Clinical Application of Epidemiology
7
Risk: From Disease to Exposure
“… take two groups presumed to be representative of persons who do and do not have the disease and determine the percentage of each group who have the characteristic…. This yields, not a true rate, but rather what is usually referred to as a relative frequency.”
—Jerome Cornfield 1952
Key Words
Latency period
Case-control study
Control
Population-based case-control study
Nested case-control study
Matching
Umbrella matching
Overmatching
Recall bias
Odds ratio
Estimated relative risk
Prevalence odds ratio
Crude odds ratio
Adjusted odds ratio
Epidemic curve
Cohort studies are a wonderfully logical and direct way of studying risk, but they have practical limitations. Most chronic diseases take a long time to develop. The latency period, the period of time between exposure to a risk factor and the expression of its pathologic effects, is measured in decades for most chronic diseases. For example, smoking precedes coronary heart disease, lung cancer, and chronic bronchitis by 20 years or more, and osteoporosis with fractures occurs in the elderly because of diet and exercise patterns throughout life. Also, relatively few people in a cohort develop the outcome of interest, even though it is necessary to measure exposure in, and to follow-up, all members of the cohort. The result is that cohort studies of risk require a lot of time and effort, not to mention money, to get an answer. The inefficiency is especially limiting for very rare diseases.
Some of these limitations can be overcome by modifications of cohort methods, such as retrospective cohort or case-cohort designs, described in the preceding chapter. This chapter describes another way of studying the relationship between a potential risk (or protective) factor and disease more efficiently: case-control studies. This approach has two main advantages over cohort studies. First, it bypasses the need to collect data on a large number of people, most of whom do not get the disease and so contribute little to the results. Second, it is faster because it is not necessary to wait from measurement of exposure until effects occur.
But efficiency and timeliness come at a cost: Managing bias is a more difficult and sometimes uncertain task in case-control studies. In addition, these studies produce an estimate of relative risk and no direct information on other measures of effect such as absolute risk, attributable risk, and population risks, all described in Chapter 6 .
Despite the drawbacks of case-control studies, the trade-off between scientific strength and feasibility is often worthwhile. Indeed, case-control studies are indispensable for studying risk for very uncommon diseases, as shown in the following example.
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TABLE 7.1 Summary of Characteristics of Cohort and Case-Control Studies |
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Example
In the 2000s, clinicians began reporting cases of an unusual form of femoral fracture in women. Bisphosphonates, drugs taken to prevent osteoporosis, were suspected because they had been introduced in the decades before and act by reducing bone remodeling. Case series reported an association between bisphosphonates and atypical fractures, but the women in these studies took other drugs and had other diseases that could also have been related to their risk of fractures. To provide a more definitive answer to whether bisphosphonates were independently associated with atypical fractures, investigators in Sweden did a case-control study (1, 2) . From the National Swedish Patient Register, they identified all 160 women aged 55 years or older with atypical femoral fractures in 2008-2010. They also identified 774 controls, women in the same registry who had had ordinary femoral fractures (to match for underlying vulnerability to fractures). Other variables that might be related to both bisphosphonate use and atypical fractures were recorded, including age, the use of bone-modifying drugs such as corticosteroids or estrogens, and diseases such as osteoporosis and previous fractures. After taking these other factors into account, women taking bisphosphonates were 29 times more likely to develop atypical fractures. The risk increased with duration of use: those who used bisphosphonates 1 to 2 years had 8 times the risk, while for patients with 4 or more years of use the relative risk increased to 126.
By adding a comparison group and accounting for other variables that might be related to bisphosphonate use and atypical fractures, the investigators were able to take the inference that bisphosphonates might be a cause of atypical fractures well beyond what was possible with case series alone.
This chapter, the third about risk, is titled “From Disease to Exposure” because case-control studies involve looking backward from disease to exposure, in contrast to cohort studies, which look forward from exposure to disease.
