American Journal of Epidemiology Advance Access originally published online on May 15, 2007
American Journal of Epidemiology 2007 166(3):332-339; doi:10.1093/aje/kwm069
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ORIGINAL CONTRIBUTIONS |
On the Estimation and Use of Propensity Scores in Case-Control and Case-Cohort Studies
From the Department of Biostatistics and Epidemiology and Center for Clinical Epidemiology and Biostatistics, University of Pennsylvania School of Medicine, Philadelphia, PA
Correspondence to Dr. Sean Hennessy, University of Pennsylvania School of Medicine, 803 Blockley Hall, 423 Guardian Drive, Philadelphia, PA 19104-6021 (e-mail: shenness{at}cceb.med.upenn.edu).
Received for publication February 8, 2006. Accepted for publication January 26, 2007.
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ABSTRACT |
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 TOP ABSTRACT INTRODUCTIONMATERIALS AND METHODSRESULTSDISCUSSIONReferences |
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The use of propensity scores to adjust for measured confounding factors has become increasingly popular in cohort studies. However, their use in case-control and case-cohort studies has received little attention. The authors present some theory on the estimation and use of propensity scores in case-control and case-cohort studies and present the results of simulation studies that examine whether large-sample expectations are realized in studies of typical size. The application of propensity scores is less straightforward in case-control and case-cohort studies than in cohort studies. The authors' simulations revealed two potentially important issues. First, when using several potential approaches, there is artifactual effect modification of the odds ratio by level of propensity score. The magnitude of this phenomenon decreases as the sample size increases. Second, several potential approaches produce estimated propensity scores that do not converge to the true value as sample size increases and, thus, can fail to adjust fully for measured confounding factors. However, the magnitude of residual confounding appeared modest in our simulations. Researchers considering using propensity scores in case-control or case-cohort studies should consider the potential for artifactual effect modification and their reduced ability to control for potential confounding factors.
bias (epidemiology); case-control studies; cohort studies; confounding factors (epidemiology); epidemiologic methods; models, statistical; propensity score
Abbreviations: IPTW, inverse probability of exposure (or treatment) weighting
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INTRODUCTION |
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TOPABSTRACTINTRODUCTIONMATERIALS AND METHODSRESULTSDISCUSSIONReferences |
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In observational studies, one way to increase the comparability of exposure groups with regard to measured factors is to calculate the propensity score (1) and use it as a matching or stratifying factor, as a covariate in a multivariable model, or to perform inverse probability of exposure weighting (2). The propensity score is the probability of exposure given measured baseline variables. Conditional on the true propensity score, exposure groups are comparable with regard to observed covariates. Although the "true" propensity score is generally unknown in observational studies, the estimated propensity score can be calculated as the predicted probability of exposure given measured variables.
Although propensity scores have been used occasionally in case-control studies (3–5), there has been little development of the theory for their use in this setting. We know of only one paper that discusses theory for their use in case-cohort studies (1). Therefore, we consider some theory on the use of propensity scores in case-control and case-cohort studies and report the results of simulation studies to assess the degree to which expectations based on large-sample theory are realized in studies of typical size in the absence of other methodological problems (e.g., measurement error or missing data).
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MATERIALS AND METHODS |
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Some theory on propensity scores
If X denotes the measured covariates, Y the outcome (1 = has outcome), and A the exposure (1 = exposed), then the propensity score is defined as e(X) = P(A = 1|X). Given e(X), X and A are conditionally independent, which balances measured covariates across exposure groups. The following are two other properties of propensity scores: 1) if it is sufficient to adjust for individual covariates X, then it is sufficient to adjust for the propensity scores e(X) (6); and 2) adjusting for estimated propensity scores is, somewhat counterintuitively, actually better for removing bias than adjusting for true propensity scores. This is because adjusting for the estimated propensity score removes both systematic and chance imbalances, while adjusting for the true propensity score removes only systematic imbalances (7). However, this advantage of the estimated propensity score over the true propensity score depends on having a correctly specified propensity score model.
The estimation of propensity scores is less straightforward in case-control and case-cohort studies than in cohort studies. Generally, the probability of being sampled in case-control and case-cohort studies is 100 percent for subjects who develop the outcome of interest (cases) but something less for subjects who do not. In many case-control studies, the sampling fraction is unknown.
We consider several potential approaches for estimating and applying the propensity score for case-control and case-cohort studies.
