, adherence, and monitoring and follow-up by providers are notoriously low.
Guideline-congruent treatment with antidepressants in the United States requires a five week follow up visit, which is only infrequently received in routine. When the five week follow-up visit is kept,
Rates of improvement in depression associated with prescription of an antidepressant in routine care approximate that achieved with pill placebo in antidepressant trials. The reasons for this are complex: but center on depression being of mild to moderate severity in primary care. Perhaps more important is that the attention, provisional positive expectations and support provided in routine primary care is lower than what is provided in the blinded pill-placebo condition in clinical trials. In blinded trials, neither the provider nor patient know whether the active medication or a pill placebo is being administered. The famous NIMH National Collaborative Study found, not surprisingly, that response in the pill-placebo condition was predicted by the quality of the therapeutic alliance between patient and provider.
In The Lancet study, readers are not provided with important baseline characteristics of the patients that are crucial to interpreting the results and their generalizability. We don’t know the baseline or subsequent adequacy of antidepressant treatment or of the quality of the routine care being provided for it. Given that antidepressants are not the first-line treatment for mild to moderate depression, we don’t know why these patients were not receiving psychotherapy. We don’t know even whether the recruited patients were previously offered psychotherapy and with what uptake, except that they were not receiving it two months prior to recruitment.
There is a fascinating missing story about why these patients were not receiving psychotherapy at the start of the study and why and with what accuracy they were described as taking antidepressants.
Readers are not told what happened to antidepressant treatment during the trial. To what extent did patients who were not receiving antidepressants begin doing so? As result of the more frequent contact and support provided in the psychotherapy, to what extent was there improvement in adherence, as well as the ongoing support inattention per providers and attention from primary care providers?
Depression identified in primary care is a highly heterogeneous condition, more so than among patients recruited from treatment in specialty mental health settings. Much of the depression has only the minimum number of symptoms required for a diagnosis or one more. The reliability of diagnosis is therefore lower than in specialty mental health settings. Much of the depression and anxiety disorders identified with semi structured research instruments in populations that is not selected for having sought treatment resolves itself without formal intervention.
The investigators were using less than ideal methods to recruit patients from a population in which major depressive disorder is highly heterogeneous and subject to recovery in the absence of treatment by the time point designated for assessment of primary outcome. They did not sufficiently address the problem of a high level of co-treatment having been prescribed long before the beginning of the study. They did not even assess the extent to which that prescribed treatment had patient adherence or provider monitoring and follow-up. The 12 month follow-up allowed the influence of lots of factors beyond the direct effects of the active ingredients of the two interventions being compared in the absence of a control group.
Examination of a table presented in the supplementary materials suggests that most change occurred in the first six months after enrollment and little thereafter. We don’t know the extent to which there was any treatment beyond the first six-month or what effect it had. A population with clinically significant depression drawn from specially care, some deterioration can be expected after withdrawal of active treatment. In a primary care population, such a graph could be produced in large part because of the recovery from depression that would be observed in the absence of active treatment.
Cost-effectiveness analyses reported in the study address the wrong question. These analyses only considered the relative cost of these two active treatments, leaving unaddressed the more basic question of whether it is cost-effective to offer either treatments at this intensity. It might be more cost-effective to have a person with even less mental health training contact patients, inquire about adherence, side effects, and clinical outcomes, and prompt patients to accept another appointment with the GP if an algorithm indicates that would be appropriate.
The intensity of treatment being offered and received
The 20 sessions plus 4 booster sessions of psychotherapy being offered in this trial is considerably higher than the 12 to 16 sessions offered in the typical RCT for depression. Having more sessions available than typical introduces some complications. Results are not comparable to what is found inthe trials offering less treatment. But in a primary care population not actively seeking psychotherapy for depression, there is further complication in that many patients will not access the full 20 sessions. There will be difficulties interpreting results in terms of intensity of treatment because of the heterogeneity of reasons for getting less treatment. Effectively, offering so much therapy to a group that is less inclined to accept psychotherapy introduces a lot of noise in trying to make sense of the data, particularly when cost-effectiveness is an issue.
This excerpt from the CONSORT flowchart demonstrates the multiple problems associated with offering so much treatment to a population that was not actively seeking it and yet needing twelve-month data for interpreting the results of a trial.
The number of patients who had no data at six months increased by 12 months. There was apparently no increase in the number of patients receiving an adequate exposure to psychotherapy
Why the interest of people with mental health problems are not served by the results claimed by these investigators being translated into clinical practice.
The UK National Health Service (NHS) is seriously underfunding mental health services. Patients being referred for psychotherapy from primary care have waiting periods that often exceed the expected length of an episode of depression in primary care. Simply waiting for depression to remit without treatment is not necessarily cost effective because of the unneeded suffering, role impairment, and associated social and personal costs of an episode that persist. Moreover, there is a subgroup of depressed patients in primary care who need more intensive or different treatment. Guidelines recommending assessment after five weeks are not usually reflected in actual clinical practice.
There’s a desperate search for ways in which costs can be further reduced in the NHS. The Lancet study is being interpreted to suggest that more expensive clinical psychologists can be replaced by less expensive and less trained mental health workers. Uncritically and literally accepted, the message is that clinical psychologist working half-time addressing particular comment clinical problems can be replaced by less expensive mental health workers achieving the same effects in the same amount of time.
The pragmatic translation of these claims into practice are replace have a clinical psychologists with cheaper mental health workers. I don’t think it’s being cynical to anticipate the NHS seizing upon an opportunity to reduce costs, while ignoring effects on overall quality of care.
Care for the severely mentally ill in the NHS is already seriously compromised for other reasons. Patients experiencing an acute or chronic breakdown in psychological and social functioning often do not get minimal support and contact time to avoid more intensive and costly interventions like hospitalization. I think would be naïve to expect that the resources freed up by replacing a substantial portion of clinical psychologists with minimally trained mental health workers would be put into addressing unmeet needs of the severely mentally ill.
Although not always labeled as such, some form of BA is integral to stepped care approaches to depression in primary care. Before being prescribed antidepressants or being referred to psychotherapy, patients are encouraged to increased pleasant activities. In Scotland, they may be even given free movie passes for participating in cleanup of parks.
A stepped care approach is attractive, but evaluation of cost effectiveness is complicated by consideration of the need for adequate management of antidepressants for those patients who go on to that level of care.
If we are considering a sample of primary care patients mostly already receiving antidepressants, the relevant comparator is introduction of a depression care manager.
Furthermore, there are issues in the adequacy of addressing the needs of patients who do not benefit from lower intensity care. Is the lack of improvement with low levels of care adequately monitored and addressed. Is the uncertain escalation in level of care adequately supported so that referrals are completed?
The results of The Lancet study don’t tell us very much about the adequacy of care that patients who were enrolled in the study were receiving or whether BA is as effective as CBT as stand-alone treatments or whether nonspecific treatments would’ve done as well. We don’t even know whether patients assigned to a waitlist control would’ve shown as much improvement by 12 months and we have reason to suspect that many would.
I’m sure that the administrations of NHS are delighted with the positive reception of this study. I think it should be greeted with considerable skepticism. I am disappointed that the huge resources that went into conducting this study which could have put into more informative and useful research.
I end with two questions for the 14 authors – Can you recognize the shortcomings of your study and its interpretation that you have offered? Are you at least a little uncomfortable with the use to which these results will be put?