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Observational Studies in Radiology

¹ Department of Radiology, Harborview Medical Center and Harborview Injury Prevention and Research Center, University of Washington, Box 359728, 325 Ninth Ave., Seattle, WA 98104.
² Department of Epidemiology, Harborview Medical Center and Harborview Injury Prevention and Research Center, University of Washington, Seattle, WA.

Received May 24, 2004; accepted after revision June 2, 2004.

Supported in part by the Agency for Healthcare Research and Quality grant K08 HS11291-02.

Series editors: Nancy Obuchowski, C. Craig Blackmore, Steven Karlik, and Caroline Reinhold.

This is the 11th in the series designed by the American College of Radiology (ACR), the Canadian Association of Radiologists, and the American Journal of Roentgenology. The series, which will ultimately comprise 22 articles, is designed to progressively educate radiologists in the methodologies of rigorous clinical research, from the most basic principles to a level of considerable sophistication. The articles are intended to complement interactive software that permits the user to work with what he or she has learned, which is available on the ACR Web site (www.acr.org).

Project coordinator: G. Scott Gazelle, Chair, ACR Commission on Research and Technology Assessment. Staff coordinator: Jonathan H. Sunshine, Senior Director for Research, ACR.

Address correspondence to C. C. Blackmore.

The objectives of this paper are to describe the commonly used observational study designs—cohort and case-control studies—and to illustrate their use in radiology research. We will also discuss the strengths and limitations of observational studies and the basics of data analysis. Comprehensive discussions of observational studies can be found in several epidemiology textbooks [1-4].

An important goal in radiology research is to estimate any causal effect of radiology interventions on patient outcome [5-7]. For example, a number of investigators have studied the effect of mammography screening on mortality due to breast cancer [8-10]. A second goal of radiology research is to provide evidence to guide selection of optimal imaging strategies. Associations between clinical factors and diseases can form the basis of clinical prediction rules that guide development of imaging strategies [11, 12]. For example, mechanism of injury, such as a high-speed motor vehicle crash, is a predictor of cervical spine fracture that can be used to select between CT or radiography to evaluate the cervical spine of trauma patients [13, 14].

The best research design for the investigation of causal relationships is the randomized clinical trial. However, clinical trials require that the investigator control which subjects receive a given treatment or exposure under study. Many circumstances exist in which it is not ethical or feasible to perform a randomized trial. For example, we cannot study the influence of cervical spine imaging on outcome in major trauma patients by randomizing which trauma patients will have their cervical spines imaged and which will not. In general, it may not be appropriate to perform a randomized trial if the exposure cannot be manipulated, if manipulation of the exposure would be unethical, if the time from exposure to outcome is very long and more immediate results are desired, or if the outcome is rare, requiring a prohibitively large and expensive randomized clinical trial. Under these circumstances, observational studies may be the best alternatives. Observational studies, including cohort and case-control studies, are hypothesis-testing analytic studies that do not require manipulation of an exposure [15].

Cohort Studies

The most intuitively understood observational study is a cohort study, in which outcomes of subjects with and without a given exposure are compared. A well-known radiology cohort study is the comparison of high- and low-osmolar contrast media by Bettmann et al. [16]. In that study, the outcomes were adverse events that could be attributed to the contrast media. Outcomes were assessed prospectively, meaning that subjects were identified at the time of exposure (use of contrast material), and then followed up to see if the outcome (adverse reaction) occurred. Bettmann et al. found that use of low-osmolar contrast material was associated with a decreased rate of all adverse reactions. Cohort studies may also be retrospective; exposed and unexposed subjects are identified retrospectively after all outcomes of interest have occurred. Both exposure and outcome are then determined from medical records or some other data source.

In cohort studies, the rate of the outcome for each of the exposure cohorts is measured directly. The groups are often compared using the risk ratio. Using notation from the 2 x 2 contingency table (Table 1), the risk ratio is computed as:

where p₁ is the probability of the outcome in subjects with the exposure and p₂ is the probability of outcome in subjects without the exposure.

The risk ratio provides an estimate of the strength of association between the exposure and outcome. Risk ratios may be greater than 1, indicating positive association between outcome and exposure, or less than 1, indicating that a given exposure is associated with a decreased risk of the outcome. Confidence intervals (CIs) for the risk ratio are described in detail elsewhere [1].

