6.5 Case–control studies
Oxford Textbook of Public Health
Noel S. Weiss
Retrospective ascertainment of exposure status in cases and controls
Physical and laboratory measurements
Minimizing selection bias
Minimizing information bias
Estimating the attributable risk from results of case–control studies
The role of case–control studies in understanding disease aetiology
In 1971, Herbst et al. (1971) reported that the mothers of seven of eight teenage girls diagnosed with clear cell adenocarcinoma of the vagina in Boston during 1966 to 1969 claimed to have taken a synthetic hormone, diethylstilboestrol, while that child was in utero. None of the mothers of 32 girls without vaginal adenocarcinoma, matched to the mothers of cases with regard to hospital and date of birth, had taken diethylstilboesterol during the corresponding pregnancy. Within a year, a New York study of five cases and eight girls without vaginal cancer obtained similar results (Greenwald et al. 1971). The introduction of prenatal diethylstilboesterol use into obstetric practice in the United States during the 1940s and 1950s, followed by the appearance of this hitherto unseen form of cancer some 20 years later, supported a causal connection between in utero exposure to diethylstilboesterol and vaginal adenocarcinoma. The means by which in utero diethylstilboesterol exposure might predispose to the occurrence of clear cell vaginal adenocarcinoma was unknown in 1971 (it is now believed that diethylstilboesterol acts by interfering with normal development of the female genital tract, resulting in the persistence into puberty of vaginal adenosis in which adenocarcinoma can arise (Ulfelder and Robboy 1976)). Nonetheless, a causal inference was made at that time by the Food and Drug Administration, which specified pregnancy as a contraindication for diethylstilboesterol use.
The investigation by Herbst et al. was a case–control study: a comparison of prior exposures or characteristics of ill people (cases) with those of people at risk for the illness in the population from which the cases arose. Generally, the prior experience of people at risk is estimated from observations on a sample of that population (controls). A difference in the frequency or levels of exposure between cases and controls—that is, an association—may be a reflection of a causal link.
At first glance, the case–control approach appears to proceed backwards, from consequence to potential cause. Nonetheless, if a case–control study enrols cases and controls from the same underlying population at risk of the outcome, and can measure exposure status validly in them, the results obtained will be identical with those from a properly done cohort study. A case–control, cohort, or any other form of non-randomized study does have the potential to identify associations that are not causal, either because of chance or because of the influence of some other factor associated with both exposure and outcome. Even so, the evidence that is provided by well-performed case–control studies can carry great weight when evaluating the validity of a causal hypothesis. Indeed, a number of causal inferences have been based largely on the results of case–control studies. These include, in addition to the diethylstilboesterol–vaginal adenocarcinoma relationship, the connection between aspirin use in children and the development of Reye’s syndrome, and the use of absorbent tampons and the incidence of toxic shock syndrome.
One of the criteria used to assess the validity of a causal hypothesis is the strength of the association between exposure and disease, usually as measured by the ratio of the incidence rate in exposed and non-exposed people. In most case–control studies, it is not possible to measure incidence rates in either of these groups. Nonetheless, from the frequency of exposure observed in cases and controls, it is usually possible to estimate closely the ratio of the incidence rates.
To understand how this can be done, consider a cohort study in which exposed and non-exposed people are followed for a certain period of time. The table below summarizes their experience with regard to a particular disease:
a + b
c + d
The cumulative incidence of the disease in exposed and non-exposed people over a given period of follow-up is a/(a + b) and c/(c + d) respectively. The relative risk (RR) is the ratio of these:
If the incidence of the disease is relatively low during the follow-up period in both exposed and non-exposed people, then a will be small relative to b and c will be small relative to d. Therefore
In this expression the numerator (a/c) is the odds of exposure in people who develop the disease, the denominator (b/d) is the odds of exposure in people who remain well, and
is the odds ratio (OR). The numerator can be estimated from a sample of cases, while the denominator can be estimated from a sample of non-cases. Neither estimate is influenced by the proportion of cases among the subjects actually chosen for study.
In the following hypothetical example, assume that 100 of 10 000 people exposed to a particular substance or organism developed a disease, in contrast with 300 of 90 000 non-exposed people:
If a case–control study had been done in this population, in which 50 per cent of cases were included but only 1 per cent of non-cases, the following results would have been obtained:
100 × 0.5 = 50
9900 × 0.01 = 99
300 × 0.5 = 150
89 700 × 0.01 = 897
In many studies, controls are chosen as they were in the previous example, that is from people who had not developed the disease by the end of the same time period during which other people (the cases) had become ill. In such studies, the less common the disease in both exposed and non-exposed people during the period, the better the odds ratio will estimate the ratio of cumulative incidence. In the example, only 1 per cent and 0.33 per cent of exposed and non-exposed people, respectively, developed the illness, and so the relative cumulative incidence and odds ratio were in close correspondence (3.00 versus 3.02). However, it is also possible to choose controls from people free of disease only until the corresponding cases have been diagnosed; a person can appear in the study first as a control and later as a case. If this approach is used, the odds ratio will be a valid estimate of the ratio of incidence rates (that is, cases divided by person-time at risk) irrespective of the disease frequency (Greenland and Thomas 1982; Pearce 1993).
