case control study in research methodology

Pearce N.  Classification of Epidemiological Studies .Int J Epidemiol (2012) 41 (2): 393-397.  (This article talks about there really only being 4 types of epidemiological studies: incidence studies, prevalance studies, incidence case-control studies and prevalance case control studies.  The differences being the outcome and whether or not you sample on outcome).

Introduction

The case-control study design, sampling of cases, sampling of controls, case-control studies – an efficient observational study design.

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Karlijn J. van Stralen , Friedo W. Dekker , Carmine Zoccali , Kitty J. Jager; Case-Control Studies – An Efficient Observational Study Design. Nephron Clinical Practice 1 February 2010; 114 (1): c1–c4. https://doi.org/10.1159/000242442

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Case-control studies are an efficient research method for investigating risk factors of a disease. The method involves the comparison of the odds of exposure in a patient group with that of the odds of exposure in a control group. As only a minority of the population is included in the study, less time can be devoted to those who remain free of the disease of interest. The design of a case-control study can be complex due to the selection of the appropriate cases and controls. Cases can be identified in a prospective and retrospective manner from various sources. Controls can be obtained via the patient, random digit dialing or in a hospital and all at different points in the time period of the study. All options have their own advantages and disadvantages. Furthermore, different forms of bias, such as recall bias and selection bias, can occur. When appropriately designed, case-control studies can provide the same information as in a cohort study, in a more rapid and efficient manner.

In the previous paper, we discussed the cohort study design [ 1 ]. In cohort studies, much effort is devoted to the follow-up of subjects who remain free of the disease of interest, as usually only a minority of the study population actually develop the disease. Case-control studies aim to obtain the same information as cohort studies: the difference in exposure to risk factors in subjects in relation to the development of the disease. But, unlike in cohort studies, only a minority of the population is included in the study, namely all cases (patients) and a selected number of control subjects. Furthermore, as data on exposure are being collected in retrospect, case-control studies can be much more efficient. Nevertheless, case-control studies have, besides the ‘general types of bias’, their own specific sources of bias. Also, the selection of cases and controls may be quite complex. In the current paper, we will discuss the basic aspects of the design and the conduct of a case-control study and we will touch upon its major difficulties.

Like case reports and case series, case-control studies can be seen as the natural expansion of the daily practice of physicians [ 2 ]. Cases are selected on the basis of the presence of the disease of interest. By asking questions to the patients or by obtaining data from medical records about the period prior to the occurrence of the disease, these cases are then classified into either exposed or unexposed to a particular risk factor. In a case series, one considers it sufficient to observe that the risk factor is present in many more cases than anticipated (some people call this ‘expected’ exposure to the risk factor a kind of ‘mental control group’). However, one could easily imagine that this mental control group is dependent on a physician’s experience and practice and that the responses of cases could depend on the way of questioning. Therefore, in a case-control study, a formal comparison with the exposure rate in controls is made. The controls are usually a representative sample of the population from which the cases originated (‘source population’; fig. 1 ). As only a sample of the population under study is included, it is not possible to determine the incidence rates in the exposed and unexposed groups, and therefore, no relative risk can be determined. However, the odds of exposure can be assessed in both groups, resulting in an odds ratio. This odds ratio can be interpreted as a relative risk, under conditions that will be explained in detail in a future paper.

Both cases and controls are sampled from a (hypothetical) source population, free of disease at the start. While the cases are sampled over time, controls can be selected in 3 different fashions: (1) the traditional case-control study with controls sampled at the end of the time period; (2) the incidence density case-control study, in which controls are sampled each time a case occurs, and (3) the case-base study, in which the controls are sampled at the (hypothetical) start of the study. When using methods 2 and 3, controls can be included in the study multiple times, both as control and as a case. When using method 1, all controls are still free of disease at the end of the time period and can therefore never be included as case.

An example of a case-control study is the one by Fored et al. [ 3 ] on the relationship between aspirin use and chronic kidney disease (CKD). Cases were patients with newly diagnosed CKD, as determined by increased serum creatinine levels, who were identified in the Swedish population register. Out of the source population of 5.3 million individuals, 926 cases were identified who had developed CKD in the preceding 2 years. The 998 controls were a random sample from the same register. Cases more often used aspirin (37%) compared with controls (19%) resulting in a 2.5 times higher risk of CKD in aspirin users compared with nonusers. If one would study this same relation between an exposure and CKD in a cohort study, to determine such an effect, one would need to include over 150,000 subjects and follow them for 1 year, because CKD is such a rare outcome. Therefore a case-control study design seems, indeed, the most efficient study design to investigate this relationship.

