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Psychosocial interventions and the likelihood reduction of subsequent suicide
suicide prevention, still elusive?
Inaccurate conclusions based on limited data
Re: Inaccurate conclusions based on limited data
Re: Re: Inaccurate conclusions based on limited data
Caution urged with meta-analysis
Authors reply
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Raafat S Labib Mishriky, SHO in Psychiatry North Staffordshire Combined NHS Trust
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raafatmishriky{at}hotmail.com Raafat S Labib Mishriky
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Raafat S Labib Mishriky, SHO in Psychiatry, Combined North Staffordshire NHS Trust, Lyme brook Mental Health center, Talke Road, Newcastle-under-Lyme ST5 7TL Phone: 07725127013 Email: Raafat.Labib@northstaffs.nhs.uk I agree with Crawford, Thomas and colleagues that the relative lack of statistical power in this meta-analysis means that caution is needed when interpreting the study findings. Although the data from the 18 studies appeared to be statistically homogenous, the clinical homogeneity appears to be ambiguous. Although, the Funnel plot of the studies was done to assess the possibility of publication bias. The inclusion of other studies which are non randomised or even small trials could have possibly given additional significant and clinically useful information. It was mentioned in the study that reducing the rate of suicidal behaviour is a national service priority in Britain and in many other countries. (Department of Health, 2002; World Health Organization, 2002). This was highlighted more than once by the authors. This appeared very interesting and It would have been more interesting to know in which country each of the studies selected for the analysis was done or whether all of the studies were done in the UK? This could have made the results of the study more generalised, and could have availed some outcomes in relation to a possible cultural context. However, it is clear that the authors have done good work in this meta-analysis of systematic reviews. But it is worth mentioning that the type of interventions offered in all the studies included were a limited number of sessions of individual psychotherapy such as cognitive behavioural therapy, interpersonal therapy or dialectical behavioural therapy. There are other forms of psychosocial interventions which could have been included in the studies selected such as Family interventions, Group therapy, assertive outreach, early intervention, home treatment and crisis intervention. The inclusion of such interventions could have affected the robustness of the outcome and the striking conclusion that this meta-analysis does not provide evidence that additional psychosocial interventions following self harm have a marked effect on the likelihood of subsequent suicide. Declaration of interest: None References: Department of Health (2002) National Suicide Prevention Strategy for England. Department of Health World Health Organization (2002) Suicide Prevention in Europe: The WHO European Monitoring Survey on National Suicide Prevention Programmes and Strategies. WHO Regional Office for Europe. |
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Sangeetha Chinnadurai, Senior House Officer, Leighton Hospital Sundaravaradan Asoka
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csangeeth{at}yahoo.co.uk Sangeetha Chinnadurai
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Risk management and suicide prevention is an integral component of effective psychiatric practice. There has been several interventions tried over the years, psychosocial methods like legislative measures of reducing the availability of the means to psychological therapies in the prevention of suicide. There has been many studies in identifying the demographic characteristics of population who commit suicide but the need to identify effective strategies to prevent suicide can only be done by large well conducted randomised controlled trials to detect significant effect size with large samples(John M Eagles, 2001). The systematic review of psychosocial interventions following self harm by the authors has reinstated its need of further research in this area. The systematic review has shown that most studies has been of 6 months duration with few studies of more duration. The suicides in the trials, have occurred when people have been followed for a longer duration, though we do not know the exact time of suicide from the date of self harm. This shows that the risk continues to rise with time. The review also includes different population groups and the intervention strategies may not be applicable to the varied population of old age and adolescents alike. Suicide also being a rare event, it is difficult to design studies of intervention strategies like psychotherapy of very long duration to see whether it would reduce the event following self harm. There are still unanswered questions of how long the interventions be provided to prevent the event. A retrospective analysis of admission to hospital of people following self harm concluded that overdoses with paracetamol has reduced but with antidepressants have increased, this adds to the need to recognise these risks effectively (Wilkinson, 2001). Though the individual studies have shown significant results, the systematic review has failed to detect significant difference and this shows a variety of psychosocial interventions with larger samples might give further insight in our search to prevent suicide and I am hopeful that it might not be elusive as it appears in future. References: John M Eagles etal: Role of psychiatrists in the prediction and prevention of suicide: a perspective from North East Scotland. British Journal of Psychiatry (2001), 178: 494 Stephen Wlikinson etal: Admission to hospital of deliberate self harm in 1995-2000: an analysis of hospital episode statisitics. Journal of Public Health Medicine 24:179-183 (2002) |
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M. David Rudd, Professor and Chair Department of Psychology, Texas Tech University
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david.rudd{at}ttu.edu M. David Rudd, et al.