Retrospective ascertainment of exposure status in cases and controls
Epidemiological studies seek to obtain information on exposures present during an aetiologically relevant period of time. That period varies across aetiological relationships. For example, while excess consumption of alcohol predisposes both to motor vehicle injuries and to cirrhosis of the liver, it does so during considerably different time intervals prior to the occurrence of the injury or the onset of the illness, respectively.
Some case–control studies are nested within cohort studies in which specimens (for example blood or urine) have been obtained prior to diagnosis on all cohort members, but have not yet been analysed for the exposure(s) in question. When these analyses are done on cohort members who developed a particular illness and on controls selected from the cohort, the results obtained cannot have been influenced by events occurring following the diagnosis of the illness. (In order to avoid the possibility of occult illness in cases influencing levels of a suspected aetiological factor, many studies of this type exclude from the analyses specimens obtained within the period prior to diagnosis that might correspond to the duration of the preclinical stage of disease.) Also, among the large majority of case–control studies in which exposure status is not measured until the illness or injury has been diagnosed, some are concerned only with an exposure or characteristic that would have been the same at all times in a person’s life. This is true for a genetically determined characteristic such as ABO blood type, or the absence of glutathione transferase M1 activity (an enzyme that metabolizes several potentially carcinogenic constituents of cigarette smoke). Clearly, these studies are no less valid for having had to measure exposure in retrospect.
However, most case–control studies are required to consider explicitly how best to assess in retrospect subjects’ exposure status during one or more possible aetiologically relevant time periods. Possible sources of exposure data include interviews or questionnaires, available records, or physical or laboratory measurements.
For many exposures, a subject’s memory is an excellent window to the past. A number of important aetiological relationships have been identified through interview-based case–control studies. Generally, study participants will report longer-term and more recent experiences with greater accuracy than shorter-term and more distant ones. Attention to the ways in which questions are asked (Armstrong et al. 1992), along with the use of visual aids when appropriate (for example, pictures of medicines, or of containers of household products, and calendars for important life events to enhance recall of the timing of other exposures) will maximize the accuracy of the information received. These efforts, along with the use of the same questions for cases and controls asked in the same way, will also minimize the potential for bias that could result from the subject’s or interviewer’s awareness of case or control status.
One virtue of exposure ascertainment via interview or questionnaire is that information can be sought for multiple points in the past. It is possible that a given exposure plays an aetiological role only if present at a certain age, for a certain duration, or at a certain time in the past. Because there is often little guidance before a study starts to suggest the most relevant age, length, or recency, key exposures are often elicited throughout much of the subject’s lifetime. However, care must be taken not to include exposures that took place after the illness began. An instructive example was provided by Victora et al. (1989) in a case–control study of infant death from diarrhoea in relation to type of feeding. These investigators asked mothers whether their child was or was not being breast fed immediately prior to the onset of the fatal illness (mothers of controls were queried about type of feeding prior to a comparable point in time). Mothers were also asked if subsequent to the onset of the illness there had been any changes in type of feeding; following the development of diarrhoea, many children are switched to formula and cow’s milk. Relative to infants who were solely breast fed, those who were supplemented with powdered or cow’s milk prior to their illness had about four times the risk of diarrhoeal death. However, the authors showed that if one inappropriately considered the feeding method that was present during the illness, about a 13-fold increase in risk associated with supplementation would have been estimated.
Case–control studies have exploited the presence of vital, registry, employment, medical, and pharmacy records, to name a few, as a means of obtaining information on exposures. However, because the information contained in the records will usually have been assembled for purposes other than epidemiological research, it may not provide precisely that information desired by the epidemiologist. For example, a death certificate or an occupational record may state an individual’s job, but often not his or her actual exposure to the substance(s) of interest to the study. Or, a pharmacy record will indicate a prescription having been filled, but not necessarily whether the patient took the medication on a given day, or took it at all. This sort of imprecision will impair a study’s ability to discern a true association between an exposure and a disease—the greater the imprecision, the greater the impairment. Nonetheless, some very strong associations have been identified through record-based case–control studies. For example, Daling et al. (1982) conducted a tumour-registry-based case–control study to test the hypothesis that homosexual men have a relatively high incidence of anal cancer. While registry data do not specify a man’s sexual preference, they do contain information regarding his marital status. The investigators found that three times more men with anal cancer than controls (men with a colon or rectal cancer) had never been married. Being single is far from a perfect predictor of homosexuality, of course. Nonetheless, the presence of such a large case–control difference, given the very poor means of gauging the relevant exposure, was a stimulus to conduct interview-based studies that could elicit information regarding sexual history with greater precision. The latter studies showed an exceedingly strong association (odds ratio of 50) (Daling et al. 1987).
In case–control studies in which medical records are used to characterize exposure status, care must be taken to restrict the information obtained to that which preceded the case’s diagnosis (and the presence of symptoms, if any, that led to the diagnosis). The records of controls must be truncated at similar points in time. Without this safeguard, it is possible that bias will arise because there are systematically more records available to review on cases than controls; the case’s illness may have stimulated an enquiry by medical personnel into his or her past, whereas no corresponding enquiry would necessarily have occurred for control subjects.