After the formulation of a research question and the decision to make use of the case-control study design, one must select eligible cases and controls. As a first step, one needs to define what a ‘case’ is. To avoid misclassification, objective criteria for the diagnosis of the disease under study are required. Moreover, a statement of eligibility criteria is essential in order to restrict the study to those who are potentially at risk for exposure. So, for example, in a study regarding the relation between oral contraceptives use and systemic lupus erythematosus, women who are postmenopausal or pregnant will need to be excluded, as they are not at risk of the use of oral contraceptives [ 4 ]. Naturally, the same eligibility criteria should be applied to the controls, as otherwise this could result in erroneous results [ 5 ].

Cases can be sampled from different sources, such as hospitals, medical records and disease or treatment registries and can be collected in 2 different ways. First, one could collect all prevalent cases, that is, all incident cases who developed the disease in the years before the start of the study, as in a retrospective cohort study. This is a very efficient and quick method. However, if the cases are patients with an unfavorable prognosis like end-stage renal disease for their study, it is likely that cases who would have been eligible died in the preceding years, resulting in a selection of only surviving cases. The second way of including cases is to collect all incident patients prospectively, i.e. to wait for a case to occur and include it into the study. This reduces the chances of including only a selection of cases (the survivors). The drawback is that this method is more time consuming and therefore less efficient.

In a case-control study, the decision which controls to select often proves to be more difficult than the selection of cases. If cases are difficult to sample one could increase the power of the study by collecting more controls than cases in the study. The first aspect needing careful attention is the choice of the population from which the controls will be derived. In principle, though not compulsory, controls should be derived from the same source population as the cases. Controls can be selected from the general population, by random-digit dialing (phone numbers), they can be obtained via the patient such as partners, friends or neighbors, or controls can be sampled from the same hospital as the case. Usually, there will be advantages for one type of control group that are missing in the other, and vice versa. For example, when studying risk factors associated with renal agenesis after a live birth [ 6 ], controls should be sampled from all live births. If patients with renal agenesis would be born more often in academic hospitals, it would not be adequate to sample controls only from babies born in the same hospital as the cases, as in this situation one would over-sample the number of babies born in academic hospitals. This may result in too high a number of babies and mothers with other diseases leading to an underestimation of the effect of potential exposures like diabetes.

A second point to address is the sampling scheme of controls. As in a cohort study, the source population must be free of the disease of interest at the start of inclusion in the study. A person is eligible to be selected as a control as long as they are free of this disease [ 7,8 ]. Therefore, theoretically, they can be included in the study multiple times, both as control and as a case. One could sample controls in 3 different manners (fig. 1 ). First, one could sample controls at the end of inclusion in the study (traditional case-control study). A second option is to sample controls each time a case occurs (incidence density sampling), and the third option is to sample controls before the first diagnosis of a case, i.e. at the (hypothetical) start of inclusion in the study (case-base study). Each sampling method has different consequences for the interpretation of the odds ratio but this is beyond the scope of this paper. In short, the case-base study and the incidence density sample case-control study will provide an accurate estimate of the relative risk. The traditional case-control study provides an accurate estimate if the disease is sufficiently rare, i.e. the ‘rare disease assumption’.

As in other types of study designs, in a case-control study, multiple types of bias can occur. If cases and controls are not derived from a similar population or if they have different chances of being exposed, selection bias may arise. Another important source of bias, which is unique for case-control studies, is recall bias. This occurs when a subject is interviewed to obtain exposure information after the disease has occurred. As the case is suffering from the disease, they may search their memory for any history of exposure. Controls do not have such a stimulus, which possibly results in less accurate or more socially acceptable answers. For example, in a study of risk factors for acute pyelonephritis, women were asked to give information about the number of urinary tract infections (UTI) in their mothers [ 9 ]. Women with pyelonephritis may have asked their mothers on their history of UTI, resulting in accurate estimates of the percentage exposed. However, controls may be unaware of the history of UTI in their mothers, simply because they have not asked them. Therefore, even if there would be no association between the exposure and outcome, it is still possible to find an effect. This bias could be avoided in several ways. One could obtain information regarding exposure from sources that documented the information before the outcome was known such as medical records. However, such records may not be available for healthy individuals. It is also possible to send the questionnaire by mail so that cases and controls both have enough time to obtain accurate answers. Finally, it is important to use trained interviewers, preferably unaware (‘blind’) of the subject’s disease status and use standardized questionnaires. Another solution is to obtain information from persons who have had a similar stimulus such as women with a different disease, resulting in an equal motivation to recall potentially relevant exposures. However, if both diseases would have ‘joint’ exposures, this would result in an underestimation of the effect of the exposure on the disease under study.