- Method A (cohort), estimating the propensity score from the entire population. In case-control and case-cohort studies, complete covariate and exposure information on the full cohort is usually unavailable, so this approach will be infeasible. Unlike methods D, E, and F described below, this method provides a consistent estimate (i.e., one that converges to the true value as the sample size increases) of the true propensity score if the model used to generate the propensity score is correctly specified, and if there are no other sources of bias. Therefore, this is included for comparison with the other methods.
- Method B (subcohort), estimating the propensity score in a group consisting of a random sample of the entire underlying population, regardless of outcome (i.e., subcohort of a case-cohort study). This method is applicable to case-cohort but not to case-control studies. Method B also provides a consistent estimate of the true propensity score if the propensity score is correctly specified.
- Method C (weighted case-control), estimating the propensity score in a group consisting of all cases plus a random sample of the noncases (i.e., cases plus controls in a case-control study), giving the noncases weights that are inversely proportional to the sampling fraction for noncases. Method C requires that the sampling fraction of controls be known, which is not true in many case-control studies. Unlike methods D, E, and F, this approach also yields consistent estimates of the true propensity score if the propensity score model is correctly specified. Inverse probability weighted estimation has a long history in the survey sampling literature (8) and has more recently been applied to weighting estimating equations (9).
- Method D (control), estimating the propensity score from the sampled noncases of a case-control study. When the outcome is rare, the covariate distribution of noncases approaches that of the entire population, so this approach would be expected to provide a propensity score that is a nearly consistent estimator of the true propensity score. Robins (10) suggested this approach in the context of marginal structural models (see below).
- Method E (unweighted case-control), estimating the propensity score from all cases plus a random sample of noncases (i.e., cases plus controls in a case-control study). This method differs from the weighted case-control method in that inverse probability weighting is not used here. This approach should give consistent estimates of the true propensity score under the null hypothesis, but not otherwise.
- Method F (modeled control), estimating the propensity score from the cases and controls using the following two-stage algorithm. First, fit a model for the probability of exposure given the covariates and the outcome. Second, for each subject, compute the predicted probability of exposure from the estimated model coefficients, treating all subjects as noncases. This conditional predicted probability of exposure is then used as the propensity score. If the model is correctly specified, this approach, like method D (control), estimates the probability of exposure among noncases and so should yield an estimated propensity score that approximates the true score when the outcome is rare. This quantity appears to be the exposure score of Miettinen (11). Like method E, this method would be expected to consistently estimate the true propensity score under the null hypothesis.
Simulation design
We conducted a series of simulations to evaluate the performance of propensity score-based estimation methods of the odds ratio in studies of typical size. In each simulation, we varied the sampling fraction of noncases (or of the subcohort for case-cohort studies) and the strength of the covariate-exposure, covariate-outcome, and exposure-outcome associations to see how each of these factors affected the estimated odds ratio.
In each simulated population, we generated 10 continuous, normally distributed covariates. In particular, if pei is the probability of exposure for individual i and if Xi = (x1i, ..., x10i) is the covariate vector for the individual, then pei was assigned according to logit(pei) = 
e + ße x Xi[1:5], where e is a parameter and ße is a parameter vector. Covariates 6:10 were generated so as to be unassociated with exposure or outcome. Thus, only five of the covariates influenced the probability of exposure (i.e., the true propensity score). If each individual's exposure level is denoted by Ai, each subject's exposure was drawn as an independent Bernoulli random variable with probability of exposure pi. Let pri denote the probability of response or having the outcome; pri is assigned according to the following formula: logit(pri) = r + ßr x Xi[1:5] + log(OR) x Ai, where r is the intercept parameter, ßr is the parameter vector in relation to the covariates, and "OR" is the odds ratio for the association between exposure and outcome. A random sample of the cohort (i.e., a subcohort) was selected by simple random sampling. For case-control analyses, the noncases in the subcohort formed the control group.
The base-case simulation had the following input parameters: size of population (nc) = 2,000; number of populations simulated (ns) = 5,000; odds ratio = 1; e = 0; ße = (0.2, ..., 0.2); r = –log(9); ßr = (0, ..., 0); and sampling fraction = 0.2. This is a scenario with no effect of the exposure and no confounding. We then varied some of these parameters and examined the effect on the geometric mean of the resultant odds ratios. An illustration of how the population odds ratio estimates vary from stratum to stratum was done first with a population size of 2,000. Thereafter, ßr was in one instance changed to (0.3, ..., 0.3) (i.e., we introduced confounding) with an exposure-outcome odds ratio of both 1 and 5. We also varied nc.