Physical and laboratory measurements
The recognized limitations of interviews and records in characterizing a variety of potentially relevant exposures have stimulated the conduct of epidemiological studies that use laboratory and other methods of measurement. A woman cannot tell an investigator the level of her reproductive hormones, the concentration of various micronutrients in her blood, or whether her cervix is infected with human papillomavirus, but laboratory tests can. Unfortunately, such tests tell us what these things are only at the time that the specimens have been obtained. For some exposures, there will be a high correlation between the measured level following case and control identification and that present during the aetiologically relevant time period. For example, lead enters and does not leave the dentine of teeth. Therefore, in young school-age children, lead dentine levels are an indicator of cumulative lead exposure, a good portion of which could be relevant to the development of intellectual impairment and other adverse neurological outcomes. In contrast, one would not rely on serum levels of reproductive hormones of postmenopausal cases of breast cancer and controls to indicate what their premenopausal levels were, much less their hormonal status during their very early reproductive years (at which time it is plausible that hormones are exerting their greatest impact on future risk of breast cancer).
Ideally, the cases in a case–control study would comprise all (or a representative sample of) members of a defined population who develop a given health outcome during a given period of time. For studies of disease aetiology, that outcome is disease incidence. For studies that seek to determine the efficacy of early disease detection or treatment, the outcome generally is the occurrence of complications of the disease or mortality; such studies have been described in detail elsewhere (Selby 1994; Weiss 1994), and will not be covered any further here.
The population from which cases are to be drawn may be defined geographically, or it may be defined on the basis of other characteristics, such as membership in a prepaid health-care plan or an occupational group. The identification of all newly ill people in a defined population can be facilitated by the presence of a reporting system such as a cancer or malformation registry that seeks to accomplish this identification for other purposes. Occasionally, care for the condition being studied may be centralized, so that it will be necessary to review the records of only one or a few institutions to identify all cases in the population in which those institutions are located. However, in many instances it is not feasible to identify all cases that occur in a given population, and so often case–control studies are based on cases identified from hospital records, or from the records of selected providers from whom patients had sought health care. The study by Herbst et al. (1971) of vaginal adenocarcinoma was of this type. Whether or not the cases are derived from a defined population, it is necessary that they be drawn in an unselected manner with regard to exposure status, for example by including in the study all otherwise eligible cases diagnosed or receiving care during a defined time period.
While the goal of a case–control study of aetiology is to enrol incident cases, under some circumstances it may be necessary to enrol prevalent cases at a particular point in time, irrespective of when each one’s illness had begun. For some conditions, the date of occurrence may simply not be known. For example, in the absence of very close sero-monitoring, one generally cannot determine when a person acquired an HIV infection. Furthermore, for uncommon diseases of long duration, an incidence series may yield too few cases for meaningful analysis. The disadvantages of using prevalent cases in a case–control study relate in part to the added problems of accurate exposure ascertainment. For prevalent conditions whose date of diagnosis is known, pre-illness exposure information on study subjects must be obtained for more distant points in the past, on average, than would be necessary for an incident series. For prevalent conditions whose date of occurrence is unknown (for example, HIV infection), there will be uncertainty as to the best point in time before which one should elicit exposure information. Also, by studying people remaining alive with a given condition, one is studying at the same time not only aetiological factors, but also those that influence survival from the condition.
Ideally, the criteria used to identify and select individual cases for study should be objective ones of high sensitivity and specificity for the disease. Specificity is of particular concern, since the inadvertent inclusion of people without disease into the case group will generally obscure any true association with exposure. With this in mind, in the case–control study of Reye’s syndrome in relation to antecedent analgesic use conducted by the Centers for Disease Control (Hurwitz et al. 1985), only cases with a substantial degree of neurological impairment (stage 2 or higher) were included. The use of this criterion minimized the chances that children with diseases other than Reye’s syndrome, which generally would have a lesser degree of severity, would be included in the case group. It also was intended to serve as protection against selective misclassification of Reye’s syndrome based on knowledge of exposure status, since the hypothesis that aspirin was associated with Reye’s syndrome was well known by the time that the study took place. Conceivably, the knowledge that the child had consumed aspirin could have led some doctors to diagnose Reye’s syndrome in cases with an atypical illness.
Occasionally, the proportion of ill people who have had a specific exposure is so high, unequivocally more than would be expected in the population from which they were derived, that the presence of an association (though not its magnitude) can be surmised from a case series alone (Cummings and Weiss 1998). For example, when it was learned that all cases of a form of pneumonia that was epidemic in Spain in 1981 had ingested adulterated rapeseed oil, a causal inference was drawn, leading to efforts to eliminate further use of that oil. This action was taken before any formal comparison of cases with controls was made (Tabuenca 1981).
However, in the vast majority of instances, an explicit control group is needed to estimate the frequency and degree of exposure that would have taken place among cases in the absence of an exposure–disease association. An ideal control group would be one that consists of individuals:
selected from a population whose distribution of exposure is that of the population from which the cases arose;
who are identical to the cases with respect to their distribution of all characteristics
that influence the likelihood and/or degree of exposure, and
that, independent of their relation to exposure, are also related to the occurrence of the illness under study or to its recognition;
in whom the presence of the exposure can be measured accurately and in a manner that is identical to that used for cases.