Although textbooks on epidemiology agree on the use of the terminology regarding case-control studies, authors of many papers have applied the term incorrectly. Recent reviews of articles in the fields of pediatrics and surgery showed that in 25–65% of the articles describing themselves as case-control studies had in fact another study design [ 10,11 ]. In these papers, the terms ‘cases’ and ‘controls’ were used to denote subjects who were affected or unaffected by a given risk factor, for example diabetic versus nondiabetic patients. Subjects were then followed forward in time to assess development of another outcome, for example CKD. However, although patients are compared with non-patients, this study design is a cohort study, as subjects are followed in time to assess the effect of exposure (in this case diabetes) to an outcome (in this case CKD). Although these studies may be of good quality, incorrect use of the terms of the used study design may lead to confusion with readers [ 12 ].

In summary, case-control studies are an efficient design to study associations in a relatively cheap and rapid manner. When appropriately designed, they can provide the same information as obtained in a cohort study. Nevertheless, selection of both cases and controls is complex and also case-control studies are subject to multiple sources of bias. Therefore, before starting a case-control study, it is advisable to consult an epidemiologist or statistician.

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Case-Control Studies

Introduction

Cohort studies have an intuitive logic to them, but they can be very problematic when one is investigating outcomes that only occur in a small fraction of exposed and unexposed individuals. They can also be problematic when it is expensive or very difficult to obtain exposure information from a cohort. In these situations a case-control design offers an alternative that is much more efficient. The goal of a case-control study is the same as that of cohort studies, i.e., to estimate the magnitude of association between an exposure and an outcome. However, case-control studies employ a different sampling strategy that gives them greater efficiency.

Learning Objectives

After completing this module, the student will be able to:

• Define and explain the distinguishing features of a case-control study
• Describe  and identify the types of epidemiologic questions that can be addressed by case-control studies
• Define what is meant by the term "source population"
• Describe the purpose of controls in a case-control study
• Describe differences between hospital-based and population-based case-control studies
• Describe the principles of valid control selection
• Explain the importance of using specific diagnostic criteria and explicit case definitions in case-control studies
• Estimate and interpret the odds ratio from a case-control study
• Identify the potential strengths and limitations of case-control studies

Overview of Case-Control Design

In the module entitled Overview of Analytic Studies it was noted that Rothman describes the case-control strategy as follows:

"Case-control studies are best understood by considering as the starting point a source population , which represents a hypothetical study population in which a cohort study might have been conducted. The source population is the population that gives rise to the cases included in the study. If a cohort study were undertaken, we would define the exposed and unexposed cohorts (or several cohorts) and from these populations obtain denominators for the incidence rates or risks that would be calculated for each cohort. We would then identify the number of cases occurring in each cohort and calculate the risk or incidence rate for each. In a case-control study the same cases are identified and classified as to whether they belong to the exposed or unexposed cohort. Instead of obtaining the denominators for the rates or risks, however, a control group is sampled from the entire source population that gives rise to the cases. Individuals in the control group are then classified into exposed and unexposed categories. The purpose of the control group is to determine the relative size of the exposed and unexposed components of the source population. Because the control group is used to estimate the distribution of exposure in the source population, the cardinal requirement of control selection is that the controls be sampled independently of exposure status."

To illustrate this consider the following hypothetical scenario in which the source population is the state of Massachusetts. Diseased individuals are red, and non-diseased individuals are blue. Exposed individuals are indicated by a whitish midsection. Note the following aspects of the depicted scenario:

• The disease is rare.
• There is a fairly large number of exposed individuals in the state, but most of these are not diseased.

If we somehow had exposure and outcome information on all of the subjects in the source population and looked at the association using a cohort design, we might find the data summarized in the contingency table below.

In this hypothetical example, we have data on all 6,000,000 people in the source population, and we could compute the probability of disease (i.e., the risk or incidence) in both the exposed group and the non-exposed group, because we have the denominators for both the exposed and non-exposed groups.

The table above summarizes all of the necessary information regarding exposure and outcome status for the population and enables us to compute a risk ratio as a measure of the strength of the association. Intuitively, we compute the probability of disease (the risk) in each exposure group and then compute the risk ratio as follows:

The problem , of course, is that we usually don't have the resources to get the data on all subjects in the population. If we took a random sample of even 5-10% of the population, we would have few diseased people in our sample, certainly not enough to produce a reasonably precise measure of association. Moreover, we would expend an inordinate amount of effort and money collecting exposure and outcome data on a large number of people who would not develop the outcome.

