case control study is known as

Is the control group appropriate for the population? Does the study use matching or pairing appropriately to avoid the effects of a confounding variable? Does it use appropriate inclusion and exclusion criteria?

Fictitious Example

There is a suspicion that zinc oxide, the white non-absorbent sunscreen traditionally worn by lifeguards is more effective at preventing sunburns that lead to skin cancer than absorbent sunscreen lotions. A case-control study was conducted to investigate if exposure to zinc oxide is a more effective skin cancer prevention measure. The study involved comparing a group of former lifeguards that had developed cancer on their cheeks and noses (cases) to a group of lifeguards without this type of cancer (controls) and assess their prior exposure to zinc oxide or absorbent sunscreen lotions.

This study would be retrospective in that the former lifeguards would be asked to recall which type of sunscreen they used on their face and approximately how often. This could be either a matched or unmatched study, but efforts would need to be made to ensure that the former lifeguards are of the same average age, and lifeguarded for a similar number of seasons and amount of time per season.

Real-life Examples

Boubekri, M., Cheung, I., Reid, K., Wang, C., & Zee, P. (2014). Impact of windows and daylight exposure on overall health and sleep quality of office workers: a case-control pilot study . Journal of Clinical Sleep Medicine : JCSM : Official Publication of the American Academy of Sleep Medicine, 10 (6), 603-611. https://doi.org/10.5664/jcsm.3780

This pilot study explored the impact of exposure to daylight on the health of office workers (measuring well-being and sleep quality subjectively, and light exposure, activity level and sleep-wake patterns via actigraphy). Individuals with windows in their workplaces had more light exposure, longer sleep duration, and more physical activity. They also reported a better scores in the areas of vitality and role limitations due to physical problems, better sleep quality and less sleep disturbances.

Togha, M., Razeghi Jahromi, S., Ghorbani, Z., Martami, F., & Seifishahpar, M. (2018). Serum Vitamin D Status in a Group of Migraine Patients Compared With Healthy Controls: A Case-Control Study . Headache, 58 (10), 1530-1540. https://doi.org/10.1111/head.13423

This case-control study compared serum vitamin D levels in individuals who experience migraine headaches with their matched controls. Studied over a period of thirty days, individuals with higher levels of serum Vitamin D was associated with lower odds of migraine headache.

Related Formulas

Confounding

When an exposure and an outcome are both strongly associated with a third variable.

A patient who does not have the disease or outcome.

Matched Design

Each case is matched individually with a control according to certain characteristics such as age and gender. It is important to remember that the concordant pairs (pairs in which the case and control are either both exposed or both not exposed) tell us nothing about the risk of exposure separately for cases or controls.

Observed Assignment

The method of assignment of individuals to study and control groups in observational studies when the investigator does not intervene to perform the assignment.

Unmatched Design

The controls are a sample from a suitable non-affected population.

Now test yourself!

1. Case Control Studies are prospective in that they follow the cases and controls over time and observe what occurs.

a) True b) False

2. Which of the following is an advantage of Case Control Studies?

a) They can simultaneously look at multiple risk factors. b) They are useful to initially establish an association between a risk factor and a disease or outcome. c) They take less time to complete because the condition or disease has already occurred. d) b and c only e) a, b, and c

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Epidemiology in Practice: Case-Control Studies

Introduction.

A case-control study is designed to help determine if an exposure is associated with an outcome (i.e., disease or condition of interest). In theory, the case-control study can be described simply. First, identify the cases (a group known to have the outcome) and the controls (a group known to be free of the outcome). Then, look back in time to learn which subjects in each group had the exposure(s), comparing the frequency of the exposure in the case group to the control group.

By definition, a case-control study is always retrospective because it starts with an outcome then traces back to investigate exposures. When the subjects are enrolled in their respective groups, the outcome of each subject is already known by the investigator. This, and not the fact that the investigator usually makes use of previously collected data, is what makes case-control studies ‘retrospective’.

Advantages of Case-Control Studies

Case-control studies have specific advantages compared to other study designs. They are comparatively quick, inexpensive, and easy. They are particularly appropriate for (1) investigating outbreaks, and (2) studying rare diseases or outcomes. An example of (1) would be a study of endophthalmitis following ocular surgery. When an outbreak is in progress, answers must be obtained quickly. An example of (2) would be a study of risk factors for uveal melanoma, or corneal ulcers. Since case-control studies start with people known to have the outcome (rather than starting with a population free of disease and waiting to see who develops it) it is possible to enroll a sufficient number of patients with a rare disease. The practical value of producing rapid results or investigating rare outcomes may outweigh the limitations of case-control studies. Because of their efficiency, they may also be ideal for preliminary investigation of a suspected risk factor for a common condition; conclusions may be used to justify a more costly and time-consuming longitudinal study later.

Consider a situation in which a large number of cases of post-operative endophthalmitis have occurred in a few weeks. The case group would consist of all those patients at the hospital who developed post-operative endophthalmitis during a pre-defined period.

The definition of a case needs to be very specific:

There are not necessarily any ‘right’ answers to these questions but they must be answered before the study begins. At the end of the study, the conclusions will be valid only for patients who have the same sort of ‘endophthalmitis’ as in the case definition.