If the criteria above are not met in a particular study, then selection bias, confounding, or information bias, respectively, will be present.
Minimizing selection bias
If the cases identified in the study are all or a sample of those that occurred in a defined population, one can seek to achieve comparability by choosing as controls people sampled from that same population. For geographically defined populations, a number of different methods of sampling have been used, including random digit dialling of telephone numbers, area sampling, neighbourhood sampling, voters’ lists, population registers, motor vehicle licenses, and birth certificates, among others. When cases are members of a prepaid health-care plan who develop an illness or injury, a sample of people who were members of the health plan when the illness or injury occurred can serve as controls. When cases are ill or injured members of an employed population, controls can be selected from that same group of employees.
If cases have not been selected from a definable population at risk for the disease, but rather from people treated for a particular illness at one or a few hospitals or clinics, then selection bias may be introduced if controls are not chosen from people who, had they developed the illness under study, would have received care at these hospitals or clinics, and people who do and do not receive care from these sources differ with regard to their frequency or level of exposure.
Therefore, when cases are chosen from a narrow range of providers of health care, controls are often chosen from other ill people treated by these providers. Such ill controls may also be used if, irrespective of the source of cases, there is no feasible way to sample from the population at large, or if sampling from the population at large would be likely to result in a substantial level of non-response or information bias (see below). For these reasons, in some studies of fatal illness, exposures in people with a given cause of death are compared with exposures in a sample of people who died for other reasons.
However, the choice of ill or deceased controls can itself give rise to selection bias if the illnesses (or causes of death) represented in the control group are in some way associated with the exposure of interest. For example, ill or recently deceased people tend to have been smokers of cigarettes more often than other people (McLaughlin et al. 1985), since smoking is associated with a variety of causes of illness and death. Because smoking histories of ill people overstate the cigarette consumption of the population from which the cases arose (even if that population cannot be defined), the odds ratio associated with smoking based on the use of ill people as controls will be spuriously low.
To minimize selection bias related to having chosen ill or deceased controls, an attempt can be made to omit potential controls with conditions known to be related (positively or negatively) to the exposure. For example, in the analysis of a hospital-based case–control study of bladder cancer in relation to prior use of artificial sweeteners, the investigators excluded from their control group people who were admitted to hospital for obesity-related diseases (Silverman et al. 1983). They showed that without this restriction, the control group would have a spuriously high proportion of users of artificial sweeteners relative to the population from which their cases actually had come. This approach will succeed to the extent that one judges correctly which conditions truly are exposure-related, and how accurately the presence of those conditions can be determined. For many exposures, this may pose little problem, and judicious exclusion will yield a control group capable of providing an unbiased result. For others, such as cigarette smoking or alcohol drinking, it has been shown that admitting diagnoses or statements of cause of death are incapable of identifying all people with illnesses related to these exposures (McLaughlin et al. 1985).
Occasionally, controls are chosen from individuals who are tested for the presence of the disease under study and are found not to have it. For example, people demonstrated to have coronary artery occlusion on coronary angiography have been compared with angiography patients without occlusion with regard to potential risk factors (Thom et al. 1992). As another example, the prior use of oral contraceptives was compared between women diagnosed with venous thromboembolism and women seen at the same institution for suspected venous thromboembolism who turned out not to have this condition (Bloemenkamp et al. 1999). It may be relatively inexpensive to select controls from people who receive the same diagnostic evaluation as do cases, and it is also possible to achieve case–control comparability with regard to the choice of a health-care provider (and the correlates of that choice). This approach can have an impact on the study’s validity if the frequency or degree of exposure differs between otherwise comparable members of a population who do and do not receive the test. It will increase the validity if the disease being investigated is generally asymptomatic, and so would not be detected in the absence of testing. Thus, the relation of the use of oral contraceptives to the incidence of in situ cancer of the cervix is best studied in women who have received cervical screening, by comparing oral contraceptive use between cases of in situ cancer and women with a negative screen. This is because:
in most societies, screening is more commonly administered to women who use oral contraceptives than women who do not
in situ cancers are asymptomatic and will not be identified in the absence of cervical screening.
Therefore, if controls are chosen from women in general, who may or may not have received cervical screening, an apparent excess of oral contraceptive users would be present among cases of in situ cancer even if no true association were present.
However, the choice of test-negative controls will detract from a study’s validity if the large majority of people who develop the disease would soon be diagnosed whether or not the test was administered. There was a controversy in the late 1970s regarding the suitability, in case–control studies of postmenopausal oestrogen use and endometrial cancer, of a control group restricted to women with no evidence of cancer on endometrial biopsy. Among women without endometrial cancer, oestrogen use differs greatly between those who have and have not undergone biopsy, since oestrogen use predisposes to uterine bleeding of non-malignant causes that often leads to endometrial biopsy. Those investigators who believed that there was a great prevalence of occult endometrial cancer in the population suggested that the optimal control group ought to be women undergoing endometrial biopsy and found not to have cancer (Horwitz and Feinstein 1978). However, the majority of investigators believed that no such large pool of prevalent, occult disease existed, and that choosing biopsy-negative controls would lead to a spuriously high estimate of oestrogen use in the population at risk, and thus a spuriously low odds ratio (Shapiro et al. 1985).
