Voluntary Firearm Divestment and Suicide Risk: Real-World Importance in the Absence of Causal Identification : Epidemiology

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Injury Epidemiology

Voluntary Firearm Divestment and Suicide Risk: Real-World Importance in the Absence of Causal Identification

Rudolph, Kara E.; Keyes, Katherine M.

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Epidemiology 34(1):p 107-110, January 2023. | DOI: 10.1097/EDE.0000000000001548
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Suicide in the United States has increased by more than 30% in the past 20 years.1 While available data indicate that the rate of suicide has stabilized and even decreased among some groups during the COVID-19 pandemic,2 in 2020, a recorded 45,855 people in the US died by suicide. Before 2020, increases occurred across every age and major demographic group, including youth.3 Suicide is preventable, and most suicidal crises are temporary and treatable.4,5 Urgent efforts towards prevention are scaling up, including a new national number for mental health support (#9-8-8).

In the United States, approximately half of suicide deaths are by firearm, and the proportion of suicides by firearm has remained relatively static.4 Firearms are a highly lethal means of intentional self-harm, and a firearm in the home is a strong risk factor for suicide death.6,7 During a suicidal crisis, reducing access to lethal means is critical, especially given the evidence that most people who survive a suicide attempt do not re-attempt.4

Given the public health burden of suicide in the United States and the central contribution of firearms to intentional self-harm, restricting access to guns among those at high risk of suicide is a key public health strategy. The analysis by Swanson et al. demonstrates that legal owners of a single handgun in California are at more than four times higher risk of suicide than the general adult population of California, and it evaluates whether voluntarily divesting from ownership reduces suicide risk.8 While the public health and policy implications of this analysis are clear and compelling, we are concerned that the assumptions necessary for causal identification are untenable. That said, the authors’ pursuit of causal identification may be unnecessary for the practical purpose of informing firearm suicide prevention efforts.


Swanson et al. state that their goal is to estimate the causal effect of handgun divestment, among single handgun owners in California, on the risk of suicide, overall and separately by whether or not a firearm was used.8 In estimating this causal effect, the authors follow the target trial framework, which is essentially a roadmap for applying counterfactual theory to identify the causal effect of interest (i.e., causal estimand) and “provides a structured process” to avoid common methodologic pitfalls in the analysis.9,10 However, the authors are not able to emulate a target trial, because identification of the causal effect is not possible due to intractable, strong unobserved confounding.

To satisfy the identification assumption that divestment (itself a rare exposure; only 2% of their sample divested) is essentially randomly distributed conditional on observed variables, the authors would need to control for all variables that are related to whether or not the individual divested their handgun and are also related to suicide.9 These factors, as the authors acknowledge, may include mental health issues and illness, such as depression; cognitive decline or dementia; other poor physical health; loss of income or wealth; and criminalized activity or history.

Indeed, considering these factors a-priori as possible confounders makes intuitive sense when one considers the possible reasons why gun owners divest. First, gun owners may divest because of a court order to divest due to danger to self or others under a Red Flag/Extreme Risk law.11 Thus, divestment under this mechanism would support a link between divestment and (1) criminalized activity and/or (2) mental illness (e.g., suicidal crisis). Second, gun owners may divest as part of a general parting of possessions before death. Divestment under this mechanism would support a link between terminal illness, possibly including dementia, and divestment. Third, gun owners may divest because of the financial incentive offered by gun buy-back programs. Divestment under this mechanism would support a link between acute financial hardship and divestment. However, none of the above variables are measured, meaning that there are multiple, strong unobserved confounders that render the causal effect unidentified.


So then what is the path forward when a causal effect is not identified?

  1. The first step is to acknowledge that causal effect estimation is not possible; that target trial emulation is not possible. As stated in Hernán and Robins: “If the observational database does not contain sufficient information on baseline confounders or if we fail to identify them, successful emulation of the target trial’s random assignment is not possible.”9
  2. A second, optional, step is to perform sensitivity analyses for unobserved confounding. Swanson et al., conduct such a sensitivity analysis using the bias formulas of VanderWeele and Arah.12 While these bias formulas are useful, they make a simplifying assumption that the unobserved confounder is a single, binary, variable.12 However, as the authors point out, and as we enumerated in the above section, there are multiple strong unobserved confounders, some of which are continuously distributed. Treating multiple confounders, some of which are continuous, as a single, binary confounder can introduce measurement error, which can itself then become a significant source of unobserved confounding.13
  3. A third, optional step, is to estimate a statistical parameter that does not have a causal interpretation. Although this step is optional, it can be critically important, recognizing that just because a causal effect cannot be estimated, that does not mean all is lost. A recent paper by Wong and Balzer14 in this journal provides an example of estimating a potentially informative and useful statistical parameter when the casual effect was unidentified. In this example, Wong and Balzer estimated the association between early implementation of state-wide mask mandates and COVID-19 cases and deaths, finding evidence of a strong association, though the causal effect was unidentified due to unobserved confounding.14
  4. Finally, a fourth, optional step is to change the research question, causal estimand, and/or data, so that an estimand of interest is identified. Another recent paper in this journal walks through an example of this process.15 For example, a similar research question as the one asked by Swanson et al. could be addressed by using different data. A randomized trial is currently being conducted to evaluate California’s Armed and Prohibited Persons program16 in which law enforcement physically removes guns from prohibited persons (essentially an enforced Red Flag law). Data from this trial will likely allow for the identification of the causal effect of involuntary divestment of guns from individuals who are prohibited from having them at risk of suicide (noting that there is a pertinent distinction between voluntarily divesting and involuntarily divesting).