CASE-CONTROL STUDIES
Example
Head injuries are relatively common among alpine skiers and snowboarders. It seems plausible that helmets would prevent these injuries, but critics point out that helmets might also increase head injuries by reducing field of vision, impairing hearing, and giving athletes a false sense of security. To obtain more definitive evidence of helmets' actual effects, investigators in Norway did a case-control study ( Fig. 7.2) (3). Cases and controls were chosen from visitors to eight major Norwegian alpine ski resorts during the 2002 winter season. Cases were all 578 people with head injuries reported by the ski patrol. Controls were a sample of people waiting in line at the bottom of the main ski lift at each of the eight resorts. For both cases and controls, investigators recorded other factors that might confound the relationship between helmet use and head injury, including age, sex, nationality, type of equipment, previous ski school attendance, rented or owned equipment, and skiing ability. After taking confounders into account, helmet use was associated with a 60% reduction in risk of head injury. The study was repeated a decade later; helmet use had increased markedly, and the protective association decreased, though a 33% reduction of risk was observed for more serious head injuries (4).
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Figure 7.1. Design of case-control studies.
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Figure 7.2. A case-control study of helmet use and head injuries among skiers and snowboarders. (Summary of Sulheim S, Holme I, Ekeland A, et al. Helmet use and risk of head injuries in alpine skiers and snowboarders. JAMA 2006; 295:919-924.)
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The word control comes up in other situations, too. It is used in experimental studies to refer to people, animals, or biologic materials that have not been exposed to the study intervention. In diagnostic laboratories, “controls” refer to specimens that have a known amount of the material being tested for. As a verb, control is used to describe the process of taking into account, neutralizing, or subtracting the effects of variables that are extraneous to the main research question. Here, the term is used in the context of case-control studies to refer to people who do not have the disease or outcome under study.
DESIGN OF CASE-CONTROL STUDIES
The validity of case-control studies depends on the care with which cases and controls are selected, how well exposure is measured, and how completely potentially confounding variables are controlled.
The Source Population
The choice of cases and controls depends on the population under study. For cohort studies, the population is usually clear because the cohort is defined at the outset. For case-control studies, the source population may be difficult to pin down, and often is not explicitly identified. To avoid bias, all cases and controls present in the population at a given time would be equally available for inclusion into the study.
Selecting Cases
The cases in case-control research should be new (incident) cases, not existing (prevalent) ones. The reasons are based on the concepts discussed in Chapter 2 . The prevalence of a disease at a point in time is a function of both the incidence and duration of that disease. Duration is in turn determined by the rate at which patients leave the disease state (because of recovery or death) or persist in it (because of a slow course or successful palliation). It follows from these relationships that risk factors for prevalent disease may be risk factors for incidence, duration, or both; the relative contributions of the two cannot be determined. For example, if prevalent cases were studied, an exposure that caused a rapidly lethal form of the disease would result in fewer cases that were exposed, reducing relative risk and thereby suggesting that exposure is less harmful than it really is or even that it is protective.
At best, a case-control study should include all the cases or a representative sample of all cases that arise in a defined population within a specified time period. For example, the bisphosphonates study included all residents of Sweden from 2008 to 2010 and the helmets study included all skiers and snowboarders in eight major resorts in Norway in a winter season (accounting for 55% of all ski runs in the country).
Some case-control studies, especially older ones, have identified cases in hospitals and referral centers where uncommon diseases are most likely to be found. This way of choosing cases is convenient, but it raises validity problems. These centers may attract particularly severe or atypical cases or those with unusual exposures—the wrong sample if the underlying research question in case-control studies is about ordinary occurrences of disease and exposures.
However the cases might be identified, it should be possible for both cases and controls to be exposed to the risk factor and to experience the outcome. For example, in a case-control study of exercise and sudden death, cases and control would have to be able to exercise (if they chose to) to be eligible.
It goes without saying that diagnosis should be rigorously confirmed for cases (and excluded for controls), and the criteria made explicit. In the bisphosphonates study, investigators agreed on explicit criteria for atypical fractures of the femur and reviewed all radiographs, not just reports of them, to classify fracture type. One investigator then reviewed a random sample of radiographs for a second time without knowing how each had been classified, and there was complete agreement between the original and the second classifications.
Selecting Controls
The purpose of controls is to get an estimate of the frequency of the exposure in the source population, while accounting for other relevant risk factors. Appropriate control selection enables the investigator to determine the expected exposure frequency in cases, compared to the actual frequency observed. The best approach to making sure controls reflect the baseline exposure frequency is to ensure that controls are a random sample of all noncases in the same population or cohort that produced the cases.
The Population Approach
Studies in which cases and controls are a complete or random sample of a defined population are called population-based case-control studies. In practice, most of these populations are dynamic—that is,
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continually changing, with people moving in and out of the population—as described in Chapter 2 (5) . This might bias the result, especially if cases and controls are sampled over a long period of time and exposure is changing rapidly during this time. This concern can be laid to rest if there is evidence that population turnover is in fact so small as to have little effect on the study results or if cases and controls are matched on calendar time—that is, controls are selected on the same date as the onset of disease in the cases.