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The authors conclude that results “do not provide evidence that additional psychosocial interventions following self-harm have a marked effect on the likelihood of subsequent suicide”. This conclusion is far too bold and definitive considering the weaknesses inherent to the analytic approach. Although the authors certainly considered, I’m not sure they have allowed for adequate weight and influence of several methodological problems. They provide a fairly detailed discussion of the “lack of statistical power” in the meta-analysis but, nonetheless, offer a definitive and sweeping conclusion. At best, this is ill-informed and, at worst, scientifically irresponsible. The lack of statistical power is only one reason not to do such a meta-analysis. Most importantly, though, the interventions were not developed nor intended to reduce suicide rates, they targeted subsequent attempts/behaviors and associated symptoms, with all of those directing the interventions clearly recognizing the low base rate problem up front. From a methodological perspective, the follow-up periods were far too brief and the samples too small to conclude anything definitive about “the likelihood of subsequent suicide”. The authors themselves note that five trials included follow-up of less than a year, with the rest only twelve months. From a clinical perspective, the authors fail to recognize the fluid nature of suicide risk and psychiatric illness, hence, the need for longer follow-up. It’s also arguable whether or not these trials are actually amendable to meta-analysis, with all of these studies targeting variable outcomes. Despite the ample caveats offered by the authors, they still offer a definitive and sweeping conclusion, one based on a flawed rationale, questionable methodology, and insufficient data. For the sake of scientific integrity, I would have hoped the authors would have waited for adequate numbers and enduring follow-up in order to offer sweeping conclusions. At a minimum, their conclusion is simply inaccurate. A more accurate statement is, “in light of serious methodological problems, we don’t yet have the data to address the impact of psychosocial interventions on subsequent suicide rates”. I’m also a bit mystified as to how these data even remotely reflect on population-based prevention studies and why a recommendation is made about means restriction? It almost appears as though there’s another agenda at work? To be quite blunt, I’m a little concerned this one made it through scientific review without harsher criticism. In an age when legislators and funding agencies rely on science for direction; it is studies like this that generate ill- informed conclusions on what interventions, treatments, and approaches to suicide prevention offer the most promise. Many readers will sadly and mistakenly carry away the message that psychosocial interventions offer no promise to reduce suicide rates. |
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Michael J Crawford, Reader in Mental Health Services Research, Department of Psychological Medicine Imperial College London
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m.crawford{at}imperial.ac.uk Michael J Crawford
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We fully endorse Rudd’s statement that an absence of evidence should not be misinterpreted as an absence of effect. Findings of our meta- analysis do not support the belief that additional psychosocial interventions following deliberate self harm reduce the rate of suicide, but wide confidence intervals around the pooled rate ratio mean that it is entirely possible that they do have such an effect. We highlighted this point in the paper, and are pleased to have the opportunity to do so again now. There are however several other points raised which do not agree with. Firstly, we believe that it can be appropriate to synthesise data from randomised trials to examine clinically significant rare outcomes that individual studies are unlikely to be able to detect. For instance, brief interventions for alcohol misuse are effective in reducing alcohol consumption, but a range of factors, including clinical inertia, mean that they are not widely delivered. By synthesising data from four randomised trials, Cuijpers and colleagues (2004) demonstrated that brief intervention is associated with a 30% reduction in subsequent mortality, a finding which may help to overcome some of the barriers to its delivery. Secondly, we do not know why Rudd is perplexed about our making a link between the impact that high-risk and population-based interventions aimed at reducing suicide. Policy documents and academic reports have repeatedly made such comparisons and we are not the first to conclude that population-based approaches may have a greater impact (Lewis et al, 1997). Finally, Rudd argues that we should have known enough about the likely impact of these interventions on suicide in advance not to have embarked in this meta-analysis. We disagree. Had other studies demonstrated an impact on suicide as