The study by Bettmann et al. [16] compared the intraarterial use of low-osmolar contrast material with intraarterial high-osmolar contrast material in diagnostic procedures. When compared with high-osmolar contrast material, low-osmolar contrast material was associated with a lower rate of adverse events, with an unadjusted risk ratio of 0.71 (95% CI, 0.67, 0.75) (Table 2) [16].

An advantage of a cohort study is that a single cohort may be used to study multiple outcomes. Bettmann et al. [16] investigated the rate of all adverse events after contrast administration. However, they were also able to investigate the rates of major reactions and minor reactions in the same patients. A disadvantage of a cohort study is that because subjects are selected on the basis of exposure; usually only a single exposure can be studied.

Case-Control Studies

In case-control studies, subjects are selected on the basis of their outcomes. Cases are those with the outcome being studied, and controls are subjects selected, often at random, from the population from which the cases arose. Exposure is then assessed for both the cases and the controls. Case-control studies may be used to study the impact of an imaging technique on patient outcome. For example, Moss et al. [8] used case-control methods to evaluate the impact of mammography screening on mortality due to breast cancer. Cases were subjects who died from breast cancer, and controls were age-matched women who survived in the Guilford and Stoke region of the United Kingdom. Women invited for breast cancer mammography screening as part of the Trial of Early Detection of Breast Cancer were considered to be exposed. Unexposed subjects were those not invited for screening. Being invited to screening was associated with decreased breast cancer-related mortality.

The analysis of case-control study data can also be illustrated using a 2 x 2 table (Table 3). However, the relevant measure of association is the odds ratio:

where p is the probability of the outcome, and p / 1 - p is the odds of the outcome. Like the risk ratio, the statistical significance of the odds ratio can be estimated using the chi-square statistic. Confidence intervals for odds ratios are described elsewhere [1].

The case-control study design has several advantages. Case-control studies are a cost-efficient research design, particularly when the outcome under study is rare. Also, in a case-control study, multiple exposures may be studied from the same data. As an example, CT rather than radiography may be the more cost-effective imaging strategy in trauma patients with a high probability of cervical spine fracture [17]. Therefore, identification of subjects at high probability of fracture can aid appropriate selection of CT versus radiography. Blackmore et al. [14] performed a case-control study to identify factors that were associated with cervical spine fractures. Cases were those with a cervical spine fracture, and controls were randomly selected trauma patients without a cervical fracture. This single set of cases and controls was then used to simultaneously assess any association between cervical spine fracture (outcome) and a host of potential predictors (exposures), including mechanism of injury, presence of associated injuries such as head injury, and clinical findings such as neurologic deficits [14].

A disadvantage of case-control studies is that they yield the odds ratio rather than the risk ratio. The risk ratio from a cohort study has a more intuitive interpretation and is generally preferred, because the risk ratio directly compares the proportion of subjects with the outcome in the exposed group with the proportion of subjects with the outcome in the unexposed group. In case-control studies, the proportion of subjects with the outcome in the exposed and unexposed groups is generally not known, so the analysis is based on the odds of the outcome. Fortunately, when the study outcome is rare in the population from which the cases and controls are drawn, the odds ratio will provide a good approximation of the risk ratio. In cohort studies, the risk ratio is [a / (a + b)] / [c / (c + d)] (Table 1). However, for rare outcomes, the contribution of the subjects with the outcome in the denominators becomes small; that is, a and c are small compared with b and d, respectively. The risk ratio becomes approximately (a / b) / (c / d). This in turn reduces to a x d / b x c, which is equal to the odds ratio derived from the case-control study (Table 3).

The relationship between the odds ratio and the risk ratio, as well as a comparison between case-control and cohort studies, is shown in the breast cancer paper by Moss et al. [8]. In that paper, the authors report on both a case-control study and a cohort study that were performed simultaneously in the same population, in order to compare the two designs. Tables 4 and 5 illustrate the 2 x 2 tables for the two study designs. The risk ratio using the cohort data was [51 / (51 + 22,647)] / [147 / (147 + 48,324)], or 0.74 (95% CI, 0.54, 1.02). The odds ratio using the case-control approach for this study was approximately the same, (51) x (678) / (312) x (147), or 0.75 (95% CI, 0.52, 1.08). Note that the number of subjects with the outcome of death due to breast cancer was the same for both studies, but the number of subjects without the outcome differed. In the case-control study, several controls were selected for each case. In the cohort study, on the other hand, all the subjects with and without the exposure were included. As a result, there are thousands of subjects in the cohort study, but only several hundred in the case-control study. Because the outcome was rare, the cohort and case-control study results were nearly identical, but many fewer subjects were required under the case-control study design.