We need a method that allows us to retain all the people in the numerator of disease frequency (diseased people or "cases") but allows us to collect information from only a small proportion of the people that make up the denominator (population, or "controls"), most of whom do not have the disease of interest. The case-control design allows us to accomplish this. We identify and collect exposure information on all the cases, but identify and collect exposure information on only a sample of the population. Once we have the exposure information, we can assign subjects to the numerator and denominator of the exposed and unexposed groups. This is what Rothman means when he says,

"The purpose of the control group is to determine the relative size of the exposed and unexposed components of the source population."

In the above example, we would have identified all 1,300 cases, determined their exposure status, and ended up categorizing 700 as exposed and 600 as unexposed. We might have ransomly sampled 6,000 members of the population (instead of 6 million) in order to determine the exposure distribution in the total population. If our sampling method was random, we would expect that about 1,000 would be exposed and 5,000 unexposed (the same ratio as in the overall population). We calculate a similar measure as the risk ratio above, but substituting in the denominator a sample of the population ("controls") instead of the whole population:

Note that when we take a sample of the population, we no longer have a measure of disease frequency, because the denominator no longer represents the population. Therefore, we can no longer compute the probability or rate of disease incidence in each exposure group. We also can't calculate a risk or rate difference measure for the same reason. However, as we have seen, we can compute the relative probability of disease in the exposed vs. unexposed group. The term generally used for this measure is an odds ratio , described in more detail later in the module.

Consequently, when the outcome is uncommon, as in this case, the risk ratio can be estimated much more efficiently by using a case-control design. One would focus first on finding an adequate number of cases in order to determine the ratio of exposed to unexposed cases. Then, one only needs to take a sample of the population in order to estimate the relative size of the exposed and unexposed components of the source population. Note that if one can identify all of the cases that were reported to a registry or other database within a defined period of time, then it is possible to compute an estimate of the incidence of disease if the size of the population is known from census data.   While this is conceptually possible, it is rarely done, and we will not discuss it further in this course.

A Nested Case-Control Study

Suppose a prospective cohort study were conducted among almost 90,000 women for the purpose of studying the determinants of cancer and cardiovascular disease. After enrollment, the women provide baseline information on a host of exposures, and they also provide baseline blood and urine samples that are frozen for possible future use. The women are then followed, and, after about eight years, the investigators want to test the hypothesis that past exposure to pesticides such as DDT is a risk factor for breast cancer. Eight years have passed since the beginning of the study, and 1.439 women in the cohort have developed breast cancer. Since they froze blood samples at baseline, they have the option of analyzing all of the blood samples in order to ascertain exposure to DDT at the beginning of the study before any cancers occurred. The problem is that there are almost 90,000 women and it would cost $20 to analyze each of the blood samples. If the investigators could have analyzed all 90,000 samples this is what they would have found the results in the table below.

Table of Breast Cancer Occurrence Among Women With or Without DDT Exposure

If they had been able to afford analyzing all of the baseline blood specimens in order to categorize the women as having had DDT exposure or not, they would have found a risk ratio = 1.87 (95% confidence interval: 1.66-2.10). The problem is that this would have cost almost $1.8 million, and the investigators did not have the funding to do this.

While 1,439 breast cancers is a disturbing number, it is only 1.6% of the entire cohort, so the outcome is relatively rare, and it is costing a lot of money to analyze the blood specimens obtained from all of the non-diseased women. There is, however, another more efficient alternative, i.e., to use a case-control sampling strategy. One could analyze all of the blood samples from women who had developed breast cancer, but only a sample of the whole cohort in order to estimate the exposure distribution in the population that produced the cases.

If one were to analyze the blood samples of 2,878 of the non-diseased women (twice as many as the number of cases), one would obtain results that would look something like those in the next table.

Odds of Exposure: 360/1079 in the cases versus 432/2,446 in the non-diseased controls.

Totals Samples analyzed = 1,438+2,878 = 4,316

Total Cost = 4,316 x $20 = $86,320

With this approach a similar estimate of risk was obtained after analyzing blood samples from only a small sample of the entire population at a fraction of the cost with hardly any loss in precision. In essence, a case-control strategy was used, but it was conducted within the context of a prospective cohort study. This is referred to as a case-control study "nested" within a cohort study.

Rothman states that one should look upon all case-control studies as being "nested" within a cohort. In other words the cohort represents the source population that gave rise to the cases. With a case-control sampling strategy one simply takes a sample of the population in order to obtain an estimate of the exposure distribution within the population that gave rise to the cases. Obviously, this is a much more efficient design.