great as the one reported in the trial of manualised cognitive therapy (Tyrer et al, 2003) we would have had ample power to detect a difference in the subsequent rate of suicide. Sadly other studies did not show this effect. At a time when official reports state that interventions following deliberate self harm are effective in preventing suicide (US DHSS, 2001), would it have been more scientifically responsible to have avoided presenting our findings because they did not demonstrate a positive effect? References Cuijpers, P., Riper, H. & Lemmers, L. (2004) The effects on mortality of brief interventions for problem drinking: a meta-analysis. Addiction, 99, 839-845 2004. Lewis, G., Hawton, K. & Jones, P. (1997) Strategies for preventing suicide. British Journal of Psychiatry, 171, 351-354. Tyrer P, Thompson S, Schmidt U, et al. (2003) Randomized controlled trial of brief cognitive behaviour therapy versus treatment as usual in recurrent deliberate self-harm: the POPMACT study. Psychological Medicine, 33, 969-976 U.S. Department of Health and Human Services. (2001) National strategy for suicide prevention: Goals and objectives for action. USDHHS, Rockville MD. Declaration of interest None. |
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M. David Rudd, Professor and Chair Texas Tech University
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david.rudd{at}ttu.edu M. David Rudd
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I appreciate the response of Crawford to the issues raised in my previous letter, partcularly that "an absence of evidence should not be misinterpreted as an absence of effect". There are a number of other points in the reply to which I would like to respond. First, I must disagree with the statement that "offical reports state that interventions following deliberate self-harm are effective in preventing suicides" (US DHHS, 2001). Having again reviewed the National Strategy goals and objectives, I cannot find any such statement. Actually, it's the very language in the National Strategy that I would endorse. It's necessarily cautious and specific to the limitations in the literature. Although the goals and objectives articluate there are many approaches to suicide prevention (e.g. means restriction, treatment of mental illness, enhancing social support and reducing stigma) I could not find a statement that indicated any have been proven effective at reducing subsequent suicide rates. The National Strategy uses appropriately cautious language, something I suggested the article could have done more effectively. I again disagree with the interpretation of the Tyrer et al. (2003) study. Follow-up of 6 to 12 months is simply inadequate to test the hypothesis that a psychosocial intervention can reduce subsequent suicide rates. Many, if not the majority, of the diagnostic problems targeted by all of the psychosocial studies included in the meta-analysis are recurrent, persistent and chronic in nature. We'll only know the efficacy of treatment after 5, 10, or 20 years. There's an implicit assumption regarding "immediacy of treatment effect" that's puzzling, at least from a clinical pespective. From my vantage point, it's a flawed assumption for the meta-analysis. Even if we saw a reduction, we really wouldn't know if the treatments were "delaying" suicide or actually preventing it unless we get longitudinal data. The "state of the science" in treatment research targeting suicidality is far from adequate and extensive. I'm concerned that the definitive nature of the conclusion offered by Crawford et al. doesn't adequately reflect those limitations. As a simple example, we are yet to understand fundamental distinctions between imminent, acute and chronic risk, although some interesting findings are emerging (and converging) with respect to multiple suicide attempters and chronic risk (e.g. Rudd et al., 1996; Forman et al., 2004). I would agree with Crawford that an argument can indeed be made to support the meta-analytic approach, but I would suggest it's not compelling. A review of the treatment protocols of the studies included reveals wide variability in the nature, oversight and fidelity of the treatments offered. Prior to inclusion in a meta-anlysis, I would suggest a critical review of the treatment approach and associated fidelity. Only those meeting strict criteria would be included. Otherwise, the sample for the meta-analysis is further weakened by studies of questionable fidelity. One or two bad apples in this case (with small samples and limited follow- up) can indeed ruin the barrel. Having reviewed the treatment literature (and protocols) in detail, I would suggest a number of studies should not be included due to considerable methodological problems (cf. Rudd, Joiner, & Rajab, 2004). Finally, my confusion about the population-based comments in the conclusion reflect my concern that they did not provide a review of that data yet suggest potentially greater impact. In light of the problems noted above and previously with the meta-analysis, the comment strikes me as somewhat dismissive of the