In “The Effect of Changes in Firearm Mortality on Nonfirearm Deaths: A Systematic Review and Meta-Analysis of the Impact of Firearm Laws” (p. 1545), Smart et al. take a thorough and methodologically sophisticated approach to estimating the net effect of state-level firearm legislation on homicide and suicide using data from the small number of extant studies that met their thoughtful inclusion criteria.

Smart et al. use a meta-analytic measure, the mortality multiplier (m), to express the effect of firearm-focused legislation as a change in the total number of violent deaths for a unit change in firearm deaths. For example, if m = 0.8 for the effect of a given set of firearm laws on homicide, for every 10 firearm homicides averted by the laws there would be two additional nonfirearm homicides that would not have occurred in the absence of the laws, resulting in eight homicides averted. Thus, the mortality multiplier is an index of the extent of lethal substitution of nonfirearm means when firearm deaths decline (increase) and of contagion, or secondary feedback effects, on nonfirearm homicide when firearm deaths increase or decrease. The construct, m, implicitly assumes that (1) the point estimates from the literature used in the meta-analysis are reasonable estimates of the direct causal effect of the law in question on firearm suicide and firearm homicide, and (2) changes in nonfirearm outcomes (referred to as second-order effects) are caused by the first-order changes in firearm fatalities. The mortality multiplier does not differentiate lethal substitution from contagion.

Putting aside for the time being whether these assumptions are warranted for homicide, suicide, both, or neither and, more fundamentally, whether the legislation evaluated plausibly causes large enough changes in exposure (i.e., firearm availability) to produce observable changes in mortality, the authors’ finding with respect to homicide is striking. With a mortality multiplier of 0.99, firearm laws that reduce firearm homicide are associated with virtually no second-order mortality effects—no compensatory increase in nonfirearm homicide (i.e., lethal substitution) and no virtuous decrease in nonfirearm homicide from negative feedback (i.e., contagion mitigation). It is worth noting that this general finding is not new, but rather comports with earlier approaches to assessing the possibility of means substitution and contagion that have found an instrumental, rather than an incidental, role of firearms in encounters that put people at risk for homicide.

For example, Cook¹ evaluated robbery over time for 43 large cities and found that rates of robbery-homicide were tightly related to whether firearms were used in the robbery: an increase of 1000 gun robberies resulted in three times as many additional deaths as an increase of 1000 nongun robberies; little else distinguished the encounters. Cross-sectional population-level data also suggest minimal lethal substitution of nonfirearm methods for firearms in places where household firearms are less prevalent. For example, the association between state-level household firearm prevalence and homicide victimization is driven by gun-related homicide rates, with non–gun-related homicide rates showing no material association with household firearm prevalence.^2,3

Smart et al. conclude that the available literature does not yet support estimation of a mortality multiplier for suicide. In particular, although the meta-analysis that generated the mortality multiplier for homicides drew on 16 studies, only a single study,⁴ of child access prevention laws, effectively determined the meta-analytic m for suicides. Moreover, as Smart et al. note, the direct effect measure used to calculate m from this study was based on the reported effect of child access prevention laws on those aged 18 to 20 years, rather than on those aged 14 to 17 years, even though those aged 18 to 20 years were chosen as negative controls by the original investigators. The authors rightly do not use the point estimates of those aged 14 to 17 years, because the published point estimates for firearm suicide, overall suicide, and nonfirearm suicide for this age group are internally inconsistent.

Unable to estimate a stable mortality multiplier for suicide, Smart et al. call for further research to determine whether “policies that produce population-level reductions in firearm suicides will translate to overall declines in suicide rates” (p. 1545). Although reasonable, this exhortation conflates two distinct issues: (1) whether legislative firearm policies that exist in the United States today produce quantitatively meaningful changes in exposure to guns sufficient to result in discernable population-level changes in rates of suicide, and (2) whether interventions that could produce quantitatively meaningful changes in exposure to firearms would, in fact, result in reductions in overall suicides, not simply in firearm suicides. Far stronger evidence supports the second idea than the first. Indeed, studies from other countries have shown that when population-level policies substantially reduce the ready availability of highly lethal, culturally acceptable, commonly used methods of suicide (e.g., coal gas [CO₂], pesticides in Sri Lanka, firearms in the Israeli military), sustained declines in overall suicide results, driven by declines in suicide by the restricted method, with minimal compensatory increases in suicides by nonrestricted methods.⁵

Moreover, a large and compelling body of empirical studies supports a causal connection between access to firearms and the risk of dying by suicide, driven, in effect, by an elevated rate of firearm suicide, with at best modest lethal substitution of nonfirearm methods. Consider, for example, the largest and most recent of the individual-level studies that contribute to this evidence base: a cohort study that identified handgun acquisitions and deaths among 26 million residents of California, aged 21 years or older, who had not previously acquired handguns.⁶ Cohort members were followed for up to 12 years; nearly 18 000 died by suicide, of which almost 7000 were suicides by firearm. Rates of suicide by any method were higher among handgun owners, with an adjusted hazard ratio (HR) of 3.7 for handgun owners compared with nonowners. These rates were driven by rates of suicide by firearm that were nine times higher and by relatively little substitution of suicide by nonfirearm methods (HR = 0.7; 95% confidence interval = 0.6, 0.8). In short, handgun ownership was associated with a greatly elevated and enduring risk of suicide by firearm, with minimal second-order substitution effects. Taken as a whole, empirical evidence strongly suggests that were policies or other interventions in place that did, in fact, materially reduce exposure to firearms at the population level, declines in overall suicide would result.

The meta-analytic article in the current issue of AJPH is carefully written and admirably detailed. The authors are transparent about their methods, generous in sharing their code, and thoughtfully inclusive of sensitivity analyses that together help the reader place the findings in proper context. In so doing, Smart et al. usefully add to the methodologic toolkit available to firearm researchers. The appendices and supplemental materials provided are also a boon to anyone interested in the topic. The materials are both comprehensive and informative and point out, in the winnowing down from hundreds to fewer than 20 studies that meet their criteria for inclusion in the analysis, the poverty of much of this literature. One criterion, responsible for jettisoning more than 40 peer-reviewed studies from consideration, deserves special mention: studies must compare outcome measures before versus after legislation was enacted (i.e., no cross-sectional analyses). That so many necessarily uninformative cross-sectional studies have been and continue to be published, including in AJPH, is a sobering reflection of how far short of the standards adopted by Smart et al. are those that have too often governed the peer review process and editorial stewardship, at least as it pertains to studies that purport to quantify the effect of firearm legislation.

Any work, including the meta-analysis published in the current issue, that seeks to evaluate how legislative policies affect mortality will be hampered to the extent that measuring exposure remains a largely unmet challenge. A national firearms registry, like the one that made the California cohort study possible, would allow researchers to approximate, rather than assume, changes in firearms availability induced by legislative policies. What we know already, however, is that if we can develop interventions that do, in fact, meaningfully change access to firearms, particularly among people at elevated risk for suicide, lives will be saved.

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