A key concept in case-control studies that guides control selection is the study base (Miettinen, 1985), defined simply as the person-time experience that gives rise to the cases. Conceptually, the study base is populated by the people at risk of becoming identified as cases in the study if they got the disease during the time period in which cases are identified. Note that this is more than just being at risk of developing the disease in that membership in the study base also requires that if the disease should develop, the individual would end up as part of the case group for that study. The question of "Who would have become a case in this study?" often has a complex, multifaceted answer. Beyond the biological changes involved with disease development, it may involve behavioral response to symptoms or seeking medical care from certain physicians or hospitals, if those are components of becoming recognized, enrolled cases in the study. If the constitution of the study base can be unambiguously defined in both theoretical and operational terms, then sampling controls is reduced to a probability sampling protocol. In fact, one of the major virtues of case-control studies nested within well-defined cohorts is precisely that clarity: all members of the study base are enrolled in the cohort, and sampling from that roster is straightforward in principle and in practice.
In many case-control studies, however, the very definition of the study base is complex. In some instances, the study base is defined a priori, e.g., all persons enrolled in a given health care plan for a defined period of time, or all persons who reside in a given geographic area over some time period, and the challenge is to accurately identify all cases of disease that arise from that study base (Miettinen, 1985). Given that the investigator has chosen the study base, the conceptual definition is clear, though practical aspects of sampling from that base in an unbiased manner may still pose a challenge. Random sampling from a geographically defined population is often not easy, at least in settings in which population rosters are lacking.
In other instances, a roster of cases is available, for example, from a given medical practice or hospital, and even the conceptual definition of the study base is unclear. The investigator must consider the entire set of attributes that are prerequisites to being enrolled as a case. The conceptual definition of the study base producing cases may include whether symptoms come to attention, whether people seek a diagnosis for those symptoms, whether they have access to medical care, and who they choose as their health care provider (Savitz & Pearce, 1988). Thus, the assessment of whether a particular mechanism of control selection has generated an unbiased sample from the study base (Miettinen, 1985) requires careful evaluation and informed judgment.
Obtaining perfectly coherent case and control groups from the same study base guarantees that there will be no additional selection bias introduced in the case-control sampling beyond whatever selection bias may be inherent in the underlying cohort. The failure to do so, however, does not automatically produce selection bias; it just introduces the possibility. In a cohort study, the ultimate purpose of the unexposed group is to estimate the disease risk of the exposed group absent exposure. In a case-control study, the purpose of the controls is to generate an accurate estimate of the exposure prevalence in the study base that gave rise to the cases. Given this goal, by good fortune or careful planning, a control group that is not coherent with the cases may nevertheless generate a valid estimate of exposure prevalence in the study base that gave rise to the cases. If, for example, the exposure of interest in a case-control study of melanoma among women were natural hair color (associated with skin pigmentation and response to sunlight), and we knew that hair color was not related to gender, we might well accept the exposure prevalence estimates among male controls in a geographically defined study base as a valid estimate for female cases. In no sense could we argue that the controls constitute a random sample from the study base that produced the cases, which must be exclusively female, yet the exposure prevalence of the controls would be a valid estimate of the exposure prevalence in that study base under the assumptions noted above.
A second consideration is that a control group can be well suited to address one exposure and yet be biased for assessing others. If controls are sampled in a valid manner from the proper study base, then they will generate accurate estimates of prevalence for all possible exposures in the study base, and thus case-control comparisons of exposure prevalence will generate valid measures of association. However, with deviations from the ideally constituted controls, the potential for selection bias needs to be considered on an exposure-by-exposure basis. In the above example of a case-control study of melanoma, males would not serve well as controls for female cases in efforts to address the prevalence of sunscreen use or diet, let alone reproductive history and oral contraceptive use. The question of whether the controls have generated a good estimate of exposure prevalence in the study base, and thus a valid measure of the exposure-disease association of concern, must be considered for each exposure of interest.