It is important to note that, unlike cohort studies, case-control studies do not follow subjects through time. Cases are enrolled at the time they develop disease and controls are enrolled at the same time. The exposure status of each is determined, but they are not followed into the future for further development of disease.

As with cohort studies, case-control studies can be prospective or retrospective. At the start of the study, all cases might have already occurred and then this would be a retrospective case-control study. Alternatively, none of the cases might have already occurred, and new cases will be enrolled prospectively. Epidemiologists generally prefer the prospective approach because it has fewer biases, but it is more expensive and sometimes not possible. When conducted prospectively, or when nested in a prospective cohort study, it is straightforward to select controls from the population at risk. However, in retrospective case-control studies, it can be difficult to select from the population at risk, and controls are then selected from those in the population who didn't develop disease. Using only the non-diseased to select controls as opposed to the whole population means the denominator is not really a measure of disease frequency, but when the disease is rare , the odds ratio using the non-diseased will be very similar to the estimate obtained when the entire population is used to sample for controls. This phenomenon is known as the r are-disease assumption . When case-control studies were first developed, most were conducted retrospectively, and it is sometimes assumed that the rare-disease assumption applies to all case-control studies. However, it actually only applies to those case-control studies in which controls are sampled only from the non-diseased rather than the whole population.  

The difference between sampling from the whole population and only the non-diseased is that the whole population contains people both with and without the disease of interest. This means that a sampling strategy that uses the whole population as its source must allow for the fact that people who develop the disease of interest can be selected as controls. Students often have a difficult time with this concept. It is helpful to remember that it seems natural that the population denominator includes people who develop the disease in a cohort study. If a case-control study is a more efficient way to obtain the information from a cohort study, then perhaps it is not so strange that the denominator in a case-control study also can include people who develop the disease. This topic is covered in more detail in EP813 Intermediate Epidemiology.

Retrospective and Prospective Case-Control Studies

Students usually think of case-control studies as being only retrospective, since the investigators enroll subjects who have developed the outcome of interest. However, case-control studies, like cohort studies, can be either retrospective or prospective. In a prospective case-control study, the investigator still enrolls based on outcome status, but the investigator must wait to the cases to occur.

When is a Case-Control Study Desirable?

Given the greater efficiency of case-control studies, they are particularly advantageous in the following situations:

• When the disease or outcome being studied is rare.
• When the disease or outcome has a long induction and latent period (i.e., a long time between exposure and the eventual causal manifestation of disease).
• When exposure data is difficult or expensive to obtain.
• When the study population is dynamic.
• When little is known about the risk factors for the disease, case-control studies provide a way of testing associations with multiple potential risk factors. (This isn't really a unique advantage to case-control studies, however, since cohort studies can also assess multiple exposures.)

Another advantage of their greater efficiency, of course, is that they are less time-consuming and much less costly than prospective cohort studies.

The DES Case-Control Study

A classic example of the efficiency of the case-control approach is the study (Herbst et al.: N. Engl. J. Med. Herbst et al. (1971;284:878-81) that linked in-utero exposure to diethylstilbesterol (DES) with subsequent development of vaginal cancer 15-22 years later. In the late 1960s, physicians at MGH identified a very unusual cancer cluster. Eight young woman between the ages of 15-22 were found to have cancer of the vagina, an uncommon cancer even in elderly women. The cluster of cases in young women was initially reported as a case series, but there were no strong hypotheses about the cause.

In retrospect, the cause was in-utero exposure to DES. After World War II, DES started being prescribed for women who were having troubles with a pregnancy -- if there were signs suggesting the possibility of a miscarriage, DES was frequently prescribed. It has been estimated that between 1945-1950 DES was prescribed for about 20% of all pregnancies in the Boston area. Thus, the unborn fetus was exposed to DES in utero, and in a very small percentage of cases this resulted in development of vaginal cancer when the child was 15-22 years old (a very long latent period). There were several reasons why a case-control study was the only feasible way to identify this association: the disease was extremely rare (even in subjects who had been exposed to DES), there was a very long latent period between exposure and development of disease, and initially they had no idea what was responsible, so there were many possible exposures to consider.