When the outcome or disease under study is common, the odds ratio may differ substantially from the risk ratio. For example, the theoretic data presented in Tables 6 and 7 compare two studies that yield an odds ratio of 2.0 for the outcome of death in subjects who received test A compared with those who received test B. When the outcome of death was rare (Table 6), the odds ratio and the risk ratio were both about 2.0. However, when death was common, the same odds ratio of 2.0 corresponds to a risk ratio of only 1.1. Thus, for common diseases or outcomes, the odds ratio may not approximate the risk ratio.

Subject Selection

In case-control studies, bias can arise if the selection of cases and controls is affected by exposure status other than through the influence of the exposure on outcome. Similarly, selection bias can arise in cohort studies if the outcome affects the selection of the exposed or unexposed subjects. A useful approach to avoid selection bias is to define the target clinical population to which the results are expected to be applied. This population represents the ideal study population. Study subjects should be drawn from this target population when possible [4, 18, 19].

For example, a number of studies have been undertaken to define clinical risk factors for cervical spine fracture in order to help guide the care and evaluation of these patients in the emergency department. The target clinical population for these studies consisted of patients who were evaluated in the emergency department for possible cervical spine fracture. In the case-control study by Blackmore et al. [14] described earlier, case and control subjects (regardless of exposure) were selected from among those who presented to the emergency department, including patients who were discharged from the emergency department as well as those who were admitted to the hospital. Head injury was a strong risk factor for cervical spine fracture, with an odds ratio of 10.0 (95% CI, 5.2, 19.1) (p < 0.0001).

Other investigators have studied clinical predictors of cervical spine fracture but have used different subject selection criteria, with correspondingly different results [14, 20-22]. In a large cohort study by Williams et al. [22], exposed (i.e., head-injured) and unexposed (i.e., not head-injured) subjects were selected from an inpatient trauma registry. The rate of cervical spine fracture was similar in both groups (risk ratio = 1.1; 95% CI, 0.93, 1.3), suggesting no association between head injury and cervical spine fracture, and conflicting with the results from the study by Blackmore et al. [14].

The different results from these studies can be understood by applying both subject selection strategies to the case-control study data from the study by Blackmore et al. (Tables 8 and 9) [14]. When the controls for this study were selected from all emergency department trauma patients (the clinically relevant target population), the results revealed a strong association between head injury and cervical spine fracture (Table 8). Another approach would have been to select the subjects only from those admitted to the hospital (Table 9). However, admitted subjects had a much greater proportion of head injuries than did the group consisting of all emergency department subjects. This difference was expected, because patients with head injury were almost always admitted, whereas those without head injury were more likely to be discharged from the emergency department. However, the increased proportion of head-injured control subjects in the inpatient study led to an odds ratio of only 1.4 for cervical spine fracture among subjects with head injury when compared with those without head injury. The exposure, head injury, affected whether subjects were admitted and therefore affected whether subjects would be eligible for the study—leading to selection bias when only admitted patients were considered. Thus, to study predictors of cervical spine fracture in emergency department patients, it is most appropriate to select subjects from the target population, emergency department patients.

Confounding

In randomized clinical trials, the randomization process helps to ensure that, on average, the study groups are alike with respect to all known and unknown confounders [23]. In observational studies, on the other hand, confounding can occur if the groups being compared differ with respect to some factor that is associated with the outcome. For example, in the study of contrast agents by Bettmann et al. [16], subjects with a history of reaction to contrast material were more likely to receive low-osmolar contrast material than were subjects without a history of contrast reaction. Furthermore, those with a history of contrast reaction were more likely to have a new adverse reaction than were those without a history of reaction. Therefore, the group that received low-osmolar contrast material included more persons with a propensity to have a reaction than did the high-osmolar contrast group. Failure to account for history of reaction would bias the risk ratio estimate for adverse outcomes. Thus, a history of contrast reactions confounded the relationship between the type of contrast material and the outcome [16].

