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Most individual-level studies use case-control or response-based study

designs to study rare events, such as completed suicide. However, the

strengths and weaknesses of this study design are not well understood by

investigators outside the public health community, and in order to clarify

the controversy surrounding some of these studies, it may be helpful to

describe the most important features of the case-control study design. Studies

of the rates and determinants of illness or behaviors can be classified as

retrospective or prospective. Prospective studies usually select people on the

basis of exposure and determine how many persons with the exposure,

compared with persons without exposure, develop a certain outcome. In

contrast, retrospective studies usually start by choosing persons according

to whether an illness or behavior has already developed and seek to find the

phenomena that might be associated with the development of the outcome.

Intuitively, it makes sense that if one is studying a rare outcome, then a

prospective design is inefficient because it may take a very large sample or

a very long time to accumulate enough occurrences. In this case, the casecontrol

sampling design is beneficial because it oversamples the behavior or

outcome of interest.

To investigate suicide, for example, a case-control study might select as

cases those persons who have committed suicide, and then randomly select

as controls a certain predetermined number of subjects from the same

population who did not commit suicide. The study design would seek to

establish an association between the outcome (suicide) and an exposure

(such as firearms or depression) by noting the proportions of cases and

controls that have been exposed to the possible risk factor.

There are a number of important advantages to the case-control

method that explain its common use in epidemiology. Because the outcomes

have already happened, case-control studies require no costly follow-

up waiting for the outcome to develop. Because case-control studies

oversample the outcome of interest, they also require smaller samples

sizes than prospective studies of comparable power; for this reason, the

case-control sampling scheme is often the only feasible way to collect the

information of interest. For example, although suicide is the most common

cause of firearm-related deaths in the United States, the overall suicide

rate is approximately 11 suicides per 100,000 persons per year. Very

few prospectively collected data sets would be large enough to draw precise

inferences about completed suicide.

Feasible and efficient as the case-control design may seem, it also suffers

from important limitations arising from the nonrandom selection of

cases or controls and from misclassification of the outcome or exposure.

For example, case-control studies are particularly susceptible to recall bias—

a bias resulting from differential recall among case respondents compared

with control respondents. The likelihood of recall bias may be directly

influenced by the respondent’s motivation to explain the illness (or outcome)

itself. In a study of suicide, the victim’s past history of depression

might be more salient to the relatives of a person who has committed

suicide compared with the relatives of a control subject, so that case-control

studies of completed suicide might overstate the risk of psychopathology or

of gun ownership among persons who have committed suicide, compared

with controls.

Furthermore, relatives may follow a “stopping rule”: once the family

has found a “sufficient” explanation for the occurrence of the suicide—

whether it is a gun in the home or psychopathology—they may be less likely

to admit the presence of other, less socially acceptable risk factors; such

ascertainment bias can lead to the underreporting of co-morbidity among

risk factors and could explain reports of a greater frequency of gun ownership

among suicides with no reported history of psychopathology. In the

case of gun suicides, ascertainment bias may also arise because the outcome

itself provides evidence of access to a gun. For example, family members are

not always aware that firearms are kept in the home. If a subject has killed

himself with a gun, family members would not be able to deny the gun’s

existence, even if they have first learned of its existence because the suicide

has occurred. In contrast, the relatives of a living control subject may not

know with certainty whether a gun is present in the household (Ludwig et

al., 1998). Family awareness of suicidal risks could lead them to take steps

to prevent the suicide of family members known to be at risk. In this case,

the absence of firearms would be a sign of appropriate family responsiveness,

and a nonexperimental study design would be unable to distinguish

the protective effects of gun removal from the protective effects of other

steps that the family may have undertaken at the same time.

Other limitations of case-control studies include nonrandom selection

of cases or controls; it is often difficult to design a sample selection

procedure that ensures that controls are, in fact, representative of the

same population from which the cases were drawn. Even if the data are

accurate and the sampling scheme is well defined, case-control studies,

like other nonexperimental study designs, have a limited ability to distinguish

causal from noncausal connections. In the case of firearms, individuals

who own guns might have unobserved attributes that are associated

with increased suicide risk, or, just as important, some individuals

may seek to purchase guns because of a specific plan to commit suicide.

These possibilities have very different implications from the point of view

of preventive intervention.

Finally, the parameter reported in many case-control studies, termed

the odds ratio, is often not the parameter of interest for policy. Presumably,

policy makers are interested in the expected number of lives saved or lost

because of firearms or other factors. The odds ratio, which is roughly the

suicide probability with firearms divided by the suicide probability without

firearms, can translate into many or few lives, depending on the suicide

probabilities that are involved. Thus, a large odds ratio does not necessarily

translate into a large number of lives, and a small odds ratio does not

necessarily translate into a small number of lives. To see the problem,

consider two populations, one in which the suicide probability conditional

on owning a firearm is 0.02 per person per year and the suicide probability

conditional on not owning a firearm is 0.01 per person per year, and

another in which these two probabilities are 0.0002 and 0.0001, respectively.

The odds ratio and the relative risk are the same in both scenarios,

but if guns are causal, then removal of guns from the population might

avert 0.01 deaths per person per year in the first scenario, but only 0.0001

deaths per person per year in the second. Policy makers would usually like

to know the attributable risk, which can be defined as the difference between

the incidence of the outcome among the exposed and the incidence of

the outcome among the unexposed. For the odds ratio or relative risk to

inform policy, it must therefore be considered in light of additional information.

The appendix to this chapter provides a detailed discussion of the

measures of association in case-control designs, illustrating the strengths

and weaknesses of the odds ratio as a measure of association and explaining

the information needed to estimate attributable risk.