Monday, 29 April 2013

The Dream Machine - Cut ups, cut ins, cut outs

Our new soap that's peachy keen saves your soul and keeps you clean
It's recommended, used by the Queen
Gonna improve your IQ, help in everything you do
It's economic, don't cost too much.
Know Your Product (The Saints)
 

Hutton P and Taylor PJ. Cognitive behavioural therapy for psychosis prevention: a systematic review and meta-analysis. Psychological Medicine (2013): 1-20


In January I blogged on a meta-analysis by Stafford, Jackson, Mayo-Wilson , Morrison & Kendall published in the BMJ - My post - Its Just a Story: Transition to Psychosis & CBT  - concerns whether CBT may prevent transition to psychosis.

Cut ups
Three months on and we have another meta-analysis on the same topic from one author (Hutton) who coincidentally works in the lab of one author (Morrison) on the earlier paper

It's a mash-up (Pistols meet Madonna)

As noted, I have already covered some problems with the original BMJ paper and much of what I said there applies here. Nonetheless, the current meta-analysis makes greater claims for CBT preventing transition to psychosis e.g. over longer periods of time.
At every time point, the relative risk of transition was reduced by more than 50% for those receiving CBT. (Hutton & Taylor 2013)

The Saints (1978, Know your Product)
A fine Australian export
"Where's the Professor...we need him now"
 
Why do Hutton & Taylor come to somewhat grander conclusions in favour of CBT? One reason is because they included a study not included by Stafford et al. The study is by Bechdolf et al. (2012) "Preventing progression to first-episode psychosis in early initial prodromal states." As Figure 2 (below) from Hutton & Taylor shows, this Bechdolf paper is the most favourable towards CBT preventing transition (with largest risk ratio here at 6 months, but also in their 12 month (0 and 9 transitions for Experimental and controls respectively) and 18-24 month analyses (1 and 10 transitions) - so is worth looking at in more detail
 
 
Its not that Stafford et al were unaware of the Bechdolf paper, so why did they not include it...?
 
Crucially, Bechdolf et al used Integrated Psychological Intervention (IPI), which does include individual CBT, but also group skills training, cognitive remediation and multifamily psychoeducation. So, even if changes in transition rates emerge - they are no more attributable to CBT than any other component of the IPI intervention. Unsurprisingly then, in their meta analysis, Stafford et al examined IPI studies including the Bechdolf study separately from their CBT analyses.

Jim Morrison (& the Doors) duets with Amy Whinehouse
Some mash-ups are made in heaven

Its also worth noting that Bechdolf et al also differs from the all other studies as their participants were prodromal, i.e. had self-reported symptoms which they describe as preceding the subthreshold psychotic symptoms typically used as entry conditions in the other studies. Finally, Stafford et al rated study quality using the GRADE system (for risk of bias, inconsistency, indirectness, imprecision, and publication bias) and classed the Bechdolf et al study as 'very low' quality evidence - indeed, the lowest possible in that framework.
You can't fake quality any more than you can fake a good meal
William Burroughs
 
A second difference concerns the inclusion of McGorry et al (2012) by Hutton & Taylor. Again its worth examining this study in more detail
 

First, what is the design of the McGorry et al study? Well...participants were randomly assigned to the following groups:
     Cognitive Therapy + Risperidone
     Cognitive Therapy + Placebo
     or Supportive Therapy + Placebo.
 Plus
a 'Monitoring' group - or those people who refused random assignment - so are not  -in fact - part of a randomised trial (but self-selecting controls!)
 
McGorry et al then have no CBT group (as such) and no randomised control group (as such)...
 