Controls should be chosen who are similar in many ways to the cases. The factors (e.g., age, sex, time of hospitalisation) chosen to define how controls are to be similar to the cases are the ‘matching criteria’. The selected control group must be at similar risk of developing the outcome; it would not be appropriate to compare a group of controls who had traumatic corneal lacerations with cases who underwent elective intraocular surgery. In our example, controls could be defined as patients who underwent elective intraocular surgery during the same period of time.

Matching Cases and Controls

Although controls must be like the cases in many ways, it is possible to over-match. Over-matching can make it difficult to find enough controls. Also, once a matching variable has been selected, it is not possible to analyse it as a risk factor. Matching for type of intraocular surgery (e.g., secondary IOL implantation) would mean including the same percentage of controls as cases who had surgery to implant a secondary IOL; if this were done, it would not be possible to analyse secondary IOL implantation as a potential risk factor for endophthalmitis.

An important technique for adding power to a study is to enroll more than one control for every case. For statistical reasons, however, there is little gained by including more than two controls per case.

Collecting Data

After clearly defining cases and controls, decide on data to be collected; the same data must be collected in the same way from both groups. Care must be taken to be objective in the search for past risk factors, especially since the outcome is already known, or the study may suffer from researcher bias. Although it may not always be possible, it is important to try to mask the outcome from the person who is collecting risk factor information or interviewing patients. Sometimes it will be necessary to interview patients about potential factors (such as history of smoking, diet, use of traditional eye medicines, etc.) in their past. It may be difficult for some people to recall all these details accurately. Furthermore, patients who have the outcome (cases) are likely to scrutinize the past, remembering details of negative exposures more clearly than controls. This is known as recall bias. Anything the researcher can do to minimize this type of bias will strengthen the study.

Analysis; Odds Ratios and Confidence Intervals

In the analysis stage, calculate the frequency of each of the measured variables in each of the two groups. As a measure of the strength of the association between an exposure and the outcome, case-control studies yield the odds ratio. An odds ratio is the ratio of the odds of an exposure in the case group to the odds of an exposure in the control group. It is important to calculate a confidence interval for each odds ratio. A confidence interval that includes 1.0 means that the association between the exposure and outcome could have been found by chance alone and that the association is not statistically significant. An odds ratio without a confidence interval is not very meaningful. These calculations are usually made with computer programmes (e.g., Epi-Info). Case-control studies cannot provide any information about the incidence or prevalence of a disease because no measurements are made in a population based sample.

Risk Factors and Sampling

Another use for case-control studies is investigating risk factors for a rare disease, such as uveal melanoma. In this example, cases might be recruited by using hospital records. Patients who present to hospital, however, may not be representative of the population who get melanoma. If, for example, women present less commonly at hospital, bias might occur in the selection of cases.

The selection of a proper control group may pose problems. A frequent source of controls is patients from the same hospital who do not have the outcome. However, hospitalised patients often do not represent the general population; they are likely to suffer health problems and they have access to the health care system. An alternative may be to enroll community controls, people from the same neighborhoods as the cases. Care must be taken with sampling to ensure that the controls represent a ‘normal’ risk profile. Sometimes researchers enroll multiple control groups . These could include a set of community controls and a set of hospital controls.

Confounders

Matching controls to cases will mitigate the effects of confounders . A confounding variable is one which is associated with the exposure and is a cause of the outcome. If exposure to toxin ‘X’ is associated with melanoma, but exposure to toxin ‘X’ is also associated with exposure to sunlight (assuming that sunlight is a risk factor for melanoma), then sunlight is a potential confounder of the association between toxin ‘X’ and melanoma.

Case-control studies may prove an association but they do not demonstrate causation. Consider a case-control study intended to establish an association between the use of traditional eye medicines (TEM) and corneal ulcers. TEM might cause corneal ulcers but it is also possible that the presence of a corneal ulcer leads some people to use TEM. The temporal relationship between the supposed cause and effect cannot be determined by a case-control study.

Be aware that the term ‘case-control study’ is frequently misused. All studies which contain ‘cases’ and ‘controls’ are not case-control studies. One may start with a group of people with a known exposure and a comparison group (‘control group’) without the exposure and follow them through time to see what outcomes result, but this does not constitute a case-control study.

Case-control studies are sometimes less valued for being retrospective. However, they can be a very efficient way of identifying an association between an exposure and an outcome. Sometimes they are the only ethical way to investigate an association. If care is taken with definitions, selection of controls, and reducing the potential for bias, case-control studies can generate valuable information.

Case-Control Studies: Advantages and Disadvantages

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A case-control study is a type of observational study commonly used to look at factors associated with diseases or outcomes. The case-control study starts with a group of cases, which are the individuals who have the outcome of interest. The researcher then tries to construct a second group of individuals called the controls, who are similar to the case individuals but do not have the outcome of interest. The researcher then looks at historical factors to identify if some exposure(s) is/are found more commonly in the cases than the controls. If the exposure is found more commonly in the cases than in the controls, the researcher can hypothesize that the exposure may be linked to the outcome of interest.

