What would cardiology do? Lessons from other medical specialties should help guide suicide prevention research

Abstract

Suicide is among the most important causes of mortality in medicine as it is the most common cause of death due to illness from the teenage years into middle age. Yet our approach to mental health research aimed at suicide prevention has often diverged from accepted practices in other areas of medicine. This includes the exclusion of those at highest risk of suicide from clinical trials and the recent emphasis on prediction. In this Viewpoint, we propose that comparing our approach to that of other medical specialties would help us to avoid strategic errors and discuss the implications for the field of suicide prevention.

Psychiatry is a branch of medicine and, given our increasing understanding of the societal burden of mental illness by both health experts and the public, it is arguably one of the most important medical specialties of the 21st century. Yet because of historical misunderstandings and past stigma, researchers and clinicians in our field have often forged a path which diverges substantially from accepted practices in other areas of modern medicine. We suggest a rethink is in order starting with a simple litmus test for decisions about how best to advance our field in the future: ‘Would other areas of medicine take the same approach with their major challenges?’ As suicide prevention researchers, we believe that pausing in this way can help us to avoid unnecessary errors in strategy and we will highlight one – the scientifically problematic emphasis on prediction – which is currently in vogue in suicide research and which is diverting key resources and human capital that could be directed more productively.

Suicide, like other major causes of mortality, has both psychosocial and medical antecedents whose interaction with healthcare delivery models and clinical interventions should be the focus of extensive study. Yet, with regard to advancing our understanding of suicide prevention, mental health research has often strayed from proven models for the design and interpretation of research to the detriment of our field and our patients. One egregious example is the long-standing practice of excluding suicidal patients from research trials due to concerns that some of them might die while in the trial, thus calling into question the safety and efficacy of the study intervention (Ballard et al., 2017). Indeed, clinically significant suicidal ideation was found to be an exclusion criteria in 75% of antidepressant randomized controlled trials and that rate appears to be increasing over time (Zimmerman et al., 2015). This despite the fact that suicide deaths that occur in the context of a research protocol, while tragic, would provide us with crucial information that could help better prevent suicides in the future. In recent years, there have been some belated calls to reverse this practice (Ballard et al., 2017) and several brave clinical researchers have been at the forefront of that effort (Linehan et al., 2015; Oquendo et al., 2011). But leaders in our field, and the regulatory agencies that set standards for our trials, ought to be making a much stronger push towards requiring suicidal patients to be included in clinical trials. Imagine if oncology researchers excluded patients at increased risk of death from cancer from their trials? Our field must align with the rest of medicine which has taught us that, if anything, it is often unethical to bar those at risk of our worst outcome from efforts to improve outcomes.

Another example in which mental health research has deviated from other areas of healthcare is the widespread, Quixotic, quest to predict suicide deaths (Large, 2018). It is true that nearly 1 million people die by suicide each year (World Health Organization (WHO), 2019); however, given that suicide can occur at any phase of life from youth to old age, it is an exceedingly uncommon event at any specific time (Glenn and Nock, 2014). Many well-meaning researchers have tried to address this issue by developing models and algorithms in the hopes of detecting these proverbial needles in the haystack (Whiting and Fazel, 2019). But they are neglecting two key lessons from our healthcare colleagues which would make clear why this endeavour is ultimately unlikely to succeed.

The first is that medicine has no history of reliably predicting sentinel events. Our colleagues in cardiology are able to use machine learning to identify patients at low and high risk of a myocardial infarction (Than et al., 2019), but they cannot determine exactly which of their patients will have coronary artery occlusion and when. Likewise our peers in neurology cannot identify who among their patients will experience a stroke and when (Li et al., 2016), despite the fact that this process is also less complex than the behavioural endpoint that is suicide. You cannot train a computer to play chess if it is unable to play checkers. Success in prediction technology in these other areas might signal the possibility that we may be able to achieve the same for suicide at some point. But, for now, pinpointing exactly when suicide will occur and in whom remains an unrealistic goal.

To understand the second lesson, we must appreciate that suicide is not a ‘silent killer’. Major depressive disorder, for example, is a crucial driving factor in about half of all suicide deaths and is also a top cause of morbidity worldwide (Turecki and Brent, 2016). Therefore, we are ethically obliged to care for all such patients whether or not they will ultimately die by suicide. Even if we could reliably predict who will die, it would not change the fact that gold-standard treatment, the kind that could prevent suicide, should be applied as broadly as possible.

Certainly nuanced differences could arise out of a better appreciation of risk. And this is what we must learn from our cardiologist colleagues who famously pioneered the Framingham scoring system (Lloyd-Jones et al., 2004). The well-established practice in medicine of risk stratification is simultaneously what our colleagues who say they are doing prediction are actually working on and what could, understood through that prism, advance the field of suicide prevention. Given that so-called ‘low risk’ patients account for the majority of suicides at a population level (Kapur et al., 2005), the goal would be to offer outstanding care to all but also to direct enhanced treatments and resources to high-risk patients at high-risk times. This sort of approach has helped lower rates of death from cardiac causes in recent decades (Mensah et al., 2017), and there is no reason to suspect it would have a different impact if applied rationally to suicide.

Mental health and suicide research remain inadequately funded and one additional concern with the emphasis on prediction is that it diverts already scant resources away from our most important potential avenue of investment – intervention studies. Our colleagues in medicine rightly place a high value on intervention research and we must align more closely with that ethos in mental health. A number of novel treatments including biological interventions such as ketamine, psychotherapeutic interventions such as Collaborative Assessment and Management of Suicidality (CAMS), and safety interventions such as Patient Safety Plans have emerging evidence (Kalin, 2019) and our top priority must be to study these interventions and to develop more.

Ultimately, we all want to see fewer suicides across the population, in our clinical trials and in our offices. Suicide is complex and perhaps it is only natural that we sometimes adopt approaches that seem useful but go beyond what is practically feasible. The bulwark to such unforced errors can be a willingness to learn from our colleagues across the world of medicine. Doing so will help us save the most patients. We do otherwise at their peril.