The Cohort Approach
Another way of ensuring that cases and controls are comparable is to draw them from the same cohort. In this situation, the study is said to be a nested case-control study (it is “nested” in the cohort).
In the era of large databases and powerful computers, why not just analyze cohort data as a cohort study rather than a case-control study? After all, the inefficiency of including many exposed members of the cohort, even though few of them will experience the outcome, could be overcome by computing power. The usual reason for case-control analyses of cohort data is that some of the study variables, especially some covariates, may not be available in the cohort database and, therefore, have to be gathered from other sources for each patient in the study. Obtaining the missing information from medical records, questionnaires, genetic analyses, and linkage to other databases can be very expensive and time-consuming. Therefore, there is a practical advantage to having to assemble this information only for cases and a sample of noncases in the cohort, not every member of the cohort.
Controls selected retrospectively from a cohort study can be chosen at different times during the observation period. Because a cohort study begins with a population without the disease, initially the entire initial cohort could in theory be available for control selection, although this is not commonly done; more often, controls have been selected from noncases at the end of the study period. Matching controls to the time a case develops tends to provide a better estimate of population exposure frequency, as will be discussed later in the chapter.
With nested case-control studies, there is an opportunity to obtain both crude measures of incidence from a cohort analysis and a strong estimate of relative risk, that takes into account a rich set of covariates, from a case-control analysis. With this information, one has the full set of risk described in Chapter 6 —absolute risk for exposed and nonexposed people, relative risk, attributable risk, and population risks.
The bisphosphonate example illustrates the advantages of complementary cohort and case-control analyses. A cohort analysis, taking only the age into account, showed that the increase in the absolute risk of atypical fractures related to bisphosphonate use was 11 cases per 10,000 patient-years. Collection of data on covariates was done by linking to other databases and was presumably too resource-intensive to be done on the entire national sample. With these data for cases and controls, a much more credible estimate of relative risk was possible in the case-control analysis. The estimate of relative risk of 29 from the case-control analysis was somewhat lower than the crude relative risk from the cohort analysis (not accounting for potential confounders other than age), which was 55. Because of the two analyses, both cohort and case-control, the authors could point out that the relative risk of atypical fracture was large but the absolute risk was small.
Hospital and Community Controls
If population- or cohort-based sampling is not possible, a fallback position is to select controls in such a way that the selection seems to produce controls that are representative of the population. For example, if cases are selected from a hospital ward, the controls might be selected from patients with different diseases, apparently unrelated to the exposure and disease of interest, in the same hospital. As pointed out earlier, for most risk factors and diseases, case-control studies in health care settings are more fallible than population- or cohort-based sampling because hospitalized patients are usually a biased sample of all people in the community, the people to whom the results should apply.
Another approach is to obtain controls from the community served by the hospital. However, many hospitals do not draw patients exclusively from the surrounding community; some people in the community go to other hospitals, and some people in other communities pass up their own neighborhood hospital to go to the study hospital. As a result, cases and controls may be systematically different in ways that distort the exposure-disease relationship.
Multiple Control Groups
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the otherwise dissimilar groups in the same direction and to the same extent. If the estimates of relative risks are different, it is a signal that one or more are biased and the reasons need to be investigated. It also may indicate that the source population and research question should be clarified.
Example
In the helmets and head injury example (2), the main control group was uninjured people skiing or snowboarding on the same hills on the same days, but one could imagine disadvantages to these controls, such as their not having similar risk-taking behavior to cases. To examine the effect of choice of control group on results, the investigators repeated the analyses with a different control group—skiers with other injuries. The estimated relative risk was similar—a reduction in risk of 55% rather than 60% with the original control group—suggesting that choice of control group did not substantially affect results.
Multiple Controls per Case
Having several control groups per case group should not be confused with having several controls for each case. If the number of cases is limited, as is often so with rare diseases, the study can provide more information if there is more than one control per case. More controls produce a gain in the ability to detect an increase or decrease in risk if it exists, a property of a study called “statistical power” (see Chapter 11 ). As a practical matter, the gain is worthwhile up to about three or four controls per case, after which little is gained by including even more controls.