No matter how controls are defined in a case–control study, selection bias may be introduced to the extent that exposure information is not obtained on all who have been selected to take part. The magnitude of the bias will increase in relation to the frequency of missing data and the degree to which exposure frequencies or levels differ between study subjects on whom exposure status is and is not known. The problem of incomplete ascertainment of exposure on study subjects is particularly common in interview- or questionnaire-based case–control studies. Strategies for minimizing the degree of non-response in case–control studies are discussed in detail elsewhere (Armstrong et al. 1992).
Characteristics of confounding variables in case–control studies
Confounding is present when the estimate of the relation between an exposure and disease is distorted by the influence of another factor. In any study design, confounding will occur to the extent that the other factor is both associated with exposure (though not as a result of the exposure) and with the occurrence of the disease or its recognition. In case–control studies alone, a factor may confound even if it is not associated with an altered risk of disease, if the proportions of cases and controls vary across levels or categories of the factor. For example, in a collaborative study of ovarian cancer in relation to use of oral contraceptives (Weiss et al. 1981), an attempt was made to identify and interview all incident cases during a several-year period in two American populations. In one of the populations (western Washington State), several controls per case were interviewed, whereas the control-to-case ratio in the other (Utah) was 1.0. Since oral contraceptive use was more common in Washington women than in Utah women, failure to take into account the state of residence in the analysis (for example, by adjustment) would have led to a spuriously high estimate of the frequency of oral contraceptive use in controls relative to that in cases.
Means of controlling for confounding
One straightforward way of preventing confounding is to restrict cases and controls to a single category or level of the potentially confounding variable. For example, in their study of physical activity in relation to primary cardiac arrest, Siscovick et al. (1982) excluded people with conditions, such as clinically recognized heart disease, that could both predispose to cardiac arrest and might be expected to alter level of activity. A second way is to obtain information on exposures or characteristics that may differ between cases and controls, and then make statistical adjustments for those that also are found to be related to the exposure/characteristic under investigation (Rothman and Greenland 1998).
Finally, it is possible to match one or more controls to each case’s category or level of a potentially confounding factor.
It is appropriate to match if the variable is expected to be strongly related to both exposure and to disease. Thus, in a case–control study of breast cancer in relation to use of hair dye, it would make sense to match on gender (if the study had not already been restricted to women) since, in most cultures use of hair dye is more common in women than in men and in the absence of matching the case-to-control ratio would be very uneven between women and men. While confounding by gender could be prevented even without matching by adjustment in the analysis, the statistical precision of the unmatched study would be substantially reduced relative to that of a case–control study having a more similar proportion of female cases and controls.
It is appropriate to match if information on possible matching variables can be obtained inexpensively. There are some means of control selection in which information regarding some confounders can be obtained at no cost. For example, from voters’ lists or prepaid health plan membership records, it would generally be possible to choose directly one or more controls who were identical to a given case’s age. Conversely, if a population sampling scheme such as random digit dialling were being employed, the age of the respondent would not be known in advance of approaching him or her. Rather than omitting already contacted controls who did not match a particular case’s age, the matching can be done much more broadly. Additional control for finer categories of age can be accomplished in the data analysis.
It is appropriate to match if information on exposure status cannot be obtained inexpensively. The higher the cost of exposure ascertainment, the greater the incentive to limit the number of control subjects to the number of cases. Case–control differences regarding confounding factors particularly will reduce the statistical power of a study that does not have a surplus of controls. Enriching the group of controls selected with people more similar to the cases with regard to confounding factors (that is, matching) can prevent this loss of statistical power.
In case–control studies of genetic characteristics as possible aetiological factors, some investigators have used a matched design in which a specified type of relative (for example parent, sibling, cousin) is chosen as a control for each case (Yang and Khoury 1997; Witte et al. 1999). This approach has the advantage of minimizing potential confounding by other genetic characteristics with which the one of interest is associated. However, it has the disadvantage of excluding a possibly large fraction of cases for whom there is no relative available of the type needed to provide a sample for genetic analysis.
It should be kept in mind that matching alone is not sufficient to eliminate a variable’s confounding influence: failure to consider a matching variable in the analysis of the study can lead to a biased result (Rothman and Greenland 1998). Analyses of studies that have matched controls to cases on a given characteristic can adjust for that characteristic as if no matching had taken place. Alternatively, these analyses can explicitly consider cases and controls as matched sets. In the instance of matched case–control pairs and a dichotomous exposure variable, the following table could be constructed.
Only the b pairs in which the case was exposed but not the matched control, and the c pairs in which the reverse was true, would enter the analysis. The odds ratio would be calculated as b/c. When there is more than one control per case, the matched odds ratio can be calculated as well (Breslow and Day 1980).