psychosocial treatment literature, suggesting that the meta-analytic results offer some firm conclusions. I simply do not believe that is the case. The concern I have is that non- scientists may not be in a position to come to that conclusion independently. References: Forman, E., Berk, M., Henriques, G., Brown, G., & Beck, A. (2004). History of multiple suicide attempts as a behavioral marker of severe psychopathology. American Journal of Psychiatry, 161 (3), 437-443. Rudd, M., Joiner, T., & Rajab, H. (1996). Relationships among suicide ideators, attempters and multiple attempters. Journal of Abnormal Psychology, 105, 541-550. Rudd, M., Joiner, T., & Rajab, H. (2004). Treating suicidal behavior. Guilford: New York. U.S. Department of Health and Human Services (2001). National strategy for suicide prevention: Goals and objectives for action. USDHHS, Rockville MD. |
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M. David Rudd, Professor and Chair Texas Tech University
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david.rudd{at}ttu.edu M. David Rudd
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Crawford, Thomas, Khan, & Kulinskaya (2007) conclude that results “do not provide evidence that additional psychosocial interventions following self-harm have a marked effect on the likelihood of subsequent suicide”. This conclusion is far too bold and definitive considering the weaknesses inherent to the analytic approach employed. Although the authors certainly considered, I don’t believe they’ve allowed for adequate weight and influence of several methodological problems, the most prominent being the rationale for including studies in the analysis. They acknowledge the “lack of statistical power” in the meta-analysis but, nonetheless, offer a definitive and sweeping conclusion, one that is at best ill-informed and, at worst, scientifically irresponsible. The lack of statistical power is only one reason not to conduct the meta-analysis. The central rationale for clustering the studies included in the meta-analysis is seriously flawed. Not only have they mixed simple interventions and treatments, the target populations range from latency- age children (some as young as 12) to older adults (50+), intervention methods and theoretical orientations vary considerably (employing individual, group, case-management and home-based care), samples include those making suicide attempts as well as those engaging in self-harm (non- suicidal) behavior, but they’ve also included studies that employed, at best, questionable intervention or treatment protocols for suicidality. A review of the intervention and treatment protocols of the studies included reveals wide variability in the nature, oversight, and fidelity of the services being offered. Actually, I have serous concerns about at least 8 of the 19 study protocols. Some of the interventions cannot realistically be described as appropriate for suicidality, at least from the perspective that they have a serious chance at reducing subsequent pathology or suicide attempts, much less actual deaths. For example, Harrington et al. (1998) employed “four home visits by a social worker”. Similarly, the Guthrie et al. (2001) study included “four sessions delivered in the patient’s home”. The study included by Cedereke et al. (2002) explored the utility of “random telephone interventions”. The Clarke et al. (2002) study included “management enhanced by nurse-led case management”. As these examples illustrate, not all psychosocial interventions are the same, something Crawford et al. (2007) failed to clearly reveal in their article. Why would we expect that a meta-analysis of randomized trials of interventions or treatments that are this broadly disparate (with samples equally disparate) would actually prove effective at reducing subsequent suicides? Meta-analytic approaches have become increasingly popular and, accordingly, increasingly misleading in their findings. Prior to inclusion in a meta-analysis of intervention or treatment outcome, and not just for suicidality, I would suggest a thorough review of the intervention/treatment approach and related fidelity. Only those meeting strict and pre-defined criteria should be included. In this case, it looks like only about half of those studies included are actually similar in nature, with similar targets. When considering strategies for including and clustering treatment studies for meta-analysis, it’s particularly important to consider the targeted problem or disorder. Many, if not the majority, of the diagnostic problems targeted by the psychosocial interventions and treatments are recurrent, persistent, and potentially chronic in nature. Hence, the need for careful scrutiny of studies included. Compounding the problems noted above, the follow-up periods for ALL of the studies included ranged from 6 to 12 months. We’ll only know the efficacy of treatment or interventions for suicide after 5, 10, or 20 years. The implicit assumption regarding the immediacy of treatment or intervention effect is quite puzzling, at least from a clinical perspective. Even