For example, a researcher may want to look at the rare cancer Kaposi's sarcoma. The researcher would find a group of individuals with Kaposi's sarcoma (the cases) and compare them to a group of patients who are similar to the cases in most ways but do not have Kaposi's sarcoma (controls). The researcher could then ask about various exposures to see if any exposure is more common in those with Kaposi's sarcoma (the cases) than those without Kaposi's sarcoma (the controls). The researcher might find that those with Kaposi's sarcoma are more likely to have HIV, and thus conclude that HIV may be a risk factor for the development of Kaposi's sarcoma.

There are many advantages to case-control studies. First, the case-control approach allows for the study of rare diseases. If a disease occurs very infrequently, one would have to follow a large group of people for a long period of time to accrue enough incident cases to study. Such use of resources may be impractical, so a case-control study can be useful for identifying current cases and evaluating historical associated factors. For example, if a disease developed in 1 in 1000 people per year (0.001/year) then in ten years one would expect about 10 cases of a disease to exist in a group of 1000 people. If the disease is much rarer, say 1 in 1,000,0000 per year (0.0000001/year) this would require either having to follow 1,000,0000 people for ten years or 1000 people for 1000 years to accrue ten total cases. As it may be impractical to follow 1,000,000 for ten years or to wait 1000 years for recruitment, a case-control study allows for a more feasible approach.

Second, the case-control study design makes it possible to look at multiple risk factors at once. In the example above about Kaposi's sarcoma, the researcher could ask both the cases and controls about exposures to HIV, asbestos, smoking, lead, sunburns, aniline dye, alcohol, herpes, human papillomavirus, or any number of possible exposures to identify those most likely associated with Kaposi's sarcoma.

Case-control studies can also be very helpful when disease outbreaks occur, and potential links and exposures need to be identified. This study mechanism can be commonly seen in food-related disease outbreaks associated with contaminated products, or when rare diseases start to increase in frequency, as has been seen with measles in recent years.

Because of these advantages, case-control studies are commonly used as one of the first studies to build evidence of an association between exposure and an event or disease.

In a case-control study, the investigator can include unequal numbers of cases with controls such as 2:1 or 4:1 to increase the power of the study.

Disadvantages and Limitations

The most commonly cited disadvantage in case-control studies is the potential for recall bias. Recall bias in a case-control study is the increased likelihood that those with the outcome will recall and report exposures compared to those without the outcome. In other words, even if both groups had exactly the same exposures, the participants in the cases group may report the exposure more often than the controls do. Recall bias may lead to concluding that there are associations between exposure and disease that do not, in fact, exist. It is due to subjects' imperfect memories of past exposures. If people with Kaposi's sarcoma are asked about exposure and history (e.g., HIV, asbestos, smoking, lead, sunburn, aniline dye, alcohol, herpes, human papillomavirus), the individuals with the disease are more likely to think harder about these exposures and recall having some of the exposures that the healthy controls.

Case-control studies, due to their typically retrospective nature, can be used to establish a correlation between exposures and outcomes, but cannot establish causation . These studies simply attempt to find correlations between past events and the current state.

When designing a case-control study, the researcher must find an appropriate control group. Ideally, the case group (those with the outcome) and the control group (those without the outcome) will have almost the same characteristics, such as age, gender, overall health status, and other factors. The two groups should have similar histories and live in similar environments. If, for example, our cases of Kaposi's sarcoma came from across the country but our controls were only chosen from a small community in northern latitudes where people rarely go outside or get sunburns, asking about sunburn may not be a valid exposure to investigate. Similarly, if all of the cases of Kaposi's sarcoma were found to come from a small community outside a battery factory with high levels of lead in the environment, then controls from across the country with minimal lead exposure would not provide an appropriate control group. The investigator must put a great deal of effort into creating a proper control group to bolster the strength of the case-control study as well as enhance their ability to find true and valid potential correlations between exposures and disease states.

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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:

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:

Map of Massachusetts with thousands of icon people overlaid. A very small percentage of them are identified as having a rare disease.

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:

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:

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:

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:

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

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:

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.

Image of the Case-Control worksheet in the Epi_Tools file

Advantages and Disadvantages of Case-Control Studies

Advantages:

Disadvantages:

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Cohort, cross sectional, and case-control studies are collectively referred to as observational studies. Often these studies are the only practicable method of studying various problems, for example, studies of aetiology, instances where a randomised controlled trial might be unethical, or if the condition to be studied is rare. Cohort studies are used to study incidence, causes, and prognosis. Because they measure events in chronological order they can be used to distinguish between cause and effect. Cross sectional studies are used to determine prevalence. They are relatively quick and easy but do not permit distinction between cause and effect. Case controlled studies compare groups retrospectively. They seek to identify possible predictors of outcome and are useful for studying rare diseases or outcomes. They are often used to generate hypotheses that can then be studied via prospective cohort or other studies.

http://dx.doi.org/10.1136/emj.20.1.54

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Cohort, cross sectional, and case-control studies are often referred to as observational studies because the investigator simply observes. No interventions are carried out by the investigator. With the recent emphasis on evidence based medicine and the formation of the Cochrane Database of randomised controlled trials, such studies have been somewhat glibly maligned. However, they remain important because many questions can be efficiently answered by these methods and sometimes they are the only methods available.