Several strategies may mitigate the bias induced by confounding variables. The first is to restrict the study to those subjects with only one level of the potential confounder. In this case, that could mean restricting the study to subjects without a history of contrast reactions. A second strategy is to stratify subjects on the basis of the confounder, create an estimate within each stratum, and then combine results across strata. For the contrast media example used by Bettmann et al. [16], separate analyses could be done for subjects with and without a history of previous contrast reaction. The relative risk estimates for the two strata could then be combined using Mantel-Haenszel techniques described later in this article [24]. Such stratification may be effective for a small number of potential confounders but can become impractical when multiple potential confounders must be considered. A third strategy is to adjust for potential confounders using regression methods. In the results reported for the study by Bettmann et al. [16], adjustment was made for potentially confounding variables in a regression model. The results showed that low-osmolar contrast material was associated with fewer reactions than high-osmolar contrast material was, after accounting for the effects of previous contrast reaction, asthma, steroid pretreatment, race, sex, and other potential confounders [16].

Finally, matching may be used to control for a potentially confounding variable. Matching in a cohort study involves selecting unexposed subjects who have equivalent values of a confounding variable as the exposed subjects. For the contrast media example, a matched cohort study could be designed whereby an unexposed (high-osmolar contrast material) subject was selected who had a history of contrast reaction for each exposed (low-osmolar contrast material) subject who had a previous contrast reaction, and an unexposed subject without contrast reaction selected for each exposed subject without a previous contrast reaction. This matching would control for potential confounding by past reaction to contrast material. Matching can also be used in case-control studies. However, if controls in a case-control study are selected on the basis of the presence of a potential confounder, then the frequency of the potential confounder will no longer be equal in the study controls and the underlying population. Matching in case-control studies can actually introduce bias unless it is accounted for in the analysis using stratification or regression.

Matching has several disadvantages. First, it is not possible to study the effects of the variable that was used for matching. Second, matching can be expensive and difficult. Third, matching may decrease the power of a study if some cases cannot be matched to appropriate controls. In general, matching should be used sparingly, or not at all.

Analysis

The basic analysis for an observational study of a binary exposure and binary outcome can be expressed in 2 x 2 tables. Measures of association—the relative risk for cohort studies and the odds ratio for case-control studies—are derived from the 2 x 2 table as described earlier. However, the 2 x 2 table allows consideration of only a single binary exposure and single binary outcome. Confounding variables may complicate the relationship between exposure and outcome.

The Mantel-Haenszel method allows consideration of one or more potentially confounding variables in assessment of the 2 x 2 table. Separate 2 x 2 tables are constructed for each level of the potentially confounding variable. The numerators and denominators for the odds ratios derived from each 2 x 2 table are then weighted on the basis of the total number of subjects in each and combined. The calculation of the Mantel-Haenszel odds ratio for a case-control study and a calculation of a Mantel-Haenszel version of the risk ratio for cohort study data are provided in Appendix 1 [2, 24]. Methods for determining variance estimates and confidence intervals for the Mantel-Haenszel estimators are explained in detail in standard epidemiology texts [1, 2].

As an example, from the contrast study by Bettmann et al. [16], it is possible to use the Mantel-Haenszel risk ratio to account for any effect of previous contrast reaction on determination of the association between low-osmolar contrast media and any adverse reaction. Separate 2 x 2 tables for subjects with and without previous contrast reactions are shown in Tables 10 and 11. These tables are combined using the Mantel-Haenszel method to yield a Mantel-Haenszel risk ratio of 0.69, slightly lower than the crude estimate of risk ratio = 0.71.

Analyses involving multiple confounders, and analyses involving multiple exposures or outcomes, may be analyzed using regression techniques. Regression allows estimation of the odds ratio or risk ratio associated with a given variable after accounting for the effects of all other variables in the model [25, 26]. Logistic regression and other regression techniques will be discussed in future articles in this series.

Conclusion

Case-control and cohort study designs are valuable alternatives to randomized clinical trials. These study designs are particularly useful in determining the influence of a radiology intervention on patient outcome, and in determining clinical risk factors for disease, in order to aid determination of optimal imaging strategies. However, radiologists should be aware of the uses, limitations, and techniques of observational study designs.

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