For each simulated population, we estimated propensity scores using methods A through F. We used three approaches for applying the propensity score:
- Stratification into quintiles of the propensity score with estimation of the odds ratio in each quintile and calculation of the summary odds ratio using the Mantel-Haenszel method (6, 12).
- Inclusion of the propensity score as a continuous variable in a logistic regression model.
- Inverse probability of exposure (or treatment) weighting (IPTW), using the probability that a subject received the observed exposure to derive the weight in a logistic regression model for the outcome, including no predictors of the outcome other than exposure. The weight wi is derived from the estimated propensity score following the formula: wi = Ai/pei + (1 – Ai)/(1 – pei). This weighted analysis is properly viewed as fitting a marginal structural logistic regression model (13).
For each set of simulations, we estimated the geometric mean of the estimated odds ratios. We also estimated nominal 95 percent confidence intervals and examined the empirical coverage of these intervals. We also examined odds ratios for strata defined by quintiles of the propensity score and considered how these odds ratios differed from each other. To consider further possible modification of the effect of exposure by the estimated propensity score, we also included as a predictor in the logistic regression for the outcome the product of the propensity score and exposure. To assess from a given data set whether the degree of such modification might be distorted (the reason for assessing this will become clear later), we considered a resampling approach. In this approach, we estimated not only the model for exposure but also a model for outcome given the covariates using inverse probability of sampling weights. We then generated new cohort data by using the covariate data from the observed case-control sample, using the covariate pattern of each case once and of each control 1/q times, where q is the control sampling fraction. We then regenerated the exposure and outcome using the estimated logistic regression parameters and then created a case-control sample by selecting only a proportion q of the noncases. We estimated the degree of bias in the effect modification by estimating both propensity scores and the interaction of exposure with the propensity score in the outcome model from both the whole cohort and the case-control sample; the degree of distortion was obtained by comparing these interaction terms estimated from the case-control data with that generated from the whole resampled cohort.
The goal of stratification and covariate adjustment is to estimate the causal odds ratio conditional on the propensity score. In contrast, the goal of IPTW is to estimate the causal odds ratio for the study population, not conditional on propensity score. These parameters may differ from one another because of noncollapsibility of the odds ratio over strata (14). By design, our simulations fixed the odds ratios conditional on propensity score, which, in the scenarios we report, equaled the odds ratios conditional on all covariates. However, when the true odds ratio conditional on the propensity score was not one, the unconditional causal odds ratio estimated by IPTW estimators differed from the conditional odds ratio used to generate the data. In this case, we used the geometric mean of the odds ratios estimated using method A (cohort) as the true odds ratio.
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RESULTS |
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Table 1 presents geometric means of cell counts and odds ratio estimates across quintiles of the propensity score estimated using the subcohort method. Results using the weighted case-control and control methods were similar when the true odds ratio was one (data not shown). The propensity score stratum-specific odds ratios declined monotonically with increasing propensity score stratum, although the Mantel-Haenszel summary odds ratio was 1.00.
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Figure 1 shows the odds ratio by propensity score quintile estimated by the subcohort method in a scenario in which there was no association between exposure and outcome, an association between covariates and exposure was present, and there was no association between covariates and outcome (i.e., no confounding). As with the results shown in table 1, the odds ratio declined monotonically with increasing quintile of propensity score. This relation was more marked in the smaller cohort than in the larger cohort.
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Figure 2 compares four methods in a scenario in which the odds ratio is one and confounding is absent. The stratum-specific odds ratio declined with increasing propensity score with the subcohort and control methods as well as with the weighted case-control method (data not shown). However, this decline was not evident with the cohort or unweighted case-control methods (figure 2) or the modeled control method (data not shown).
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Table 2 presents ratios of the estimated odds ratio divided by the true odds ratio under three different scenarios. In scenario 1, with a true odds ratio of 1.0 and confounding absent, the estimated odds ratios very closely approximated the true odds ratio regardless of the method of estimating or applying the propensity score. In scenario 2, with an odds ratio of 1.0 and confounding present, several of the ratios showed residual bias, although the magnitude of the bias was relatively modest. Stratification yielded more residual confounding than covariate adjustment. Among methods of estimating the propensity score, the subcohort, weighted case-control, and control methods appeared to result in the most residual confounding. In scenario 3, in which the true odds ratio was 5.0 and confounding was present, all of the methods of propensity score estimation produced residual confounding. The weighted case-control method produced estimates close to those of the cohort method for all methods of applying the propensity score. The subcohort and unweighted case-control methods produced relatively unbiased odds ratios when adjusting by subclassification or covariate adjustment, but the control and modeled control methods left substantial residual confounding. Nominal 95 percent confidence intervals included the true parameter for 92–96 percent of parameter estimates, depending on the methods and assumptions. For IPTW estimation in this scenario, the subcohort and weighted case-control methods of propensity score estimation produced nearly unbiased estimates. The unweighted case-control method and especially the control and modeled control methods had substantial bias; the control and modeled control methods produced 95 percent confidence intervals that covered the true parameter substantially less than 95 percent of the time.