In this situation, a case-control study was the only reasonable approach to identify the causative agent. Given how uncommon the outcome was, even a large prospective study would have been unlikely to have more than one or two cases, even after 15-20 years of follow-up. Similarly, a retrospective cohort study might have been successful in enrolling a large number of subjects, but the outcome of interest was so uncommon that few, if any, subjects would have had it. In contrast, a case-control study was conducted in which eight known cases and 32 age-matched controls provided information on many potential exposures. This strategy ultimately allowed the investigators to identify a highly significant association between the mother's treatment with DES during pregnancy and the eventual development of adenocarcinoma of the vagina in their daughters (in-utero at the time of exposure) 15 to 22 years later.

For more information see the DES Fact Sheet from the National Cancer Institute.

An excellent summary of this landmark study and the long-range effects of DES can be found in a Perspective article in the New England Journal of Medicine. A cohort of both mothers who took DES and their children (daughters and sons) was later formed to look for more common outcomes. Members of the faculty at BUSPH are on the team of investigators that follow this cohort for a variety of outcomes, particularly reproductive consequences and other cancers.

Selecting & Defining Cases and Controls

The "case" definition.

Careful thought should be given to the case definition to be used. If the definition is too broad or vague, it is easier to capture people with the outcome of interest, but a loose case definition will also capture people who do not have the disease. On the other hand, an overly restrictive case definition is employed, fewer cases will be captured, and the sample size may be limited. Investigators frequently wrestle with this problem during outbreak investigations. Initially, they will often use a somewhat broad definition in order to identify potential cases. However, as an outbreak investigation progresses, there is a tendency to narrow the case definition to make it more precise and specific, for example by requiring confirmation of the diagnosis by laboratory testing. In general, investigators conducting case-control studies should thoughtfully construct a definition that is as clear and specific as possible without being overly restrictive.

Investigators studying chronic diseases generally prefer newly diagnosed cases, because they tend to be more motivated to participate, may remember relevant exposures more accurately, and because it avoids complicating factors related to selection of longer duration (i.e., prevalent) cases. However, it is sometimes impossible to have an adequate sample size if only recent cases are enrolled.

Sources of Cases

Typical sources for cases include:

• Patient rosters at medical facilities
• Death certificates
• Disease registries (e.g., cancer or birth defect registries; the SEER Program [Surveillance, Epidemiology and End Results] is a federally funded program that identifies newly diagnosed cases of cancer in population-based registries across the US )
• Cross-sectional surveys (e.g., NHANES, the National Health and Nutrition Examination Survey)

Selection of the Controls

As noted above, it is always useful to think of a case-control study as being nested within some sort of a cohort, i.e., a source population that produced the cases that were identified and enrolled. In view of this there are two key principles that should be followed in selecting controls:

• The comparison group ("controls") should be representative of the source population that produced the cases.
• The "controls" must be sampled in a way that is independent of the exposure, meaning that their selection should not be more (or less) likely if they have the exposure of interest.

If either of these principles are not adhered to, selection bias can result (as discussed in detail in the module on Bias).

Note that in the earlier example of a case-control study conducted in the Massachusetts population, we specified that our sampling method was random so that exposed and unexposed members of the population had an equal chance of being selected. Therefore, we would expect that about 1,000 would be exposed and 5,000 unexposed (the same ratio as in the whole population), and came up with an odds ratio that was same as the hypothetical risk ratio we would have had if we had collected exposure information from the whole population of six million:

What if we had instead been more likely to sample those who were exposed, so that we instead found 1,500 exposed and 4,500 unexposed among the 6,000 controls?   Then the odds ratio would have been:

This odds ratio is biased because it differs from the true odds ratio.   In this case, the bias stemmed from the fact that we violated the second principle in selection of controls. Depending on which category is over or under-sampled, this type of bias can result in either an underestimate or an overestimate of the true association.

A hypothetical case-control study was conducted to determine whether lower socioeconomic status (the exposure) is associated with a higher risk of cervical cancer (the outcome). The "cases" consisted of 250 women with cervical cancer who were referred to Massachusetts General Hospital for treatment for cervical cancer. They were referred from all over the state. The cases were asked a series of questions relating to socioeconomic status (household income, employment, education, etc.). The investigators identified control subjects by going door-to-door in the community around MGH from 9:00 AM to 5:00  PM. Many residents are not home, but they persist and eventually enroll enough controls. The problem is that the controls were selected by a different mechanism than the cases, AND the selection mechanism may have tended to select individuals of different socioeconomic status, since women who were at home may have been somewhat more likely to be unemployed. In other words, the controls were more likely to be enrolled (selected) if they had the exposure of interest (lower socioeconomic status). 

Sources for "Controls"

Population controls:.