The objective of most clinical studies is to determine one of the following—prevalence, incidence, cause, prognosis, or effect of treatment; it is therefore useful to remember which type of study is most commonly associated with each objective (table 1)

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While an appropriate choice of study design is vital, it is not sufficient. The hallmark of good research is the rigor with which it is conducted. A checklist of the key points in any study irrespective of the basic design is given in box 1.

Study purpose

The aim of the study should be clearly stated.

The sample should accurately reflect the population from which it is drawn.

The source of the sample should be stated.

The sampling method should be described and the sample size should be justified.

Entry criteria and exclusions should be stated and justified.

The number of patients lost to follow up should be stated and explanations given.

Control group

The control group should be easily identifiable.

The source of the controls should be explained—are they from the same population as the sample?

Are the controls matched or randomised—to minimise bias and confounding.

Quality of measurements and outcomes

Validity—are the measurements used regarded as valid by other investigators?

Reproducibility—can the results be repeated or is there a reason to suspect they may be a “one off”?

Blinded—were the investigators or subjects aware of their subject/control allocation?

Quality control—has the methodology been rigorously adhered to?

Completeness

Compliance—did all patients comply with the study?

Drop outs—how many failed to complete the study?

Missing data—how much are unavailable and why?

Distorting influences

Extraneous treatments—other interventions that may have affected some but not all of the subjects.

Confounding factors—Are there other variables that might influence the results?

Appropriate analysis—Have appropriate statistical tests been used?

All studies should be internally valid. That is, the conclusions can be logically drawn from the results produced by an appropriate methodology. For a study to be regarded as valid it must be shown that it has indeed demonstrated what it says it has. A study that is not internally valid should not be published because the findings cannot be accepted.

The question of external validity relates to the value of the results of the study to other populations—that is, the generalisability of the results. For example, a study showing that 80% of the Swedish population has blond hair, might be used to make a sensible prediction of the incidence of blond hair in other Scandinavian countries, but would be invalid if applied to most other populations.

Every published study should contain sufficient information to allow the reader to analyse the data with reference to these key points.

In this article each of the three important observational research methods will be discussed with emphasis on their strengths and weaknesses. In so doing it should become apparent why a given study used a particular research method and which method might best answer a particular clinical problem.

COHORT STUDIES

These are the best method for determining the incidence and natural history of a condition. The studies may be prospective or retrospective and sometimes two cohorts are compared.

Prospective cohort studies

A group of people is chosen who do not have the outcome of interest (for example, myocardial infarction). The investigator then measures a variety of variables that might be relevant to the development of the condition. Over a period of time the people in the sample are observed to see whether they develop the outcome of interest (that is, myocardial infarction).

In single cohort studies those people who do not develop the outcome of interest are used as internal controls.

Where two cohorts are used, one group has been exposed to or treated with the agent of interest and the other has not, thereby acting as an external control.

Retrospective cohort studies

These use data already collected for other purposes. The methodology is the same but the study is performed posthoc. The cohort is “followed up” retrospectively. The study period may be many years but the time to complete the study is only as long as it takes to collate and analyse the data.

Advantages and disadvantages

The use of cohorts is often mandatory as a randomised controlled trial may be unethical; for example, you cannot deliberately expose people to cigarette smoke or asbestos. Thus research on risk factors relies heavily on cohort studies.

As cohort studies measure potential causes before the outcome has occurred the study can demonstrate that these “causes” preceded the outcome, thereby avoiding the debate as to which is cause and which is effect.

A further advantage is that a single study can examine various outcome variables. For example, cohort studies of smokers can simultaneously look at deaths from lung, cardiovascular, and cerebrovascular disease. This contrasts with case-control studies as they assess only one outcome variable (that is, whatever outcome the cases have entered the study with).

Cohorts permit calculation of the effect of each variable on the probability of developing the outcome of interest (relative risk). However, where a certain outcome is rare then a prospective cohort study is inefficient. For example, studying 100 A&E attenders with minor injuries for the outcome of diabetes mellitus will probably produce only one patient with the outcome of interest. The efficiency of a prospective cohort study increases as the incidence of any particular outcome increases. Thus a study of patients with a diagnosis of deliberate self harm in the 12 months after initial presentation would be efficiently studied using a cohort design.

Another problem with prospective cohort studies is the loss of some subjects to follow up. This can significantly affect the outcome. Taking incidence analysis as an example (incidence = cases/per period of time), it can be seen that the loss of a few cases will seriously affect the numerator and hence the calculated incidence. The rarer the condition the more significant this effect.

Retrospective studies are much cheaper as the data have already been collected. One advantage of such a study design is the lack of bias because the outcome of current interest was not the original reason for the data to be collected. However, because the cohort was originally constructed for another purpose it is unlikely that all the relevant information will have been rigorously collected.

Retrospective cohorts also suffer the disadvantage that people with the outcome of interest are more likely to remember certain antecedents, or exaggerate or minimise what they now consider to be risk factors (recall bias).