Matching
If some characteristics seem especially strongly related to either exposure or disease, such that one would want to be sure that they occur similarly in cases and controls, they can be matched. With matching, for each case with a set of characteristics, the study includes one or more controls that possess the same characteristics. Researchers commonly match for age and sex, because these are often strongly related to both exposure and disease, but matching may extend beyond these demographic characteristics (e.g., to risk profile or disease severity) when other factors are known to be strongly associated with an exposure or outcome. Matching increases the useful information obtainable from a set of cases and controls by reducing differences between groups in determinants of disease other than the one being considered, thereby allowing a more powerful (sensitive) measure of association.
Sometimes, cases and controls are made comparable by umbrella matching, matching on a variable such as hospital or community that is a proxy for many other variables that could confound the exposure-disease relationship and would be difficult to measure one at a time, if that were possible at all. Examples of variables that might be captured under an umbrella include social disadvantage related to income, education, race, and ethnicity; propensity to seek health care or follow medical advice; and local patterns of health care.
Matching can be overdone, biasing study results. Overmatching can occur if investigators match on variables so closely related to exposure that exposure rates in cases and controls becomes more similar than they are in the population. The result is to make the observed estimate of relative risk closer to 1 (no effect). There are many reasons why the matching variable might be related to exposure. It may be part of the chain of events leading from exposure to disease. Other variables might be highly related to each other because they have similar root causes; education, income, race, and ethnicity tend to be related to each other, so if one matches on one, it will obscure effects of the others. Matching on diseases with the same treatment would result in overmatching for studies of the effects of that treatment. For example, in a study of nonsteroidal anti-inflammatory drugs (NSAIDs) and renal failure, if cases and controls were matched for the presence of arthritic symptoms, which are commonly treated with NSAIDs, matched pairs would have an artificially similar history of NSAID use.
A disadvantage of matching is that once a variable is matched for, and so made similar in cases and controls, it is no longer possible to learn how it affects the exposure-disease relationship. Also, for many studies it is not possible to find matched controls for more than a few case characteristics. This can be overcome, to some extent, if the number of potential controls is huge or if the matching criteria are relaxed (e.g., by matching age within a 5-year range rather than the same year). In summary, matching is a useful way of controlling for confounding, but it can limit the questions that can be asked in the study and can cause rather than remove bias.
Measuring Exposure
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accurate records that were collected before disease developed. Examples include pharmacy records for studies of prescription drug risks, surgical records for studies of surgical complications, and stored blood specimens for studies of risk related to biomolecular abnormalities. With such records, knowledge of disease status cannot bias reporting of exposure.
However, many important exposures can only be measured by asking cases and controls or their proxies about them. Among these are exercise, diet, over-thecounter medications, and recreational drug use.
Example
Is cannabis a risk factor for a new-onset psychotic disorder such as schizophrenia? Investigators studied 901 patients with a first-episode psychotic disorder at 11 sites in Europe and Brazil (6). Cases were identified from those who presented to mental health services with psychosis, and confirmed with a standardized and validated questionnaire; diagnoses of psychosis due to the acute effects of recreational drugs were excluded. Exposure to cannabis was measured in a questionnaire that quantified frequency, duration, and type of cannabis use. Exposure was classified as high or low potency, based on the type of cannabis reported and the concentration of THC (one of the main active ingredients) measured in the community for each type. There were 1,237 population-based controls selected from the same sites. Compared to those who never used (and adjusted for other risk factors), there was a threefold risk of a psychotic disorder among daily cannabis users. For daily users of high-potency cannabis, the risk increased to five times that of never-users.
When cases and controls are asked to recall their previous exposures, bias can occur for several reasons. Cases, knowing they have the disease under study, may be more likely to remember whether they were exposed, a problem called recall bias. For example, parents of a child with Reye syndrome (an encephalopathy) may be more likely to recall aspirin use after widespread efforts to make parents aware of an association between aspirin use and Reyes syndrome in febrile children. A man with prostate cancer might be more likely to report a prior vasectomy after stories of an association were in the news. With all the publicity surrounding the possible risks of various environmental and drug exposures, it is entirely possible that victims of disease would remember their exposures more often than people without the disease.
Investigators can limit recall bias by not telling patients the specific purpose of the study (as was done in the cannabis study). It would be unethical not to inform participants in research about the general nature of the study question, but to provide detailed information about specific questions and hypotheses could so bias the resulting information as to commit another breach of ethics—involving subjects in a flawed research project.