Minimizing information bias
In case–control studies in which information on exposure status is sought via an interview or questionnaire, the chief safeguards against information bias entail asking questions about events that are salient to the respondent, that are framed in an unambiguous way, and that are presented identically to both cases and controls. Employment of these safeguards, however, will not prevent differential accuracy of reporting between cases and controls in all circumstances. Some past exposures/events will simply be more salient to people with an illness, who might have dwelled on possible reasons for its occurrence, than to people without that illness. Other exposures may be viewed as socially undesirable, and there may be a difference between cases and healthy controls in their willingness to admit to them. If the anticipated difference in the quality of information between cases and otherwise appropriate controls is too great, a control group that is less than ideal in other respects may be selected instead so as to minimize the potential for information bias. For example, some studies of prenatal risk factors for a particular congenital malformation that utilize maternal interviews as the source of exposure data have selected as controls infants with other malformations (Rosenberg et al. 1983). This control group will provide a more valid result than a control group that consists of infants in general if mothers of malformed and mothers of normal infants report prenatal exposures to a different degree even in the absence of an association, and the exposure in question is not associated with the occurrence of the malformations present in control infants.
Similar reasoning led Daling et al. (1987), when conducting their case–control study of anal cancer in relation to a history of anal intercourse, to eschew the geographic population from which their case had arisen as a sampling frame for controls. They feared that interviews that sought information about prior anal intercourse might be more complete among men with cancer than men in the population at large. Thus, they chose as controls men with a cancer of a different site (colon), which they believed was unlikely to have been aetiologically related to prior anal intercourse.
When the exposure under consideration is sufficiently imprecise or is open to subjective interpretation, there may not be any control group that will provide information comparable to that provided by cases. An instructive example comes from a case–control study of Down’s syndrome (Stott 1958) conducted shortly before the chromosomal basis for the aetiology of this condition had been learned. The study sought to determine whether emotional ‘shocks’ during pregnancy might be a risk factor. The author interviewed mothers of children with Down’s syndrome with regard to the occurrence of a ‘situation or event [that would be] stress- or shock-producing if this would have been its expected effect on an emotionally stable woman’. Identical interviews were administered to mothers of normal children, and also to mothers of retarded children who did not have Down’s syndrome. Even though it is not possible that an emotional shock in pregnancy could play any aetiological role in a condition already determined at conception, a far higher proportion of mothers of cases of Down’s syndrome reported an emotional shock than did mothers of normal controls (relative risk estimated from the data, 17.0). The use of other retarded children as controls only partially reduced the spuriously high relative risk to a value of 4.3.
When conducting an interview-based study of a rapidly fatal disease, or a disease that impairs a person’s ability to provide valid interview data, it is necessary to obtain information from at least some surrogate respondents. Typically, these respondents are close relatives of the cases. In general, for purposes of comparability, similar information ought to be obtained from surrogates of controls, even though the control would be expected to provide more accurate data. Results of case–control studies based on exposure information provided by surrogate respondents need to be interpreted with particular caution. Though by no means present in every instance (Nelson et al. 1990), there can be a large difference in the validity of the responses given by case and control surrogates. For example, Greenberg et al. (1985) investigated the basis for an apparent strong association between cancer mortality and ‘nuclear’ work among employees of a naval shipyard which had been found in a comparison of work histories provided by surrogates of men who died from cancer and of those who died of other conditions. They observed that, regarding work in the nuclear part of the industry, surrogates of the cases generally provided information similar to that contained in employment records of the shipyard. In contrast, the surrogates of controls substantially misclassified the nature of their relatives’ jobs as not involving radiation. Using the data provided by employment records, which included individual radiation dosimetry (Rinsky et al. 1981), little or no association was found between cancer mortality and radiation exposure received at the shipyard.
What was undoubtedly a spuriously negative association was found in a case–control study of lung cancer and passive cigarette smoking that used, for one analysis, information obtained from surrogate respondents (Janerich et al. 1990). In this analysis, the relative risk of lung cancer among non-smokers associated with a spouse’s having smoked—0.33 (that is, a 67 per cent reduction in risk)—would seem almost certainly due to a spurious minimization or denial of smoking by spouses of cases, who may have feared their habit caused their spouse to develop lung cancer.
Incomparable assessment of exposure status between cases and controls is not confined to interview- or questionnaire-based studies. Most laboratory-based studies seek to prevent this by testing samples blind to case/control status. If feasible, it is desirable to do this blinding as well in studies in which exposure is to be determined from medical or other records. However, there are instances in which the nature of the information available in records has already been influenced by whether the subject is a case or a control. For example, it was found that among 100 infertile women who underwent laparoscopy (Strathy et al. 1982), 21 had endometriosis. Only 2 per cent of 200 women undergoing laparoscopy for another indication, tubal ligation, were noted in the records of their procedure to have endometriosis. However, the interpretation of this association is unclear, since the identification and/or recording of endometriosis in cases and controls (women undergoing tubal ligation) may well have been incomparable—only in the infertile women was the laparoscopy expressly done as a diagnostic tool to investigate the possible presence of conditions such as endometriosis.
Estimating the attributable risk from results of case–control studies
Occasionally, a case–control study identifies a large odds ratio relating an exposure and a disease, and for this and other reasons a causal influence of the exposure may be suspected. The decision to seek to limit or eliminate that exposure requires weighing its negative and positive consequences. This weighing must be done in absolute, rather than in relative terms, since the same relative increase (or decrease) in risk is of far greater consequence for common than for rare outcomes. The absolute increase in the risk of disease believed to be due to a dichotomous exposure, sometimes referred to as the ‘attributable risk’ (AR), can be estimated directly from data gathered in cohort studies or randomized trials as the difference between the incidence among exposed (Ie) and non-exposed people (In). The term Ie – In can be rewritten as RR(In) – In, or as In(RR – 1). Since the relative risk can be estimated from the results of a case–control study by means of the odds ratio, the only additional piece of information needed to estimate the attributable risk is an estimate of In. For the population in which the study has been conducted, In can be estimated if:
the overall incidence (I) of the disease in that population is known or can be approximated;
the frequency of exposure (pe) in the controls selected for study reasonably reflects that of the population that gave rise to the cases.