Among the most challenging exposures to evaluate are those that are associated with social factors or discretionary individual behaviors, e.g., diet, exercise, tobacco use. These characteristics are often susceptible to selection bias in that they may well be related to inclination to seek medical care, source of medical care, and willingness to voluntarily participate in studies. In contrast, if exposure were determined solely by genetic factors, e.g., blood type or hair color, or those not based on conscious decisions, e.g., public water source, eating at a restaurant discovered to employ a carrier of hepatitis, then selection bias is less likely. Therefore, it is much easier to choose controls for studies of some exposures, such as blood type, than others, such as psychological stress or diet.
In asking whether a particular method of control selection constitutes an unbiased method of sampling from the study base, corrections can be made for intentionally unbalanced sampling, e.g., stratified sampling by demographic attributes or cluster sampling. Consideration of confounding may justify manipulation of the sampling of controls to better approximate the distribution of the confounding factor among cases. Such manipulation of control selection is a form of intentional selection bias (Rothman, 1986), which is then removed through statistical adjustment. When it is known that stratification and adjustment for the confounding factor will be required to obtain valid results, then there may be some benefit from manipulating the distribution of the confounding factor among the controls. If that stratified sampling makes the distribution of the confounding factor among controls more similar to the distribution among cases, then the stratified analysis will be more statistically efficient and thus generate more precise results than if the distribution were markedly different among cases and controls.
For example, we may be interested in the question of whether coffee consumption is associated with the risk of developing bladder cancer. We know that tobacco use is a major determinant of bladder cancer and also that coffee consumption and smoking tend to be positively associated. Thus, we can anticipate that in our analysis of the association between coffee consumption and bladder cancer, we will need to make adjustments for a confounding effect of cigarette smoking. If we take no action at the time of control selection, we will have many more cases who are smokers than controls (given that tobacco use is a strong risk factor for bladder cancer). We lose precision by creating strata of smoking in which there is gross imbalance of cases and controls, i.e., many controls who are nonsmokers relative to the number of cases and few controls who are heavy smokers relative to the number of cases. In anticipation of this problem, we may well choose to distort our control sampling to oversample smokers, i.e., intentionally shift the balance using probability sampling among strata of smokers and nonsmokers to make the smoking distribution of controls more similar to that of the cases. We will still need to adjust for smoking, as we would have without stratified sampling, but now when we do adjust we will have a better balance of cases and controls across the smoking strata, and a more statistically precise result for the estimated measure of association.
Given the ability to account for stratified sampling from the study base, we do not need a mechanism to achieve a simple random sample that represents exposure prevalence but only a mechanism to achieve a defined probability sample from the study base. Even when the uneven sampling in relation to measured attributes is unintentional, we can correct for it in data analysis. For example, if a door-to-door sampling procedure inadvertently oversamples older women, we can readily adjust for age and gender distribution in the analysis. The key question then is whether the exposure prevalence reflects that in the study base within those strata known to be unbalanced. In the example with overrepresentation of elderly women, we need only assurance that the exposure prevalence among older women in the study base has been sampled accurately and that the exposure prevalence among young women and men of all ages in the study base has also been sampled accurately, not necessarily that the proportion of women and men in the study base has been sampled accurately (unless gender is the exposure of interest). Conversely, selecting a sample that is representative with regard to social and demographic factors does not guarantee that it reflects accurately exposure prevalence and thus would generate an unbiased estimate of the association between exposure and disease. Exposed persons may be oversampled (or undersampled) inadvertently in each of the age-sex strata even if the distribution by age and sex is perfectly representative of the study base. For example, participants in studies generally are less likely to be users of tobacco than are nonparticipants. This might well be true in all age and gender strata so that a control sample that is perfectly balanced across age and gender could well underestimate tobacco use in all those strata and yield a biased measure of association between tobacco use and disease.
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Among the evils which a vitiated appetite has fastened upon mankind, those that arise from the use of Tobacco hold a prominent place, and call loudly for reform. We pity the poor Chinese, who stupifies body and mind with opium, and the wretched Hindoo, who is under a similar slavery to his favorite plant, the Betel but we present the humiliating spectacle of an enlightened and christian nation, wasting annually more than twenty-five millions of dollars, and destroying the health and the lives of thousands, by a practice not at all less degrading than that of the Chinese or Hindoo.