Physicians may be more likely to ask about an exposure and record that information in the medical record in cases than in controls if exposure is already suspected of being a cause. Thus, a physician may be more likely to record a family history of prostate cancer in a patient with prostate cancer or to record cell phone use in a patient with brain cancer. This bias should be understandable to all students of physical diagnosis. If a resident admitting a relatively young woman with deep venous thrombosis is aware of the reported association with the use of birth control pills, he or she might question the patient more intensely about birth control pill use and record this information more carefully. Protections against this kind of bias are the same as those mentioned earlier: multiple sources of information and “blinding” the data gatherers by keeping them in the dark about the specific hypothesis under study.
The existence of disease can also lead to exposure. This concern arises with drug use and mental health—in the cannabis example, it is possible that initial schizophrenic symptoms led to cannabis use before the diagnosis. Disease can also precede exposure when the exposure under study is a medical treatment. Early manifestations of the disease may lead to treatment, while the study question is just the other way around: whether treatment causes disease. If this problem is anticipated, it can be dealt with in the design of the study, as illustrated in the following example.
Example
Do beta-blocker drugs prevent first myocardial infarctions in patients being treated for hypertension? A case-control study addressed this question (7). Because angina is a major indication for the use of beta-blockers, and also a symptom of coronary disease, the investigators carefully excluded any subjects with a history that suggested angina or other manifestation of coronary heart disease. They found that patients with hypertension treated with beta-blockers had a reduced risk of nonfatal myocardial infarctions, even after those with angina or other evidence of coronary disease were carefully excluded.
All that might be said about bias in measurement of exposure can also be said of confounders. Many important covariates (e.g., smoking, diet, exercise, as well as race and ethnicity) may be poorly recorded in medical records and databases and, therefore, must be obtained by interview if they are to be included in the study at all.
Multiple Exposures
Case-control studies are an efficient means of examining a rich array of exposures: from a single, dichotomous exposure (as in the helmet study) or various doses of the same exposure (as with the bisphosphonate and cannabis studies) to the effects of multiple exposures, and exposures that are early symptoms (not risk factors) of disease.
Example
Ovarian cancer is notoriously difficult to diagnose early in its course when treatment might be more effective. Investigators in England did a case-control study of symptoms of ovarian cancer in primary care (8). Cases were 212 women over 40 years of age diagnosed with primary ovarian cancer in 39 general practices in Devon, England, 2000-2007; 1,060 controls without ovarian cancer were matched to cases by age and practice. Symptoms were abstracted from medical records for the year before diagnosis. Seven symptoms were independently associated with ovarian cancer: abdominal distension, postmenopausal bleeding, loss of appetite, increased urinary frequency, abdominal pain, rectal bleeding, and abdominal bloating. After excluding symptoms reported in the 180 days before diagnosis (to get a better estimate of “early” symptoms), three remained independently associated with ovarian cancer: abdominal distension, urinary frequency, and abdominal pain.
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Figure 7.3. A: Calculation of relative risk from a cohort study and odds ratio (estimated relative risk). B: Calculation of odds ratio from a case-control study using noncases from the end of the study. C: Calculation of odds ratio from a case-control study using population-based sampling.
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THE ODDS RATIO: AN ESTIMATE OF RELATIVE RISK
The odds ratio is calculated in case-control studies to measure the association between the exposure and outcome. It also estimates relative risk, either directly or as an approximation, depending on how controls are sampled. To show why, it is helpful to review how cohort studies estimates relative risk, and compare this to two different approaches to sampling controls in case-control studies. The ski helmet study is used for illustration.
Figure 7.3A shows how the results of a completed cohort study can be displayed, such as if the
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ski-helmet study were done as a cohort study. In a cohort study, participants are divided based on the exposure status—exposed ( A + B, e.g., helmeted skiers), and unexposed ( C + D, e.g., skiers without helmets). Cases of head injury emerged naturally over the course of the ski season, in the exposed ( A) and unexposed ( C) skiers. This provides the appropriate numerators and denominators to calculate the incidence of head injury in the exposed [ A/( A + B)] and unexposed [ C/( C + D)] members of the cohort. It would also be possible to calculate the relative risk:
Relative risk
Case-control studies derived from this larger cohort can use all the cases or sample of cases ( a and c); the controls are always a sample of noncases. What qualifies as a noncase, however, changes during the course of a cohort study. At the outset, there are no cases, and controls could be sampled from the entire study cohort. Over time, as cases arise, the pool of noncases decreases in a fixed cohort. At the end of the study, the remaining noncases are shown in the cohort table ( B and D), and controls would be sampled only from these ( b and d in Fig. 7.3B ).