So, its difficult to see how the studies by Bechdolf  et al and McGorry et al could be described as assessing the impact of CBT per se
and when they are removed them from the equation ...the effect is non-existent
 
As mentioned, I have covered the Stafford et al meta analysis and some of the studies and issues in my other post. Nevertheless, I would conclude by reiterating:
a) the extremely low transition rates (<10%) of Ultra High Risk individuals
b) CBT shows no evidence of preventing transition - indeed, no single study shows a significant and reliable effect; and finally,
c) even if CBT did prevent transition to psychosis ...How would it actually be preventing psychosis?  The whole approach is bereft of any theoretical ideas on this notion - one thing is sure - it is NOT via the reduction of symptoms - as both meta analyses definitely show that symptoms do not change from before to after CBT
 
~
When Brion Gysin spoke about his 'Dream Machine', he said it was "The worlds only artwork that you look at with eyes tightly closed" - I wonder if the same might be said of CBT for psychosis.

 

 
 
 


12 comments:

  1. This really reminded me of this comment about the way data was being spun by Trudie Chalder from an old trial for cognitive therapy intended to prevent IM leading on to CFS: http://forums.phoenixrising.me/index.php?threads/2003-a-randomised-controlled-trial-of-a-psycho-educational-intervention-to-aid-reco.13326/

    So many claims made by researchers fall apart when the details are looked at, yet there's still such a tendency to assume that their claims are impartial and 'evidence based'.

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  2. Hi Keith.

    I was alerted to your blog by some friends/ colleagues attending a CBT conference here in Boston USA. They seem to enjoy checking it out in much the same way that I enjoy checking out the Daily Mail website - it gives then some amusement coupled to a satisfactory feeling of moral superiority.

    As you know, your critique of CBT is not taken very seriously in the mental health community, mainly because its seen as very biased (I think a commentator of one of your earlier posts called it vitriolic, which you disputed, but that seems about right to me). NICE recommends that CBT is made available to all patients with 'schizophrenia' and, if the new data we've been looking over during the last few days is anything to go by, they're going to keep recommending it (although, at present, implementation is poor, so only about 10% of patients get it despite many more wanting to see a therapist).

    It seems to me that there are three problems in your critique. First, part of your strategy seems to be to pick flaws in each of the individual studies, which is of course always possible (I don't think you've ever carried out an RCT but, believe me, they are fiendishly difficult, and no one has yet been able to carry out a perfect trial for anything - whether for drug or psychotherapy). This allows you to dismiss the trees without noticing the wood, which is that most of the trials show some kind of positive effect.

    Another issue is that you seem to take a niave view about control therapies. The difficulty of showing that any one type of psychotherapy beats any other is well known to psychotherapy researchers (the 'Dodo bird conjecture' is the term used in the trade for the hypothesis that all psychotherapies are equally effective, which is usually attributed to common factors such as the therapeutic alliance). What really matters, if you are a patient, is whether therapy is more helpful than no therapy, rather than whether CBT is more helpful than, say, Rogerian counselling.

    Finally, of course, CBT (or any other kind of therapy - when you look in detail at what CBT therapists do they often employ a broad range of strategies that overlap with other kinds of approaches) is not just targetted at 'schizophrenic symptoms'. Here in Boston we've been looking at interventions designed to reduce post-trauma symptoms in patients (a surprising proportion of 'schizophrenia' patients also meet the criteria for PTSD) and yesterday we were looking at strategies to improve social skills (usually by combining CBT with old fashioned social skills training).

    Richard Bentall

    To be continued (reached word limit)

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    1. Dear Richard,
      thanks for taking the time to liken my blog to the Daily Mail – of course it’s flattering to serve as amusement and to receive visitations from the self-declared morally superior

      You say our “…critique of CBT is not taken very seriously in the mental health community”. I assume some take our paper seriously - as it was one of the 50 most read papers at 'Psychological Medicine' over the past 50 years, is 'still' in the top 10 most downloaded today and has been cited nearly 100 times in 2.5 years. If anyone wants to judge for themselves, our meta-analysis is free here (https://uhra.herts.ac.uk/dspace/bitstream/2299/5741/3/903449.pdf)
      ...And I would hope you take it (and all research) seriously as a member of the REF2013 panel – whether you agree with it or not!