Where two cohorts are compared one will have been exposed to the agent of interest and one will not. The major disadvantage is the inability to control for all other factors that might differ between the two groups. These factors are known as confounding variables.

A confounding variable is independently associated with both the variable of interest and the outcome of interest. For example, lung cancer (outcome) is less common in people with asthma (variable). However, it is unlikely that asthma in itself confers any protection against lung cancer. It is more probable that the incidence of lung cancer is lower in people with asthma because fewer asthmatics smoke cigarettes (confounding variable). There are a virtually infinite number of potential confounding variables that, however unlikely, could just explain the result. In the past this has been used to suggest that there is a genetic influence that makes people want to smoke and also predisposes them to cancer.

The only way to eliminate all possibility of a confounding variable is via a prospective randomised controlled study. In this type of study each type of exposure is assigned by chance and so confounding variables should be present in equal numbers in both groups.

Finally, problems can arise as a result of bias. Bias can occur in any research and reflects the potential that the sample studied is not representative of the population it was drawn from and/or the population at large. A classic example is using employed people, as employment is itself associated with generally better health than unemployed people. Similarly people who respond to questionnaires tend to be fitter and more motivated than those who do not. People attending A&E departments should not be presumed to be representative of the population at large.

How to run a cohort study

If the data are readily available then a retrospective design is the quickest method. If high quality, reliable data are not available a prospective study will be required.

The first step is the definition of the sample group. Each subject must have the potential to develop the outcome of interest (that is, circumcised men should not be included in a cohort designed to study paraphimosis). Furthermore, the sample population must be representative of the general population if the study is primarily looking at the incidence and natural history of the condition (descriptive).

If however the aim is to analyse the relation between predictor variables and outcomes (analytical) then the sample should contain as many patients likely to develop the outcome as possible, otherwise much time and expense will be spent collecting information of little value.

Cohort studies

Cohort studies describe incidence or natural history.

They analyse predictors (risk factors) thereby enabling calculation of relative risk.

Cohort studies measure events in temporal sequence thereby distinguishing causes from effects.

Retrospective cohorts where available are cheaper and quicker.

Confounding variables are the major problem in analysing cohort studies.

Subject selection and loss to follow up is a major potential cause of bias.

Each variable studied must be accurately measured. Variables that are relatively fixed, for example, height need only be recorded once. Where change is more probable, for example, drug misuse or weight, repeated measurements will be required.

To minimise the potential for missing a confounding variable all probable relevant variables should be measured. If this is not done the study conclusions can be readily criticised. All patients entered into the study should also be followed up for the duration of the study. Losses can significantly affect the validity of the results. To minimise this as much information about the patient (name, address, telephone, GP, etc) needs to be recorded as soon as the patient is entered into the study. Regular contact should be made; it is hardly surprising if the subjects have moved or lost interest and become lost to follow up if they are only contacted at 10 year intervals!

Beware, follow up is usually easier in people who have been exposed to the agent of interest and this may lead to bias.

There are many famous examples of Cohort studies including the Framingham heart study, 2 the UK study of doctors who smoke 3 and Professor Neville Butler‘s studies on British children born in 1958. 4 A recent example of a prospective cohort study by Davey Smith et al was published in the BMJ 5 and a retrospective cohort design was used to assess the use of A&E departments by people with diabetes. 6

CROSS SECTIONAL STUDIES

These are primarily used to determine prevalence. Prevalence equals the number of cases in a population at a given point in time. All the measurements on each person are made at one point in time. Prevalence is vitally important to the clinician because it influences considerably the likelihood of any particular diagnosis and the predictive value of any investigation. For example, knowing that ascending cholangitis in children is very rare enables the clinician to look for other causes of abdominal pain in this patient population.

Cross sectional studies are also used to infer causation.

At one point in time the subjects are assessed to determine whether they were exposed to the relevant agent and whether they have the outcome of interest. Some of the subjects will not have been exposed nor have the outcome of interest. This clearly distinguishes this type of study from the other observational studies (cohort and case controlled) where reference to either exposure and/or outcome is made.

The advantage of such studies is that subjects are neither deliberately exposed, treated, or not treated and hence there are seldom ethical difficulties. Only one group is used, data are collected only once and multiple outcomes can be studied; thus this type of study is relatively cheap.

Many cross sectional studies are done using questionnaires. Alternatively each of the subjects may be interviewed. Table 2 lists the advantages and disadvantages of each.

Any study with a low response rate can be criticised because it can miss significant differences in the responders and non-responders. At its most extreme all the non-responders could be dead! Strenuous efforts must be made to maximise the numbers who do respond. The use of volunteers is also problematic because they too are unlikely to be representative of the general population. A good way to produce a valid sample would be to randomly select people from the electoral role and invite them to complete a questionnaire. In this way the response rate is known and non-responders can be identified. However, the electoral role itself is not an entirely accurate reflection of the general population. A census is another example of a cross sectional study.

Market research organisations often use cross sectional studies (for example, opinion polls). This entails a system of quotas to ensure the sample is representative of the age, sex, and social class structure of the population being studied. However, to be commercially viable they are convenience samples—only people available can be questioned. This technique is insufficiently rigorous to be used for medical research.

