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In a recent, excellent study that found handgun purchase to be a risk factor for violent death, Grassel and colleagues gave explanations for why their findings may have inaccurately characterized the impact of handgun purchase on violent death, leading to results that if anything underestimate the magnitude of the danger associated with buying a handgun.1 “The healthy handgun purchaser effect”, which we suggest is akin to the healthy worker effect, may be a source of bias as well. Bias from this source could produce results that either underestimate or overestimate the impact of a handgun purchase on violent death. When dead controls are used in a case-control study, the death rate due to the comparison cause(s) should be equal in the exposed and unexposed populations.2–6 If this assumption is met, the odds ratio (OR) can be used as an estimate of the mortality density (or rate) ratio:
where a and c are exposed and unexposed cases and b and d are exposed and unexposed controls, respectively, and TE and TĒ are the person-time contributed by exposed and unexposed subjects, respectively. We follow Morgenstern and use his notation,6 but notation used by others is similar.2,4,5 In the present context, the OR represents the rate of violent death in handgun purchasers versus non-purchasers (mortality density ratio, MDR) relative to the rate of non-violent death in handgun purchasers versus non-purchasers (MDR′). If MDR′ equals 1, which occurs if the exposed and unexposed populations do have equal rates of death from the comparison (non-violent) cause(s), the person-time denominators cancel out, the formula collapses to the familiar ad/bc (that is, the formula to calculate an OR from a 2 × 2 table), and the OR provides an unbiased estimate of MDR. However, if the exposed and unexposed populations do not have equal rates of death from the comparison (non-violent) cause(s), MDR′ may not equal 1. In this instance, the OR will provide a biased measure of the parameter being estimated (that is, MDR). Even though the authors excluded from the comparison group causes of death that had clear associations with the purchase of a handgun, bias could still exist if handgun purchasers were “healthier” or less healthy than non-purchasers. For instance, consider that heart disease was the most common cause of death in California in 1998, accounting for 31% of all deaths.7 Therefore, a proportion of subjects who comprised the comparison group in this study could reasonably have been expected to die from heart disease. In addition, the rate of heart disease among Californian adults was 1.4 times higher for men than for women in 1998.7,8 Consider this alongside the fact that males accounted for 91% of the adults who purchased handguns in California in 19989 and that fewer than 1% of adult Californians purchased a handgun in 1998.8,9 Therefore, the gender distribution of adults in California who did not purchase a handgun, and who represent approximately 99% of the adult population in California, was approximately equal to the gender distribution in the state; that is, about 50% male and 50% female.8 This information provides reasonable evidence to expect that the death rate in the comparison subjects (that is, those who died by non-violent causes) was higher in handgun purchasers than in non-handgun purchasers. That is, b/TE > d/TĒ and therefore MDR′ >1. If MDR′ was actually >1 in the study by Grassel and colleagues, the OR would provide an underestimate of the true impact of handgun purchase on violent death.
However, it is especially difficult to assess the direction and magnitude of this source of bias in the study by Grassel and colleagues because many causes of death were included in the comparison group, each of which may have occurred at different, and potentially offsetting, rates among handgun purchasers and non-purchasers. Moreover, even if the comparison group had been comprised solely of heart disease decedents, the result of our short example above does not mean that this source of bias would necessarily serve to underestimate the impact of handgun purchase on the risk of violent death. Numerous factors could lead to variation in the direction and magnitude of bias stemming from an MDR′ ≠ 1. For instance, if we consider victim age, the relative rate of heart disease mortality among young (age 20–24 years) Californians in 1998 was actually lower in males than in females (relative rate = 0.8).7,8 If the true value of MDR′ was <1 in the study by Grassel and colleagues, the resulting OR would be an overestimate of the true impact of handgun purchase on violent death among this subgroup of young Californians. The magnitude of the bias would be equal to the reciprocal of MDR′.5,6 For example, if MDR′ was found to be 0.8 and a logistic regression model including only the subset of 20–24 year old subjects yielded an OR of 3.0, the effect estimate that is adjusted for the bias we are concerned with is actually MDR = 3.0 × 0.8 = 2.4. That is to say, the initial OR of 3.0 was an overestimate, being 1.25 times (1/0.8 = 1.25) larger than expected. Including age as a covariate would not specifically control for this source of bias, nor would it obviate the need to test effect modification by age.
The major challenge in all case-control studies, including those in which injury cases are the center piece, is to identify control subjects that will yield unbiased risk factor estimates.4,5 This note illustrates one mechanism of bias that injury epidemiologists must be wary of when designing and interpreting case-control studies that incorporate dead control subjects.
We gratefully acknowledge Hal Morgenstern and Colin Cryer for helpful comments, and the National Institute on Alcohol Abuse and Alcoholism and The Joyce Foundation for funding.