      If you think there’s vitriol, then please specifically point it out and I will happily remove it and apologise – rather, I think I take great efforts to stick to the 'data' and avoid being drawn by the non-science (anti-science) emotional responses that come my way from CBT acolytes

      Re your Boston conference, I cant discuss ‘data’ that only you have seen– though you seem not to believe in discussing individual studies (see below)

      Re my apparent ‘strategy’ – It hardly bears comment that you see my finding flaws in individual studies as a problem! And to say I don’t see the wood for the trees misses my critiques of meta-analyses – that is presumably putting the trees together to see the wood

      I don’t see how its relevant whether I have carried out an RCT or not (though I have)

      Not sure what your nebulous phrase “most trials show some kind of positive effect” means - but if you mean 'significant' symptom reduction, then its simply untrue - go ahead and prove me wrong on here! If you mean something else, please be specific

      Re being ‘na├»ve view about control therapies’ – I don’t see your point - we are well aware of the dodo bird conjecture – if all are equal, then what's the basis for NICE (you or anyone) advocating CBT over cheaper, simpler equally 'effective' alternatives e.g. befriending? So it does matter to taxpayers who are in receipt of NICE advocated interventions

      Please try to deal with the issues raised (rather than the Daily Mail etc nonsense) – I am perfectly happy to discuss trees or wood with you here

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  3. To continue:

    But, whether or not you think that CBT is helpful to patients (I'm inclined to beleive the patients on this issue), I'd like to asky you two questions:

    1. Why don't you turn your forensic eye to other treatments, particularly psychiatric drugs? In general, the quality of drug trials is far inferior to the quality of CBT trials (shorter follow-up and much higher drop out rates being two well-documented problems) and there's also far greater evidence of publication bias (CBT trials usually have to get published because they're publicly funded; drug trial often go unpublished when they fail to find the results desired by their pharmaceutical industry sponsors). As you know, there's also a lot of evidence of corruption in the way that the pharmaceutical industry promotes psychiatric drugs (see Bob Whitaker's book 'Mad in America' or Ben Goldachre's 'Bad Pharma'), because of the vast profits involved. There's very little money to be made out of CBT, apart from the not particularly enormous salary of an NHS clinical psychologist. Most importantly, the worst you might say about CBT is that its useless - there's absolutely no evidence that it actually harms people. Psychiatric drugs , on the other hand, cause some very serious, sometimes life-threatening side effects - diabetes and cardiac problems in the case of antipsychotics, for example; increased suicidal ideation in the case of some SSRIs. These side effects partly although not wholey (suicide is also a big factor) explain the reduced life expectancy of psychiatric patients. If you really cared about the science, you'd surely focus on an aspect of psychiatric care in which bad science is deliberately promoted for profit. And if you really cared about patients, you'd focus on treatments that actually harm them.

    2. What is your vision for psychiatric care in the UK? How would you like to see patients treated? Over the past several decades I've seen many patients who have felt that services ignore their personal stories, and who have been coerced to take unpleasant drugs. At the very least, CBT (and other kinds of psychotherapy) are humanizing. They make patients feel cared for and listened to. So, in your wisdom, maybe instead of being negative about what hard working NHS psychologists are currently doing, you'd tell us what we could do that would be better?

    Richard Bentall

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    1. A few points on your second post as people have asked if I would reply:

      1. “I'm inclined to believe the patients on this issue” Listening to ‘patients’ is important, but the problem – being “inclined to believe patients” self-report is not the level of evidence normally required for adopting interventions (as I'm sure you would argue about pharma interventions)

      2. I appreciate you career advice to me "Why don't you turn your forensic eye to other treatments, particularly psychiatric drugs?" but as you say lots of other people are doing a fine job in that field

      3. I am unaware of any studies directly comparing the quality of CBT trials and antipsychotic trials to support your ‘argument’ – please point me to the relevant study of comparison to back up your bold statement.
      Its easy to also point to studies documenting poor quality in CBT trials (e.g. Cuijpers et al CBT for depression). In the meta analysis of CBT trials in schizophrenia by Wykes et al – when talking about the low level of methodological rigour in CBT for psychosis studies states “These results are no different to those that have been found for drug and other medical treatment, and the results reported here are salutary for all psychiatric studies.”