How to run a cross sectional study

Formulate the research question(s) and choose the sample population. Then decide what variables of the study population are relevant to the research question. A method for contacting sample subjects must be devised and then implemented. In this way the data are collected and can then be analysed

The most important advantage of cross sectional studies is that in general they are quick and cheap. As there is no follow up, less resources are required to run the study.

Cross sectional studies are the best way to determine prevalence and are useful at identifying associations that can then be more rigorously studied using a cohort study or randomised controlled study.

The most important problem with this type of study is differentiating cause and effect from simple association. For example, a study finding an association between low CD4 counts and HIV infection does not demonstrate whether HIV infection lowers CD4 levels or low CD4 levels predispose to HIV infection. Moreover, male homosexuality is associated with both but causes neither. (Another example of a confounding variable).

Often there are a number of plausible explanations. For example, if a study shows a negative relation between height and age it could be concluded that people lose height as they get older, younger generations are getting taller, or that tall people have a reduced life expectancy when compared with short people. Cross sectional studies do not provide an explanation for their findings.

Rare conditions cannot efficiently be studied using cross sectional studies because even in large samples there may be no one with the disease. In this situation it is better to study a cross sectional sample of patients who already have the disease (a case series). In this way it was found in 1983 that of 1000 patients with AIDS, 727 were homosexual or bisexual men and 236 were intrvenous drug abusers. 6 The conclusion that individuals in these two groups had a higher relative risk was inescapable. The natural history of HIV infection was then studied using cohort studies and efficacy of treatments via case controlled studies and randomised clinical trials.

An example of a cross sectional study was the prevalence study of skull fractures in children admitted to hospital in Edinburgh from 1983 to 1989. 7 Note that although the study period was seven years it was not a longitudinal or cohort study because information about each subject was recorded at a single point in time.

A questionnaire based cross sectional study explored the relation between A&E attendance and alcohol consumption in elderly persons. 9

A recent example can be found in the BMJ , in which the prevalence of serious eye disease in a London population was evaluated. 10

Cross sectional studies

Cross sectional studies are the best way to determine prevalence

Are relatively quick

Can study multiple outcomes

Do not themselves differentiate between cause and effect or the sequence of events

CASE-CONTROL STUDIES

In contrast with cohort and cross sectional studies, case-control studies are usually retrospective. People with the outcome of interest are matched with a control group who do not. Retrospectively the researcher determines which individuals were exposed to the agent or treatment or the prevalence of a variable in each of the study groups. Where the outcome is rare, case-control studies may be the only feasible approach.

As some of the subjects have been deliberately chosen because they have the disease in question case-control studies are much more cost efficient than cohort and cross sectional studies—that is, a higher percentage of cases per study.

Case-control studies determine the relative importance of a predictor variable in relation to the presence or absence of the disease. Case-control studies are retrospective and cannot therefore be used to calculate the relative risk; this a prospective cohort study. Case-control studies can however be used to calculate odds ratios, which in turn, usually approximate to the relative risk.

How to run a case-control study

Decide on the research question to be answered. Formulate an hypothesis and then decide what will be measured and how. Specify the characteristics of the study group and decide how to construct a valid control group. Then compare the “exposure” of the two groups to each variable.

When conditions are uncommon, case-control studies generate a lot of information from relatively few subjects. When there is a long latent period between an exposure and the disease, case-control studies are the only feasible option. Consider the practicalities of a cohort study or cross sectional study in the assessment of new variant CJD and possible aetiologies. With less than 300 confirmed cases a cross sectional study would need about 200 000 subjects to include one symptomatic patient. Given a postulated latency of 10 to 30 years a cohort study would require both a vast sample size and take a generation to complete.

In case-control studies comparatively few subjects are required so more resources are available for studying each. In consequence a huge number of variables can be considered. This type of study is therefore useful for generating hypotheses that can then be tested using other types of study.

This flexibility of the variables studied comes at the expense of the restricted outcomes studied. The only outcome is the presence or absence of the disease or whatever criteria was chosen to select the cases.

The major problems with case-control studies are the familiar ones of confounding variables (see above) and bias. Bias may take two major forms.

Sampling bias

The patients with the disease may be a biased sample (for example, patients referred to a teaching hospital) or the controls may be biased (for example, volunteers, different ages, sex or socioeconomic group).

Observation and recall bias

As the study assesses predictor variables retrospectively there is great potential for a biased assessment of their presence and significance by the patient or the investigator, or both.

Overcoming sampling bias

Ideally the cases studied should be a random sample of all the patients with the disease. This is not only very difficult but in many instances is impossible because many cases may not have been diagnosed or have been misdiagnosed. For example, many cases of non-insulin dependent diabetes will not have sought medical attention and therefore be undiagnosed. Conversely many psychiatric diseases may be differently labelled in different countries and even by different doctors in the same country. As a result they will be misdiagnosed for the purposes of the study. However, in reality you are often left studying a sample of those patients who it is possible to recruit. Selecting the controls is often a more difficult problem.

To enable the controls to represent the same population as the cases, one of four techniques may be used.