Given (l) and (2) above,
For example, consider a disease with an incidence rate of 10 per 100 000 per year in a population in which 5 per cent of people have been exposed during a relevant period of time. The following table summarizes data from a case–control study conducted in that population:
The attributable risk that corresponds to the estimated 3.35-fold increase in risk is
From the results of case–control studies that suggest a causal relation, it is also possible to estimate the percentage of exposed people with the disease who developed it because of their exposure, rather than through one or more causal pathways not involving the exposure. This measure, often termed the ‘attributable risk per cent’ (AR%) among exposed people, is defined as
It can be described in terms of the relative risk alone:
Therefore, the results of a case–control study that provide a valid estimate of the relative risk (via the odds ratio) can provide the attributable risk per cent as well, with no additional assumptions or sources of data. It is also possible to estimate the percentage of a disease’s occurrence in the population as a whole that resulted from the actions of given exposure. This measure, the ‘population attributable risk per cent’ (PAR%) or ‘aetiological fraction’, is simply the attributable risk per cent multiplied by the proportion of cases in that population who were exposed (pc):
PAR% = AR% (pc) × 100%.
In the present example,
PAR% = 70.1% (0.15) = 10.5%.
The role of case–control studies in understanding disease aetiology
Randomized trials will not be able to answer all questions regarding the reasons diseases occur. Many potential disease-causing or disease-preventing exposures cannot be manipulated, either at all—for example, most genetic characteristics—or in any practical way for purposes of a study. For many exposure–disease relationships, either the disease is too uncommon or the induction period is too long to conduct a randomized trial that is not infeasibly large in size or long in duration. Finally, it generally will not be possible to conduct separate randomized trials to measure the impact of all potential types, amounts, and durations of a class of exposure.
Also, it is not possible to rely solely on cohort studies for answers. Just as with randomized trials, the disease outcome being studied may be too rare to allow a cohort approach to be useful. This explains why the aetiologies of vaginal adenocarcinoma and Reye’s syndrome, for example, have been evaluated exclusively by case–control studies—these diseases are simply too uncommon for most cohort studies to generate any cases, even in ‘exposed’ individuals. Prospective cohort studies are also of limited use when the induction period for the exposure–disease relationship is either very short or very long. If the induction period is very short and the exposure status of an individual varies over time, a cohort study would need to assess exposure status repeatedly among cohort members. For this reason, studies of alcohol consumption in relation to the occurrence of injuries typically are case–control in nature (Holcomb 1938). Similarly, unless information on exposure status can be ascertained retrospectively at the time that the cohort is formed, it would not be feasible to initiate a cohort study of a suspected aetiological relation that requires a very long time (perhaps several decades) to manifest itself.
While case–control studies may be of particular value in the evaluation of the aetiology of uncommon diseases, they may have difficulty in obtaining statistically precise results if the frequency of the exposure in the population under study is either extremely common or extremely uncommon (Crombie 1981). Thus, only an association as strong as the one between cigarette smoking and lung cancer could have emerged reliably from case–control studies of several hundred British men conducted in the late 1940s (Doll and Hill 1950), given that well over 90 per cent of that population were cigarette smokers. For very uncommon exposures—for example, occupational exposure to a specific substance suspected of posing a risk to health, or an infrequently prescribed drug—barring a strong observed association based on a large number of subjects, even the best-designed case–control study will usually offer no more than a suggestion of the presence or absence of a relation with regard to the occurrence of a given illness.
Armstrong, B.K., White, E., and Sarucci, R. (1992). Principles of exposure measurement in epidemiology. Oxford University Press.
Bloemenkamp, K.W.M., Rosendaal, F.R., Buller, H.R., et al. (1999). Risk of venous thrombosis with use of current low-dose oral contraceptives is not explained by diagnostic suspicion and referral bias. Archives of Internal Medicine, 159, 65–70.
Breslow, N.E. and Day, N.E. (1980). Statistical methods in cancer research. Vol. 1: The analysis of case–control studies. Scientific Publication No. 32, IARC, Lyon.
Crombie, I.K. (1981). The limitations of case–control studies in the detection of environmental carcinogens. Journal of Epidemiology and Community Health, 35, 281–7.
Cummings, P. and Weiss, N.S. (1998). Case series and exposure series: the role of studies without controls in providing information about the etiology of injury or disease. Injury Prevention,4, 34–57.
Daling, J.R., Weiss, N.S., Klopfenstein, L.L., et al. (1982). Correlates of homosexual behavior and the incidence of anal cancer. Journal of the American Medical Association, 247, 1988–90.
Daling, J.R., Weiss, N.S., Hislop, T.G., et al. (1987). Sexual practices, sexually transmitted diseases, and the incidence of anal cancer. New England Journal of Medicine,317, 973–7.