      4 You say “there's absolutely no evidence that it [CBT] actually harms people.” This is both disingenuous and incorrect. Its disingenuous because CBT for psychosis researchers hardly ever report adverse effects of the intervention – in fact the recent meta analysis by Stafford et al (on CBT for high risk psychosis) stated “Psychological treatments are also associated with significant side effects, with about 10% of participants in such treatments deteriorating… Any future trials of psychological interventions should measure and report such adverse effects.”
      Indeed, recent studies show that CBT for psychosis may increase negative symptoms (Klingberg et al 2012) and increase relapse rates (Garety et al)

      5 Finally, I am frankly astonished at the insinuations in your offensive statements “And if you really cared about patients, you'd focus on treatments that actually harm them”
      And “If you really cared about the science…”
      And “maybe instead of being negative about what hard working NHS psychologists are currently doing”


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  4. This doesn't really address Keith's point. "At least it doesn't harm anyone" is not a reason for delivering a treatment. "Do no harm" is a starting point, not the limit of our aspiration.

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  5. All distorted claims about the efficacy of treatments should be seen as harmful. The post I linked to above shows how misleading claims can leave patients feeling angry and betrayed.

    In one of the two largest trials testing psychosocial approaches for Chronic Fatigue Syndrome, for which Bentall was a co-author and participated in the training and supervision of therapists, patients were given “Rousing Reassurance”. This included claiming that:

    From the moment you walk out of this room your recovery is beginning.

    There is no disease

    Go for 100% recovery.

    http://www.fine-trial.net/downloads/CFS%20patient%20presentation.pdf

    The results from this trial showed that the promotion of these cognitions did not have a positive effect on patients according to their primary outcome measure:

    “At one year after finishing treatment (70 weeks), there were no statistically significant differences in fatigue or physical functioning between patients allocated to pragmatic rehabilitation and those on treatment as usual (-1.00, 95% CI -2.10 to +0.11; P=0.076 and +2.57, 95% CI 3.90 to +9.03; P=0.435).”

    http://www.ncbi.nlm.nih.gov/pmc/articles/PMC2859122/

    That is not to say that the promotion of these cognitions had no effect. Telling people that patients’ disability was a result of severe deconditioning and disruption of circadian rhythms which could be reversed by rehabilitation, when this illness model was not supported by the evidence and the treatment was ineffective, unsurprisingly led to frustration and unreasonable views of patients: “The bastards don’t want to get better”.

    http://www.implementationscience.com/content/pdf/1748-5908-6-132.pdf?forumid=331851

    In the case of CFS, we should be able to assess the value of treatments by measuring improvements in the amount of activity that patients are able to do. However, results showing that CBT for CFS can only affect patient’s questionnaire scores, and not objectively measured levels of activity is instead interpreted as showing that CBT is so effective it can treat patients’ symptoms without there being any improvement in activity levels: http://journals.cambridge.org/action/displayAbstract?fromPage=online&aid=7826378

    When the value of the outcome measures being used is questionable and we find that, while encouraging patients to think positively leads to them answering questionnaires more positively, it does not improve more objective measures of disability (the recently published PACE trial also found that the addition of CBT and GET led to no improvements in occupational outcomes, or claims for disability benefits), then it would be sensible to be cautious in one’s claims about efficacy rather than rousing or reassuring.

    If different psychotherapies lead to similar results, far better to only use those that make the most minimal intervention, and are thus least likely to lead to unintended consequences and harm.