A convenience sample—sampled in the same way as the cases, for example, attending the same outpatient department. While this is certainly convenient it may reduce the external validity of the study.

Matching—the controls may be a matched or unmatched random sample from the unaffected population. Again the problems of controlling for unknown influences is present but if the controls are too closely matched they may not be representative of the general population. “Over matching” may cause the true difference to be underestimated.

The advantage of matching is that it allows a smaller sample size for any given effect to be statistically significant.

Using two or more control groups. If the study demonstrates a significant difference between the patients with the outcome of interest and those without, even when the latter have been sampled in a number of different ways (for example, outpatients, in patients, GP patients) then the conclusion is more robust.

Using a population based sample for both cases and controls. It is possible to take a random sample of all the patients with a particular disease from specific registers. The control group can then be constructed by selecting age and sex matched people randomly selected from the same population as the area covered by the disease register.

Overcoming observation and recall bias

Overcoming retrospective recall bias can be achieved by using data recorded, for other purposes, before the outcome had occurred and therefore before the study had started. The success of this strategy is limited by the availability and reliability of the data collected. Another technique is blinding where neither the subject nor the observer know if they are a case or control subject. Nor are they aware of the study hypothesis. In practice this is often difficult or impossible and only partial blinding is practicable. It is usually possible to blind the subjects and observers to the study hypothesis by asking spurious questions. Observers can also be easily blinded to the case or control status of the patient where the relevant observation is not of the patient themselves but a laboratory test or radiograph.

Case-control studies

Case-control studies are simple to organise

Retrospectively compare two groups

Aim to identify predictors of an outcome

Permit assessment of the influence of predictors on outcome via calculation of an odds ratio

Useful for hypothesis generation

Can only look at one outcome

Bias is an major problem

Blinding cases to their case or control status is usually impracticable as they already know that they have a disease or illness. Similarly observers can hardly be blinded to the presence of physical signs, for example, cyanosis or dyspnoea.

As a result of the problems of matching, bias and confounding, case-control studies, are often flawed. They are however useful for generating hypotheses. These hypotheses can then be tested more rigorously by other methods—randomised controlled trials or cohort studies.

Case-control studies are very common. They are particularly useful for studying infrequent events, for example, cot death, survival from out of hospital cardiac arrest, and toxicological emergencies.

A recent example was the study of atrial fibrillation in middle aged men during exercise. 11

USING DATABASES FOR RESEARCH (SECONDARY DATA)

Pre-existing databases provide an excellent and convenient source of data. There are a host of such databases and the increasing archiving of information on computers means that this is an enlarging area for obtaining data. Table 3 lists some common examples of potentially useful databases.

Such databases enable vast numbers of people to be entered into a study prospectively or retrospectively. They can be used to construct a cohort, to produce a sample for a cross sectional study, or to identify people with certain conditions or outcomes and produce a sample for a case controlled study. A recent study used census data from 11 countries to look at the relation between social class and mortality in middle aged men. 12

These type of data are ordinarily collected by people other than the researcher and independently of any specific hypothesis. The opportunity for observer bias is thus diminished. The use of previously collected data is efficient and comparatively inexpensive and moreover the data are collected in a very standardised way, permitting comparisons over time and between different countries. However, because the data are collected for other purposes it may not be ideally suited to the testing of the current hypothesis, additionally it may be incomplete. This may result in sampling bias. For example, the electoral roll depends upon registration by each individual. Many homeless, mentally ill, and chronically sick people will not be registered. Similarly the notification of certain communicable diseases is a statutory responsibility for doctors in the UK: while it is probable that most cases of cholera are reported it is highly unlikely that most cases of food poisoning are.

Causes and associations

Because observational studies are not experiments (as are randomised controlled trials) it is difficult to control many external variables. In consequence when faced with a clear and significant association between some form of illness or cause of death and some environmental influence a judgement has to be made as to whether this is a causal link or simply an association. Table 4 outlines the points to be considered when making this judgement. 13

None of these judgements can provide indisputable evidence of cause and effect, but taken together they do permit the investigator to answer the fundamental questions “is there any other way to explain the available evidence?” and is there any other more likely than cause and effect?”

Qualitative studies can produce high quality information but all such studies can be influenced by known and unknown confounding variables. Appropriate use of observational studies permits investigation of prevalence, incidence, associations, causes, and outcomes. Where there is little evidence on a subject they are cost effective ways of producing and investigating hypotheses before larger and more expensive study designs are embarked upon. In addition they are often the only realistic choice of research methodology, particularly where a randomised controlled trial would be impractical or unethical.

Cohort studies look forwards in time by following up each subject

Subjects are selected before the outcome of interest is observed

They establish the sequence of events

Numerous outcomes can be studied

They are the best way to establish the incidence of a disease

They are a good way to determine causes of diseases

The principal summary statistic of cohort studies is the relative risk ratio

If prospective, they are expensive and often take a long time for sufficient outcome events to occur to produce meaningful results

Cross sectional studies look at each subject at one point in time only

Subjects are selected without regard to the outcome of interest

Less expensive

They are the best way to determine prevalence

The principal summary statistic of cross sectional studies is the odds ratio

Weaker evidence of causality than cohort studies

Inaccurate when studying rare conditions

Case-control studies look back at what has happened to each subject

Subjects are selected specifically on the basis of the outcome of interest

Efficient (small sample sizes)

Produce odds ratios that approximate to relative risks for each variable studied

Prone to sampling bias and retrospective analysis bias

Only one outcome is studied

GLOSSARY OF TERMS

The inclusion of subjects or methods such that the results obtained are not truly representative of the population from which it is drawn

The process by which the researcher and or the subject is ignorant of which intervention or exposure has occurred.