Doll, R. and Hill, A.B. (1950). Smoking and carcinoma of the lung. British Medical Journal, 2, 739–48.
Greenberg, E.R., Rosner, B., Nennekens, C., et al. (1985). An investigation of bias in a study of nuclear shipyard workers. American Journal of Epidemiology, 121, 301–8.
Greenland, S. and Thomas, D.C. (1982). On the need for the rare disease assumption in case–control studies. American Journal of Epidemiology, 116, 547–53.
Greenwald, P., Barlow, J.J., Nasca, P., et al. (1971). Vaginal cancer after maternal treatment with synthetic estrogens. New England Journal of Medicine, 285, 390–3.
Herbst, A.L., Ulfelder, H., and Poskanzer, D.C. (1971). Adenocarcinoma of the vagina: association of maternal stilbestrol therapy with tumor appearance in young women. New England Journal of Medicine, 284, 878–81.
Holcomb, R.L. (1938). Alcohol in relation to traffic accidents. Journal of the American Medical Association, 111, 1076–85.
Horwitz, R.I. and Feinstein, A.R. (1978). Alternative analytic methods for case–control studies of estrogens and endometrial cancer. New England Journal of Medicine, 299, 1089–94.
Hurwitz, E.S., Barren, M.J., Bregman, D., et al. (1985). Public Health Service Study on Reye’s syndrome and medications. Report of the Pilot Phase. New England Journal of Medicine, 313, 849–57.
Janerich, D.T., Thompson, W.D., Varela, L.R., et al. (1990). Lung cancer and exposure to tobacco smoke in the household. New England Journal of Medicine, 323, 632–6.
McLaughlin, J.K., Blot, W.J., Mehl, E.S., et al. (1985). Problems in the use of dead controls in case–control studies. II. Effect of excluding certain causes of death. American Journal of Epidemiology, 122, 485–94.
Nelson, L.M., Longstreth, W.T., Koespell, T.D., et al. (1990). Proxy respondents in epidemiologic research. Epidemiology Review, 12, 71–86.
Pearce, N. (1993). What does the odds ratio estimate in a case–control study? International Journal of Epidemiology, 22, 1189–92.
Rinsky, R.A., Zumwolde, R.D., Waxweiller, R.J., et al. (1981). Cancer mortality at a naval nuclear shipyard. Lancet, 1, 231–5.
Rosenberg, L., Mitchell, A.A., Parsells, J.L., et al. (1983). Lack of relation of oral clefts to diazepam use during pregnancy. New England Journal of Medicine, 309, 1282–5.
Rothman, K.J. and Greenland, S. (1998). Modern epidemiology (2nd edn). Lippincott-Raven, Philadelphia, PA.
Selby, J.V. (1994). Case control evaluations of treatment and program efficacy. Epidemiology Review, 46, 91–101.
Shapiro, S., Kelly, J.P., Rosenberg, L., et al. (1985). Risk of localized and widespread endometrial cancer in relation to recent and discontinued use of conjugated estrogens.New England Journal of Medicine, 313, 969–72.
Silverman, D.T., Hoover, R.N., and Swanson, G.M. (1983). Artificial sweeteners and lower urinary tract cancer: hospital vs. population controls. American Journal of Epidemiology, 117, 326–34.
Siscovick, D.S., Weiss, N.S., Hallstrom, A.P., et al. (1982). Physical activity and primary cardiac arrest. Journal of the American Medical Association, 248, 3113–17.
Stott, D.H. (1958). Some psychosomatic aspects of casualty in reproduction.Journal of Psychosomatic Research, 3, 42–55.
Strathy, J.H., Molgaard, C.A., Coulam, C.B., et al. (1982). Endometriosis and infertility: A laparoscopic study of endometriosis among fertile and infertile women. Fertility and Sterility, 38, 667–72.
Tabuenca, J.M. (1981). Toxic-allergic syndrome caused by ingestion of rapeseed oil denatured with aniline. Lancet, ii, 567–8.
Thom, D.H., Grayston, J.T., Siscovick, D.S., et al. (1992). Association of prior infection with Chlamydia pneumoniae and angiographically demonstrated coronary artery disease. Journal of the American Medical Association, 268, 68–72.
Ulfelder, H. and Robboy, S.J. (1976). The embryologic development of the human vagina. American Journal of Obstetrics and Gynecology, 126, 769–76.
Victora, C.G., Smith, P.G., Vaughn, J.P., et al. (1989). Infant feeding and deaths due to diarrhea. American Journal of Epidemiology, 129, 1032–41.
Weiss, N.S. (1994). Application of the case–control method in the evaluation of screening. Epidemiology Review, 16, 102–8.
Weiss, N.S., Lyon, J.L., Liff, J.M., et al. (1981). Incidence of ovarian cancer in relation to the use of oral contraceptives. International Journal of Cancer, 28, 669–71.
Witte, J.S., Gauderman, W.J., and Thomas, D.C. (1999). Asymptotic bias and efficiency in case–control studies of candidate genes and gene-environment interactions: basic family designs. American Journal of Epidemiology, 149, 693–705.
Yang, Q. and Khoury, M.J. (1997). Evolving methods in genetic epidemiology. III. Gene–environment interaction in epidemiologic research. Epidemiology Review, 19, 33–43.