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Table 3 presents results from our resampling approach to assessing the degree of bias in the interaction of the estimated propensity score (using the weighted case-control approach). In small cohort sizes, the bias estimated using resampling underestimates the bias; as the cohort size increases, the estimated bias more closely approximates the bias.
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DISCUSSION |
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TOPABSTRACTINTRODUCTIONMATERIALS AND METHODSRESULTSDISCUSSIONReferences |
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Propensity scores have become a popular approach to controlling for confounding in cohort studies. Although this approach has been used occasionally in case-control and case-cohort studies, there has been little investigation of their validity in these designs. We have identified two potentially important issues that need to be considered in this context: artifactual effect modification by the estimated propensity score and residual confounding due to bias in the estimation of the true propensity score. We will discuss each in turn.
We found that the subcohort, weighted case-control, and control methods of estimating the propensity score all produce artifactual effect modification of the odds ratio by propensity score. The magnitude of the artifactual effect modification declined as the sample size increased. Despite this induced effect modification, there was little bias in the summary odds ratios obtained using the subcohort or weighted case-control methods, regardless of the method used to combine data across strata. Some authors (15) have advocated omitting any propensity score stratum in which there is substantial imbalance between exposed and unexposed subjects. We expect that doing so in this context might introduce bias into the summary odds ratio, since the summary odds ratio might not include the full range of stratum-specific odds ratios. Investigators using one of these approaches should anticipate that any observed effect modification by propensity score may represent artifact rather than true effect modification. However, if the full range of propensity scores is used to calculate summary measures, the summary measure may remain unbiased. Further evaluation of this conclusion is needed, as is the potential effect of violation of the homogeneity assumption.
Little to no effect modification by propensity score was induced by estimating the propensity score using the unweighted case-control or the modeled control methods. We expect that this will only be true for the modeled control method if the model for exposure probability used does not include interactions between the covariates and case-control status (16).
To try to understand the source of the artifactual effect modification, one must consider the control method for propensity score estimation. When exposure does not affect the outcome, this method, like the other methods, provides a consistent estimate of the propensity score. Suppose first that the probability of exposure does not vary with covariates, as would be the case in a randomized trial. Under that circumstance, any variation in the estimated propensity score by covariates would be artifactual. In the lowest stratum of the estimated propensity score, the proportion exposed among the controls will be less than the true propensity score; however, among the cases, the proportion exposed will equal (on average) the true propensity score. Thus, the odds ratio in this stratum will tend to be greater than one. Similarly, the odds ratio in the top stratum of propensity score will tend to be less than one. When the true propensity score varies, it will still be true (in expectation) that the proportion exposed in the lowest strata of the estimated score in the controls will be less than the true propensity score, whereas the proportion exposed among cases will equal the true propensity score (which is higher in this group), leading to the same upward bias in the stratum-specific odds ratio.
The same artifactual effect modification carries over in somewhat less marked fashion to the subcohort and weighted case-control methods, which provide consistent estimates of the propensity score even when exposure affects the outcome. Here, individual control subjects are much more influential in estimating the propensity score than cases. Thus, in the lowest stratum of the estimated propensity score, the estimated propensity score in controls will be farther below the true propensity score than is the estimated propensity score in cases (on average). In contrast, in the unweighted case-control and modeled control methods, each individual case and control is equally influential in estimating the propensity score, and so no effect modification is induced.
More generally, the effect of exposure may vary across levels of the propensity score. In such settings, the true degree of modification of exposure effect by the propensity score estimated by the subcohort, weighted case-control, and control methods will be systematically distorted in case-control and case-cohort studies.