Cochrane database

An international collaborative project collating peer reviewed prospective randomised clinical trials.

Is a component of a population identified so that one or more characteristic can be studied as it ages through time.

Confounding variable

A variable that is associated with both the exposure and outcome of interest that is not the variable being studied.

A group of people without the condition of interest, or unexposed to or not treated with the agent of interest.

False positive

A test result that suggests that the subject has a specific disease or condition when in fact the subject does not.

Is a rate and therefore is always related either explicitly or by implication to a time period. With regard to disease it can be defined as the number of new cases that develop during a specified time interval.

A period of time between exposure to an agent and the development of symptoms, signs, or other evidence of changes associated with that exposure.

The process by which each case is matched with one or more controls, which have been deliberately chosen to be as similar as the test subjects in all regards other than the variable being studied.

Observational study

A study in which no intervention is made (in contrast with an experimental study). Such studies provide estimates and examine associations of events in their natural settings without recourse to experimental intervention.

The ratio of the probability of an event occurring to the probability of non-occurrence. In a clinical setting this would be equivalent to the odds of a condition occurring in the exposed group divided by the odds of it occurring in the non-exposed group.

Is not defined by a time interval and is therefore not a rate. It may be defined as the number of cases of a disease that exist in a defined population at a specified point in time.

Randomised controlled trial

Subjects are assigned by statistically randomised methods to two or more groups. In doing so it is assumed that all variables other than the proposed intervention are evenly distributed between the groups. In this way bias is minimised.

Relative risk

This is the ratio of the probability of developing the condition if exposed to a certain variable compared with the probability if not exposed.

Response rate

The proportion of subjects who respond to either a treatment or a questionnaire.

Risk factor

A variable associated with a specific disease or outcome.

Validity—internal

The rigour with which a study has been designed and executed—that is, can the conclusion be relied upon?

Validity—external

The usefulness of the findings of a study with respect to other populations.

A value or quality that can vary between subjects and/or over time

Study design for cohort studies.

Study design for cross sectional studies

Study design for case-control studies.

Read the full text or download the PDF:

Chapter 8. Case-control and cross sectional studies

Case-control studies

Selection of cases, selection of controls, ascertainment of exposure, cross sectional studies.

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Study Designs in the Health Sciences

Case-Control Study

What is a case-control study.

“A study that compares patients who have a disease or outcome of interest (cases) with patients who do not have the disease or outcome (controls), and looks back retrospectively to compare how frequently the exposure to a risk factor is present in each group to determine the relationship between the risk factor and the disease.

Case control studies are also known as "retrospective studies" and "case-referent studies.”[1]

Why use this type of study type?

Format and features

Strengthening the Reporting of Observational Studies in Epidemiology (STROBE) Statement checklist for case-control studies [2]

References

A case-control study of readmission to the intensive care unit after cardiac surgery.

Benetis R, Sirvinskas E, Kumpaitiene B, Kinduris S.

Med Sci Monit. 2013 Feb 28; 19:148-52.

Background: The aim of this study was to identify predictors of repeated admission to the intensive care unit (ICU) of patients who underwent cardiac surgery procedures.

Material and Methods: This retrospective study analyzed 169 patients who underwent isolated coronary artery bypass grafting (CABG) between January 2009 and December 2010. The case group contained 54 patients who were readmitted to the ICU during the same hospitalization and the control group comprised 115 randomly selected patients.

Results: Logistic regression analysis revealed that independent predictors for readmission to the ICU after CABG were: older age of patients (odds ratio [OR] 1.04; CI 1.004-1.08); body mass index (BMI) >30 kg/m2 (OR 2.55; CI 1.31-4.97); EuroSCORE II >3.9% (OR 3.56; CI 1.59-7.98); non-elective surgery (OR 2.85; CI 1.37-5.95); duration of operation >4 h (OR 3.44; CI 1.54-7.69); bypass time >103 min (OR 2.5; CI 1.37-4.57); mechanical ventilation >530 min (OR 3.98; CI 1.82-8.7); and postoperative central nervous system (CNS) disorders (OR 3.95; CI 1.44-10.85). The hospital mortality of patients who were readmitted to the ICU was significantly higher compared to the patients who did not require readmission (17% vs. 3.8%, p=0.025). Conclusions: Identification of patients at risk of ICU readmission should focus on older patients, those who have higher BMI, who underwent non-elective surgery, whose operation time was more than 4 hours, and who have postoperative CNS disorders. Careful optimization of these high-risk patients and caution before discharging them from the ICU may help reduce the rate of ICU readmission, mortality, length of stay, and cost.

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