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    1. Thanks Crumb - I will have to take a look when I get time

      Delete
  6. When Richard Bentall states that that most of the trials of CBT for schizophrenia ‘show some kind of positive effect’, he could equally well be saying that few of them show a clear or convincing effect. What supporters of this form of therapy badly need is a large, well-controlled trial showing clear beneficial effects on key psychosis-related outcome measures.

    Alternatively, if such a trial (like most of the large, well-controlled trials of CBT for schizophrenia to date) were to fail to deliver the goods, then it could well be curtains for the whole painful, protracted endeavour.

    It's good to know, therefore, that just such a trial has now been carried out. The POSITIVE study (open-access protocol available at Klingberg S et al, Trials, 2010) aimed to recruit 330 patients with non-affective functional psychosis who were assigned to either CBT and or a control intervention for the nonspecific effects of psychotherapy, supportive therapy. It was carried out under blind conditions and built in several other design features to minimize bias from other sources.

    Preliminary results were presented at a conference in Berlin 18 months ago, so published results should be coming out any day now. And in the remote event the authors have difficulty publishing, I’m sure that, following good research practice, they’ll post the findings on the web.

    So one way or another the debate is shortly going to become academic. Maybe someone who reads this blog already knows something....

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  7. Dear Peter
    as we all know, it is completely false to say or imply that most CBT for psychosis studies document a significant effect - even a cursory look at Til Wykes meta analysis shows this (Open Access at http://www.ncbi.nlm.nih.gov/pmc/articles/PMC2632426/pdf/sbm114.pdf)

    The forest plot (Fig 1) in Wykes shows that 6 of the studies were definitely significant (possibly 1 or 2 'borderline significant') - Interestingly, you would be quite hard-pressed to see many of the nonsignificant studies standing up & highlighting this conclusion in their paper (as I have noted elsewhere in my blog (http://keithsneuroblog.blogspot.co.uk/2012/11/in-manner-of-speaking.html)
    Most strikingly, I am pretty sure NONE of the significant studies were blind at assessment outcome.
    So, contrary to Richard Bentall's #boldism - in the Wykes et al Meta Analysis, we have over 30 studies, the majority of which are poor quality (as defined by Wykes), most are nonsignificant and where significant, they are not blind ...hardly impressive enough for NICE to be advocating 'CBT for all people with schizophrenia'

    With regard to the Klingberg et al study - who knows where its at (Paging Prof Klingberg please?)

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  8. Hello Keith. I am one of the authors of the Wykes et al meta-analysis that you have been quoting.
    I can see many points have been made in recent comments, so I won’t attempt to address them all. For my part I see our meta analysis as an honest representation of a growing evidence base. You are right to make the points about what CBTp is compared against, and the importance of blind ratings. As you know, our meta analysis went further in that it rated a wide range of issues associated with methodological rigor, and in assessing for publication bias. The outcome of a modest but significant effect (in the higher quality studies) is one, I think, that is not getting carried away with itself.
    However, the intervention is relatively young, and developing rapidly. For me, a big message from our meta-analysis is that CBTp is still highly generic, and that we have been restrained for too long by the psychiatric system which imposes an outcome measure of generic symptoms as measured by the PANSS.
    Previous comments have highlighted the current focus/impact of CBTp on distress, and on trials which have specific targets such as command hallucinations. You stated you were unaware of this and asked for references. To help you with this, our meta-analysis reports outcome in relation to mood/depression, again a modest outcome. However current developments are aimed at a more specific targeting of emotional distress. I am surprised you are unaware of the work on command hallucinations as this is one of the trials (Trower et al, 2004) included in our meta-analysis. The fact that this study had a high effect size and the intervention target was highly specific is, for me, not a coincidence. This approach is being adopted within current developments which have specific targets such as worry, PTSD, insomnia and depression. We have to wait and see of course, but the hope (for patients) is that these will prove effective.
    To anticipate your response, I am not changing the goal posts as a ‘trick’. CBTp was originally forced to define itself as treating symptoms so as to be compared against drugs (and has shown a modest effect). Now it is determining outcomes in relation to what matters to patients.
    As said the current evidence base is modest, and I would be a quick as anyone to point it out if I thought anyone was over egging it. If there were a range of highly effective alternatives available then we should go for them. However, I do not see CBTp as having an easy ride, or being shoed in by influential supporters. It has emerged from a system dominated by traditional psychiatry and been challenged along the way. I am curious as to whether you think the developments I mention deserve to be funded or not. Whether the conclusion of your work is to stop thinking ahead. When asked for your suggestion of what a highly disadvantaged group should be offered in the way of psychosocial interventions, for something that may offer some hope, and not just a pill, your reply was befrienders/counseling. Presumably referring to the studies where these were a control group. This did really surprise me, as the evidence base for befrienders/counseling for psychosis is minimal, indeed weaker than for CBTp, albeit as you say cheaper. So it would seem to me that in a bid to avoid saying that the conclusion of your work is that nothing should be offered, you are suggesting this group are offered something with a weak(er) evidence base because it’s cheap.