However, other control sampling methods, such as a population-based sampling done throughout the course of a study ( Fig. 7.3C ), can be used to obtain controls that are representative of the exposure status in the entire population ( N0 and N1 in the cohort; n0 and n1 in the case-control sample). The ski helmet study, for example, uses a population-based sample for controls. Figure 7.3B shows a case-control study using controls that are randomly sampled from a fixed cohort at the end of the study, a random sample of exposed ( b) and unexposed ( d) noncases. Figure 7.3C shows an alternative case-control sampling scheme that approximates a population sample of exposure, with exposed controls ( n1) and unexposed controls ( n0).
Whichever control sampling approach is used, the exposed and unexposed incidence can no longer be determined from the data in a case-control study. For example, the incidence in the exposed group calculated in the cohort study, A/ A + B, would not be the same as in the case-control study, a/ a + b. In the ski helmet study, all head injury cases were counted, but only a sample of controls, so the cases in the numerator ( a) would be the same as the cohort study, but the denominator is smaller because the size of b has decreased.
Odds Ratio Calculation
The odds ratio calculated in case-control studies provides an estimate of risk that is conceptually and mathematically similar to relative risk. The odds ratio ( Fig. 7.3B ) is defined as the odds that a case is exposed divided by the odds that a control is exposed:
Which simplifies to:
where odds are the ratios of two probabilities, the probability of an event divided by 1 - the probability of that event.
The odds ratio can be further simplified to:
Referring back to Figure 7.3B , the odds ratio can be obtained by multiplying diagonally across the table and dividing these cross-products.
The meaning of the odds ratio is analogous to that of relative risk obtained from cohort studies. If the frequency of exposure is higher among cases, the odds ratio will exceed 1, indicating increased risk. The stronger the association is between the exposure and disease, the higher the odds ratio. Conversely, if the frequency of exposure is lower among cases, the odds ratio will be <1, indicating protection. Because of the similarity of the information conveyed by an odds ratio and the relative risk, and the meaning more readily attached to relative risk, odds ratios are often reported as estimated relative risks.
Odds Ratio as an Indirect Estimate of Relative Risk
When controls are sampled among noncases after all cases have occurred ( Fig. 7.3B ), an odds ratio is approximately equal to a relative risk when the incidence of disease is low. To see this mathematically, look at the formula for relative risk in Figure 7.3B. If the
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number of cases in the exposed group ( a) is small relative to the number of noncases in that group ( b) then a/( a + b) is approximately equal to a/b. Similarly, if the number of cases in the nonexposed group ( c) is small relative to noncases in that group ( d), then c/( c + d) is approximated by c/ d. Then, relative risk = a/ b divided by c/ d, which simplified to ad/ bc, the odds ratio.
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Figure 7.4. Comparison of risk calculations for the ski helmet study using a hypothetical cohort, and two methods of control selection. Note that this example demonstrates the calculation of crude odds ratios that differ from the adjusted odds ratios of 0.40. (Data from Sulheim S, Holme I, Ekeland A, et al. Helmet use and risk of head injuries in alpine skiers and snowboarders. JAMA 2006;295:919-924.)
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Odds Ratio as a Direct Estimate of Relative Risk
When controls are selected using methods that estimate the population exposure frequency, then the odds ratio is a direct estimate of the relative risk, even if the disease is common:
Relative risk of cohort:
Odds ratio of case-control:
Relative risk of cohort = Relative risk of case-control if:
In practice, the odds ratio usually approximates relative risk in case-control studies. In part this is because case-control studies are usually done with population sampling methods (5). In addition, most diseases, particularly those examined by means of case-control studies, have considerably lower rates than would be needed in the absence of population sampling methods. Understanding how case-control studies can directly estimate relative risk is nevertheless important because it highlights guiding principles in control selection, to provide an unbiased estimate of exposure frequency in the source population.
Figure 7.4 shows the ski helmet study data, using hypothetical cohort data, a hypothetical case-control study with controls selected from noncases at the end of the ski season, and the actual case-control data using population-based estimates. (The example ignores the role of chance in sampling.) When head injuries are uncommon among all skiers (the usual case), the odds ratio and relative risk are about the same, no matter which control is used.