This systematic distortion of the degree of effect modification raises the question of when measures of effect conditional on a propensity score are clinically meaningful or useful. In general, examining effect modification by observable clinical characteristics will be more meaningful for decision making. These observed characteristics, unlike the propensity score, are directly observable; further, the propensity score depends on the behavior of individuals in choosing various behaviors leading to exposure or treatment and so will likely differ substantially over time and among populations. Nonetheless, examining the modification of exposure or treatment effect by the propensity score is sometimes of interest. For example, if physicians preferentially prescribe one type of drug over its alternatives in patients most likely to benefit (e.g., preferentially prescribing cyclooxygenase 2 inhibitors to patients at increased risk for gastrointestinal bleeding), one might expect that the effect of treatment is more beneficial in groups with a higher propensity score. Kurth et al. (17) provide such an analysis.
A more technical reason for examining effect modification by the propensity score is that the interpretation of summary "common" measures of effect is complicated in the presence of effect modification by the confounding variables controlled for through stratification or modeling (this is not applicable to the IPTW approach) (18). Because of the difficulty in properly assessing effect modification from case-control or case-cohort data, it will be harder to know whether summary measures of effect are appropriate. We considered one approach to assessing the degree of distortion of the modification of effects, based on a model-assisted resampling scheme. This approach will sometimes underestimate the degree of distortion and so may be more useful for identifying when such distortion is present than when absent or for correcting estimates. The systematic distortion described above is largely a small-sample phenomenon. In our simulations, the bias in estimates of the degree of effect modification decreases with increasing cohort size (all other things remaining constant). When there truly is no variation in propensity score (e.g., a randomized trial), coefficients for the interaction of the propensity score and exposure may not get smaller with increasing sample size (data not shown). However, the degree of apparent modification of effect by the propensity score quantiles is reduced with increasing sample size. This would suggest that even here the distortions we have described may have little consequence.
The second issue identified by our simulations is residual confounding due to bias in estimation of the true propensity score. The control, unweighted case-control, and modeled control methods left residual confounding when confounding was present and the true odds ratio was not equal to one. This is because when exposure has an effect, these methods did not consistently estimate the true propensity score. The magnitude of this residual confounding does not decline as sample size increases. In contrast, this residual confounding was least marked for the unweighted case-control method. For the control and modeled control methods, we expect the magnitude of this residual confounding to decline as the frequency of the outcome declines, since the amount of bias in the propensity score declines with the frequency of the outcome. Stratification into quintiles left more residual confounding than other applications of the propensity score. This was expected, since there is a limit to the amount of bias that is removed through quintile stratification (19).
In conclusion, using propensity scores in case-control research is more problematic than in cohort studies. The artifactual effect modification in studies of moderate size limits the applicability of important analytical options: exploration of effect modification and restriction of the analysis to strata of the data in which there are sufficient numbers of subjects in both exposed and unexposed groups to provide meaningful estimates of stratum-specific effects; artifactual effect modification does not appear to be a problem when regressing outcome on observed covariates and exposure. Other approaches to estimating the propensity score (e.g., unweighted estimation from the combined cases and controls) do not appear to produce this apparent effect modification. When the true odds ratio is one and the study is valid, these methods allow consistent estimates of this effect, which suggests that valid statistical tests can be constructed if one has a consistent variance estimate. However, when there is a true exposure effect, these estimators of the propensity score do not produce consistent estimates of the causal odds ratio. Thus, it may be appropriate to use these methods to test the overall null hypothesis of no effect and to test whether the apparent absence of effect holds across different strata of the propensity score.
Methods based on the propensity score methods have been extended to nondichotomous exposures. Extending methods based on IPTW is most straightforward; for categorical exposures, one can continue to use as weights the inverse of the probability of receiving one's observed exposure given covariates and estimate marginal structural models (13). For continuous exposures, one can use generalized weights (20). Methods based on stratification or covariance adjustment are also available; when exposure falls into ordered categories, one can (if appropriate) use a model for ordinal logistic regression and then adjust for the linear predictor of exposure in these models (1). For continuous exposures, one can also adjust for the expected value of exposure given covariates (21); methods have also been suggested for unordered categorical exposures (22). We expect that, in case-control and case-cohort studies, the various approaches to estimating the propensity score and using these estimates would exhibit behavior similar to the corresponding approaches for binary exposures.
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ACKNOWLEDGMENTS |
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M. M. J. and W. S. were supported by grant R01 CA-095415 from the National Cancer Institute.
The authors thank Paul Rosenbaum for useful discussions, in which he first reported the effect modification by estimated propensity score and suggested method D (unweighted case-control) as a possible alternative. The authors also thank Sander Greenland for useful discussion and suggesting method F (modeled control) and James Robins for suggestions about using simulation methods to estimate bias.
Conflict of interest: none declared.
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