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    Replies
    1. Hello Craig, thanks for your comments. Here are my responses
      1) For what it's worth, I think your meta-analysis with Til Wykes and co is both fair and rigorous in this field - though I also note you don't dispute anything I quote from your meta-analysis
      2) I am not sure CBT for psychosis is 'young' - we have had around 40 RCTs (as well as numerous case studies etc) and Beck started this work in the late 1950s - so I suppose it depends how you measure 'age'
      3) Distress - I dont mean to sound 'picky', but your meta-analysis never once mentions the word 'distress' - largely because it is rarely examined in CBT trials
      4) You say " our meta-analysis reports outcome in relation to mood/depression, again a modest outcome". Your MA shows that the effect size for low quality studies is over 8 times larger than for high quality studies (.68 vs .08) and furthermore, is nonsig in those studies of acceptable (high) quality
      5) I am, of course, familiar with the Trower et al study of command hallucinations (http://bjp.rcpsych.org/content/184/4/312.full.pdf+html)
      As readers can see in your own meta-analysis - Trower et al produced a massive outlying positive CBT effect - totally unlike anything ever recorded before ...or since!
      You say "this is not a coincidence' - I would say why has this one exception emerged? The authors had a large number of outcome variables (across time) - & most primary outcomes were, in fact, nonsig.
      Where hallucination changes were significant, the authors rightly remark "changes in power, distress/depression and omniscience (which were largely measured by self-report scales") - in other words....not blind (patients rated themselves)
      5) You mention the Trower study in the context of 'distress', but as I assuem you know, no differences in distress were present 12 months following CBT
      6) Regarding how I perceive your proposed shift of focus - away from the quasi-neuroleptic use of CBT for psychosis (ie treating symptoms) to "determining outcomes in relation to what matters to patients." - thsi is not new and was indeed called for by Trower (http://www.brown.uk.com/schizophrenia/birchwood.pdf) - but little data have emerged in the 7 years since his paper on this issue
      7) I see that, unfortunately like Richard Bentall, you finally resort to an avoiding the issues, saying:
      "Whether the conclusion of your work is to stop thinking ahead. ...it would seem to me that in a bid to avoid saying that the conclusion of your work is that nothing should be offered, you are suggesting this group are offered something with a weak(er) evidence base because it’s cheap."

      I was quite clear when asked - and regarding befriending/supp counseling, you are simply wrong! Please do point me to evidence that CBT is 'better' than these alternatives. In the meantime, my conclusion is supported here in the latest Cochrane 2012 review - (http://summaries.cochrane.org/CD008712/cognitive-behaviour-therapy-versus-other-psychosocial-treatments-for-schizophrenia) and here by the Newton-Howes & Wood in their meta-analysis (http://www.ncbi.nlm.nih.gov/pubmed/23674464)

      If you want to argue that CBT 'outperforms' active controls, then best to stick to discuss the data rather than painting me as some kind of callous luddite

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