Earlier in this chapter, we described why casecontrol studies should be about incident (new onset) cases, not prevalent ones. Nevertheless, prevalence odds ratios are sometimes calculated for prevalence studies and reported in the medical literature. The prevalence odds ratio is a measure of association but not a very informative one, not only because of difficulty distinguishing factors related to incidence versus duration but also because the rare disease assumption is less likely to be met.
CONTROLLING FOR EXTRANEOUS VARIABLES
The greatest threat to the validity of observational (cohort and case-control) studies is that the groups being compared might be systematically different in factors related to both exposure and disease—that is, there is confounding. In Chapter 6 , we described various
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ways of controlling for extraneous variables when looking for independent effects of exposure on disease in observational studies. All of these approaches—exclusion, matching, stratified analyses, and modeling—are also used in case-control studies, often in combination. Of course, this can only be done for characteristics that were already suspected to affect the exposure-disease relationship and were measured in the study.
Because mathematical modeling is almost always used to control for extraneous variables, in practice, calculations of odds ratios are much more complicated than the cross product of a two-by-two table. An odds ratio calculated directly from a 2 × 2 table is referred to as a crude odds ratio because it has not taken into account variables other than exposure and disease. After adjustment for the effects of these other variables, it is called an adjusted odds ratio. The presence of confounding does not suggest that controls were selected inappropriately, or that there is an inherent problem with the results. Controls that are representative of the source population may be quite different from cases, including the frequency of confounders; recognizing, measuring, and adjusting for confounders can produce valid results.
The implicit reason for case-control studies is to find causes. However, even when extraneous variables have been controlled for by state-of-the-science methods, the possibility remains that unmeasured variables are confounding the exposure-disease relationship. Therefore, one has to settle for describing how exposure is related to disease independently of other variables included in the study and be appropriately humble about the possibility that unmeasured variables might account for the results. For these reasons, the results of observational studies are best described as associations, not causes.
INVESTIGATION OF A DISEASE OUTBREAK
Up to this point, we have described the use of the case-control method to identify risk factors for chronic diseases. The same method is used to identify risk factors for outbreaks (small epidemics) of acute diseases, typically infectious diseases or poisonings. Often, the microbe or toxin is obvious early in the epidemic, after diagnostic evaluation of cases, but the mode of transmission is not. Information on how the disease was spread is needed to stop the epidemic and to understand possible modes of transmission, which might be useful in the control of future epidemics.
Example
A large outbreak of gastroenteritis, with many cases complicated by hemolytic-uremic syndrome (a potentially fatal condition with acute renal failure, hemolytic anemia, and thrombocytopenia) occurred in Germany in May 2011 (10). During the epidemic, there were 3,816 reported cases, 845 with hemolytic-uremic syndrome. Figure 7.5 shows the epidemic curve, the number of cases over time. The immediate cause, infection with a toxin-producing strain of the bacterium Escherichia coli was quickly identified, but the source of the infection was not. Investigators did a case-control study comparing 26 cases of hemolytic-uremic syndrome with 81 controls, matched for age and neighborhood (11). They found that 6/24 cases (25%) and 7/80 controls (9%) were exposed to sprouts, for an odds ratio of 5.8, suggesting that the infection was transmitted by eating contaminated sprouts. (Note that the odds ratio is not exactly the cross-products in this case because the calculation of odds ratio took into account the matching.) However, cucumbers and other produce were also implicated, although less strongly. To take this further, investigators did a small cohort study of people dining in groups at a single restaurant during the epidemic period. Cases were empirically defined as diners who developed bloody diarrhea or hemolytic-uremic syndrome or were found by culture to have the offending organism. Twenty percent of the cohort met these criteria, 26% of whom had hemolytic-uremic syndrome. The relative risk for sprout consumption was 14.2, and no other food was strongly associated with the disease. Sprout consumption accounted for 100% of cases. Investigators traced back the source of sprouts from the distributor that supplied the restaurant to a single producer. However, they could not culture the causal Escherichia coli from seeds in the implicated lot. Following the investigation, and after attention to the producer, the epidemic subsided ( Fig. 7.5) and incidence returned to the low levels seen before the epidemic.
This example also illustrates how case-control and cohort studies, laboratory studies of the responsible organism, and “shoe-leather” epidemiology during trace-back acted in concert to identify the underlying cause of the epidemic.