A population-based case-control study is one in which the cases come from a precisely defined population, such as a fixed geographic area, and the controls are sampled directly from the same population. In this situation cases might be identified from a state cancer registry, for example, and the comparison group would logically be selected at random from the same source population. Population controls can be identified from voter registration lists, tax rolls, drivers license lists, and telephone directories or by "random digit dialing". Population controls may also be more difficult to obtain, however, because of lack of interest in participating, and there may be recall bias, since population controls are generally healthy and may remember past exposures less accurately.

Example of a Population-based Case-Control Study: Rollison et al. reported on a "Population-based Case-Control Study of Diabetes and Breast Cancer Risk in Hispanic and Non-Hispanic White Women Living in US Southwestern States". (ALink to the article - Citation: Am J Epidemiol 2008;167:447–456).

"Briefly, a population-based case-control study of breast cancer was conducted in Colorado, New Mexico, Utah, and selected counties of Arizona. For investigation of differences in the breast cancer risk profiles of non-Hispanic Whites and Hispanics, sampling was stratified by race/ethnicity, and only women who self-reported their race as non-Hispanic White, Hispanic, or American Indian were eligible, with the exception of American Indian women living on reservations. Women diagnosed with histologically confirmed breast cancer between October 1999 and May 2004 (International Classification of Diseases for Oncology codes C50.0–C50.6 and C50.8–C50.9) were identified as cases through population-based cancer registries in each state."

"Population-based controls were frequency-matched to cases in 5-year age groups. In New Mexico and Utah, control participants under age 65 years were randomly selected from driver's license lists; in Arizona and Colorado, controls were randomly selected from commercial mailing lists, since driver's license lists were unavailable. In all states, women aged 65 years or older were randomly selected from the lists of the Centers for Medicare and Medicaid Services (Social Security lists). Of all women contacted, 68 percent of cases and 42 percent of controls participated in the study."

"Odds ratios and 95% confidence intervals were calculated using logistic regression, adjusting for age, body mass index at age 15 years, and parity. Having any type of diabetes was not associated with breast cancer overall (odds ratio = 0.94, 95% confidence interval: 0.78, 1.12). Type 2 diabetes was observed among 19% of Hispanics and 9% of non-Hispanic Whites but was not associated with breast cancer in either group."

In this example, it is clear that the controls were selected from the source population (principle 1), but less clear that they were enrolled independent of exposure status (principle 2), both because drivers' licenses were used for selection and because the participation rate among controls was low. These factors would only matter if they impacted on the estimate of the proportion of the population who had diabetes.

Hospital or Clinic Controls:

• They have diseases that are unrelated to the exposure being studied. For example, for a study examining the association between smoking and lung cancer, it would not be appropriate to include patients with cardiovascular disease as control, since smoking is a risk factor for cardiovascular disease. To include such patients as controls would result in an underestimate of the true association.
• Second, control patients in the comparison should have diseases with similar referral patterns as the cases, in order to minimize selection bias. For example, if the cases are women with cervical cancer who have been referred from all over the state, it would be inappropriate to use controls consisting of women with diabetes who had been referred primarily from local health centers in the immediate vicinity of the hospital. Similarly, it would be inappropriate to use patients from the emergency room, because the selection of a hospital for an emergency is different than for cancer, and this difference might be related to the exposure of interest.

The advantages of using controls who are patients from the same facility are:

• They are easier to identify
• They are more likely to participate than general population controls.
• They minimize selection bias because they generally come from the same source population (provided referral patterns are similar).
• Recall bias would be minimized, because they are sick, but with a different diagnosis.

Example: Several years ago the vascular surgeons at Boston Medical Center wanted to study risk factors for severe atherosclerosis of the lower extremities. The cases were patients who were referred to the hospital for elective surgery to bypass severe atherosclerotic blockages in the arteries to the legs. The controls consisted of patients who were admitted to the same hospital for elective joint replacement of the hip or knee. The patients undergoing joint replacement were similar in age and they also were following the same referral pathways. In other words, they met the "would" criterion: if one of the joint replacement surgery patients had developed severe atherosclerosis in their leg arteries, they would have been referred to the same hospital.

Friend, Neighbor, Spouse, and Relative Controls:

Occasionally investigators will ask cases to nominate controls who are in one of these categories, because they have similar characteristics, such as genotype, socioeconomic status, or environment, i.e., factors that can cause confounding, but are hard to measure and adjust for. By matching cases and controls on these factors, confounding by these factors will be controlled.   However, one must be careful that the controls satisfy the two fundamental principles. Often, they do not.

How Many Controls?