As stated in Step 1, it is important to acknowledge that casual effect estimation is not possible when the assumptions required for identifiability are violated. Instead, as stated in Step 3, an alternative, and perhaps next-best parameter to estimate is a statistical parameter that is not imbued with a causal interpretation, but which could still be well defined if the positivity assumptions are met. For example, in the Swanson et al. paper,8 such a statistical parameter would be the adjusted relative risk or the adjusted difference in risk of suicide (any, and separately by firearm involvement) associated with comparing divestment to no divestment.

One may wonder, though, if there is much value in estimating a statistical, non-causal, parameter. Perhaps the best-known example of where the causal effect was not identified, but where the statistical parameter was still useful, in combination with a sensitivity analysis for unobserved confounding (Step 2), is the example of cigarette smoking and lung cancer in the seminal paper by Cornfield et al.17 In this paper, Cornfield et al. acknowledged that the identifiability assumption of conditional exchangeability may not be met in observational data. However, he argued that the estimates of the statistical parameter representing the association between cigarette smoking and lung cancer were so large that the strength of unobserved confounding would need to be similarly enormous to explain away the association; the unobserved confounder would need to almost perfectly predict lung cancer, be nine times more prevalent in smokers than nonsmokers, and be 60 times more prevalent in two-pack-a-day smokers than nonsmokers. Considered together, this evidence was, in his words, “sufficient for planning and activating public health measures.”17,18

In reality, Swanson et al. also estimated noncausal statistical parameters. They too estimated strong associations. Swanson et al. estimated that handgun divestment was associated with a 68% increased risk of suicide in the per-protocol analysis (which compared those who divested and did not re-purchase to those who did not divest) and a 94% increased risk in the intent-to-treat analysis (which compared those who divested but may have re-purchased to those who did not divest).8 The authors estimated that handgun divestment was even more strongly associated with the risk of nonfirearm suicide, associated with a >700% increased risk. If coupled with a sensitivity analysis accounting for the likely multiple named unobserved confounders, such estimates could provide valuable evidence that effects between divestment and suicide exist.

The above example and discussion assume the presence of a true casual effect of the exposure on the outcome (depicted in the directed acyclic graph (DAG) in Figure 1A. But it is also possible that estimating statistical parameters could be useful even in the absence of a true causal effect between divestment and suicide. We give an example of this in the DAG in Figure 1B. In Figure 1B (which matches Figure 1e in Joffe and Greene),19 divestment would be a proxy surrogate for suicide, though there is no causal effect of handgun divestment on suicide. (In Figure 1B, divestment is a proxy for suicidal ideation, which itself would be considered a surrogate for suicide, where a surrogate is defined as “an outcome for which knowing the effect of treatment on the surrogate allows prediction of the effect of treatment on the more clinically relevant outcome.”19) If Figure 1B, represents the truth, the statistical parameter Swanson et al. estimated could still be of value, as evidence that divestment is a predictor of suicide risk. The authors point out that the strength of divestment as a predictor of suicide is on-par with depression and other serious mental illnesses.8 Although predictors should not be equated with diagnostic markers (e.g., most people who divest their handguns do not commit suicide, just as most people who are depressed do not commit suicide), it may nevertheless suggest an opportunity for intervention. Just as the postpartum period represents a period of increased depression risk for women, resulting in public health interventions and depression screenings during this period, voluntary divestment could also represent a period of increased risk and opportunity for the potential suicide risk screening of individuals who recently divested. Swanson et al. speculate that it may be valuable to incorporate suicide prevention efforts at the time of divestment, e.g., at gun buy-back programs.8

Figure 1.:
Example-directed acyclic graphs. [Casual effect of divestment on suicide. U,W represent unobserved and observed confounders, respectively.} [No causal effect of divestment on suicide. U 1, U 2 represent unobserved confounders; note that suicidal ideation is unobserved.}.


While debates about the specifics of causal assumptions and analytic choices are appropriate in the pages of Epidemiology, we should remain attuned to the fact that in these data, 19,926 people died by suicide, many by firearm. The suicide rate in this sample of gun owners was extraordinarily high—over four-fold higher than the general population of California over age 21 during the same time. These rates are indicative of a population that needs urgent support for both firearm and non-firearm suicide prevention.

Given the need for public health efforts in communities of gun owners, it is all the more important that our science of suicide research points to ways to reduce risks. Because of the politicized nature of firearm access and restrictions, research on this topic is highly visible. The data and analyses by Swanson et al. contain valuable information demonstrating the dangerously high risk of suicide among firearm owners and corroborates the decades of research documenting the lethal and destructive consequences of firearm ownership. As noted by the authors as well as other scholars, divestment sits within other evidence-based approaches to reducing firearm suicide, including safe storage, Red Flag laws, and other approaches.20 Continuing to support research to identify additional ways to prevent both firearm and non-firearm suicides is critical to saving lives.


Kara Rudolph is an Assistant Professor of Epidemiology at Columbia University. She studies casual inference, substance use disorders, and violence. Katherine Keyes is a Professor of Epidemiology at Columbia University. She studies psychiatric disorders, substance use disorders, and injuries including overdose and suicide.


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firearm; suicide; causal inference; identification; target trial; surrogacy

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