if the results did show a reduction in subsequent suicides, we really wouldn’t know if the interventions or treatments were “delaying” suicide or actually preventing it unless we get longitudinal data. There are a host of other problems that need to be scrutinized prior to inclusion in a meta-analysis (e.g. sample size, categorization of attempt status and suicide intent, fidelity/oversight of intervention or treatment), but space does not allow a full discussion. The point is that identifying appropriate inclusion criteria for such a study is a complex process. It’s far more complicated than simply taking “all randomized controlled trials”. The definitive nature of the conclusion offered belies the current state of the science in this area. In an age when legislators and funding agencies rely on science for direction, studies like this one generate ill -informed conclusions on what interventions, treatments and approaches to suicide prevention offer the most promise. Many readers will sadly and mistakenly carry away the message that psychosocial interventions offer no promise to reduce suicide rates. _________________________ Cedereke, M., Monti, K., & Ojehagen, A. (2002). Telephone contact with patients in the year after a suicide attempt: Does it affect treatment attendance and outcome? European Psychiatry, 17, 82-91. Clarke, T., Baker, P., Watts, C.J., et al. (2002). Self-harm in adults: A randomized controlled trial of nurse-led management versus routine care only. Journal of Mental Health, 11, 167--176. Crawford, M.J., Thomas, O., Khan, N., & Kulinskaya, E. (2007). Psychosocial interventions following self-harm: Systematic review of their efficacy in preventing suicide. British Journal of Psychiatry, 190, 11-17. Guthrie, E., Kapur, N., Mackway-Jones, K., et al. (2001). Randomized controlled trial of brief psychological intervention after deliberate self -poisoning. BMJ, 323, 135-138. Harrington, R., Kerfoot, M., Dyer, E., et al. (1999). Randomized trail of a home-based intervention for children who have deliberately poisoned themselves. Journal of the Academy of Child and Adolescent Psychiatry, 37, 512-518. |
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Mike J Crawford, Academic psychiatrist Imperial College London, Olivia Thomas
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m.crawford{at}imperial.ac.uk Mike J Crawford, et al.
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Rudd raises important questions about whether it was appropriate to undertake this meta-analysis given the nature of interventions studied and the length of follow-up periods used. We believe that it can be appropriate to synthesise data from randomised trials to examine clinically important rare outcomes that individual studies are unlikely to be able to detect. For instance, psychosocial interventions for alcohol misuse are effective in reducing alcohol consumption, but a range of factors, including clinical inertia, mean that they are not widely delivered. By synthesising data from trials conducted in a range of different settings, Cuijpers and colleagues (2004) demonstrated that they are associated with a 30% reduction in subsequent mortality, a finding which may help to overcome some of the barriers to their delivery. Although none of the studies we examined set out specifically to try to reduce suicide, it seems logical that interventions that are designed to reduce the incidence of suicidal behaviour should impact on the likelihood of fatal as well as non-fatal deliberate self-harm. While several studies we included involved only brief interventions, such interventions have been shown to reduce the likelihood of suicide in other contexts, for instance in the period following discharge from inpatient psychiatric care (Motto & Bostrom, 2001). Most of the studies we included followed people up for between 6 and 12 months after the initial episode of self-harm. While this is a relatively short period it is also the period during which suicide is most likely to occur (Owens et al. 2002). By focussing on this period we maximised the likelihood of being able to demonstrate an impact on the rate of suicide. However we fully endorse Rudd’s comment that results of our meta- analysis need to be interpreted with caution. Lack of data on suicide deaths in several of the trials that we identified meant that study power was limited. This resulted in wide confidence intervals around the pooled difference in suicide rates and it is therefore possible that additional psychosocial interventions do lead to reductions in subsequent suicide. References Cuijpers, P., Riper, H. & Lemmers, L. (2004) The effects on mortality of brief interventions for problem drinking: a meta-analysis. Addiction, 99, 839-845 2004. Owens, D., Horrocks, J., & House, A. (2002) Fatal and non-fatal repetition of self-harm. Systematic review. British Journal of Psychiatry, 181, 193-199. Motto, J. A., & Bostrom A.G. (2001) A randomized controlled trial of postcrisis suicide prevention. Psychiatric Services, 52, 828-33. |
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