Since case-control studies are often used for uncommon outcomes, investigators often have a limited number of cases but a plentiful supply of potential controls. In this situation the statistical power of the study can be increased somewhat by enrolling more controls than cases. However, the additional power that is achieved diminishes as the ratio of controls to cases increases, and ratios greater than 4:1 have little additional impact on power. Consequently, if it is time-consuming or expensive to collect data on controls, the ratio of controls to cases should be no more than 4:1. However, if the data on controls is easily obtained, there is no reason to limit the number of controls.

Methods of Control Sampling

There are three strategies for selecting controls that are best explained by considering the nested case-control study described on page 3 of this module:

• Survivor sampling: This is the most common method. Controls consist of individuals from the source population who do not have the outcome of interest.
• Case-base sampling (also known as "case-cohort" sampling): Controls are selected from the population at risk at the beginning of the follow-up period in the cohort study within which the case-control study was nested.
• Risk Set Sampling: In the nested case-control study a control would be selected from the population at risk at the point in time when a case was diagnosed.

The Rare Outcome Assumption

It is often said that an odds ratio provides a good estimate of the risk ratio only when the outcome of interest is rare, but this is only true when survivor sampling is used. With case-base sampling or risk set sampling, the odds ratio will provide a good estimate of the risk ratio regardless of the frequency of the outcome, because the controls will provide an accurate estimate of the distribution in the source population (i.e., not just in non-diseased people).

More on Selection Bias

Always consider the source population for case-control studies, i.e. the "population" that generated the cases. The cases are always identified and enrolled by some method or a set of procedures or circumstances. For example, cases with a certain disease might be referred to a particular tertiary hospital for specialized treatment. Alternatively, if there is a database or a disease registry for a geographic area, cases might be selected at random from the database. The key to avoiding selection bias is to select the controls by a similar, if not identical, mechanism in order to ensure that the controls provide an accurate representation of the exposure status of the source population.

Example 1: In the first example above, in which cases were randomly selected from a geographically defined database, the source population is also defined geographically, so it would make sense to select population controls by some random method. In contrast, if one enrolled controls from a particular hospital within the geographic area, one would have to at least consider whether the controls were inherently more or less likely to have the exposure of interest. If so, they would not provide an accurate estimate of the exposure distribution of the source population, and selection bias would result.

Example 2: In the second example above, the source population was defined by the patterns of referral to a particular hospital for a particular disease. In order for the controls to be representative of the "population" that produced those cases, the controls should be selected by a similar mechanism, e.g., by contacting the referring health care providers and asking them to provide the names of potential controls. By this mechanism, one can ensure that the controls are representative of the source population, because if they had had the disease of interest they would have been just as likely as the cases to have been included in the case group (thus fulfilling the "would" criterion).

Example 3: A food handler at a delicatessen who is infected with hepatitis A virus is responsible for an outbreak of hepatitis which is largely confined to the surrounding community from which most of the customers come. Many (but not all) of the infected cases are identified by passive and active surveillance. How should controls be selected? In this situation, one might guess that the likelihood of people going to the delicatessen would be heavily influenced by their proximity to it, and this would to a large extent define the source population. In a case-control study undertaken to identify the source, the delicatessen is one of the exposures being tested. Consequently, even if the cases were reported to the state-wide surveillance system, it would not be appropriate to randomly select controls from the state, the county, or even the town where the delicatessen is located. In other words, the "would" criterion doesn't work here, because anyone in the state with clinical hepatitis would end up in the surveillance system, but someone who lived far from the deli would have a much lower likelihood of having the exposure. A better approach would be to select controls who were matched to the cases by neighborhood, age, and gender. These controls would have similar access to go to the deli if they chose to, and they would therefore be more representative of the source population.

Analysis of Case-Control Studies

The computation and interpretation of the odds ratio in a case-control study has already been discussed in the modules on Overview of Analytic Studies and Measures of Association. Additionally, one can compute the confidence interval for the odds ratio, and statistical significance can also be evaluated by using a chi-square test (or a Fisher's Exact Test if the sample size is small) to compute a p-value. These calculations can be done using the Case-Control worksheet in the Excel file called EpiTools.XLS.

Advantages and Disadvantages of Case-Control Studies

Advantages:

• They are efficient for rare diseases or diseases with a long latency period between exposure and disease manifestation.
• They are less costly and less time-consuming; they are advantageous when exposure data is expensive or hard to obtain.
• They are advantageous when studying dynamic populations in which follow-up is difficult.

Disadvantages:

• They are subject to selection bias.
• They are inefficient for rare exposures.
• Information on exposure is subject to observation bias.
• They generally do not allow calculation of incidence (absolute risk).