1 Division of Preventive Medicine, Department of Medicine, Brigham and Women's Hospital, Harvard Medical School, Boston, MA.
2 Department of Epidemiology, Johns Hopkins Bloomberg School of Public Health, Baltimore, MD.
3 Department of Medicine, Epidemiology and Public Health, University of Miami School of Medicine, Miami, FL.
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ABSTRACT |
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aspirin; bias (epidemiology); cardiovascular diseases; confounding factors (epidemiology); epidemiologic methods; mortality; myocardial infarction
Abbreviations: CABG, coronary artery bypass graft; CI, confidence interval; MI, myocardial infarction; PTCA, percutaneous transluminal coronary angioplasty; RR, rate ratio
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INTRODUCTION |
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Deliberations of the Data Monitoring Board for the trial (2) included discussion of the lower-than-expected rate of cardiovascular death in this cohort, the apparent lack of effect regarding this endpoint, and the increasing use of aspirin among those who experienced a first MI. During the trial period, striking evidence accumulated for a protective effect of aspirin in secondary prevention of cardiovascular disease (3
), and the US Food and Drug Administration had already approved its use for this purpose (4
). By December 1987, among those in the placebo group of the Physicians' Health Study who had experienced an MI, over 85 percent were subsequently treated with aspirin.
When such secondary use of aspirin occurs in both placebo and active groups, estimates derived from the usual intention-to-treat analysis may be driven to the null value. Nonfatal cardiovascular events (e.g., MI) are independent prognostic factors for cardiovascular death (A0). Additionally, they may be both predictors of subsequent aspirin use (A1) and predicted by past aspirin use (A2), as depicted in figure 1, a directed acyclic graph (5, 6
). A measured risk factor that satisfies (A1) is called a confounder and may be accounted for by correctly modeling its effect in a standard regression model, such as a Cox proportional hazards model. However, a risk factor that satisfies (A2) may be an intermediate variable and would not be adjusted for in this analysis (7
). We call a risk factor that simultaneously satisfies both (A1) and (A2) a "time-dependent confounder affected by previous treatment." In the presence of such variables, standard survival analysis methods, such as Cox regression with time-dependent covariates, may provide biased estimates of the true or "causal" total effect of observed aspirin use on cardiovascular death whether or not we control for intermediate nonfatal events. We used Robins' marginal structural model (8
10
) to control for such time-varying confounders affected by previous exposure and estimated the causal effect of aspirin on cardiovascular death among the participants in the Physicians' Health Study.
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MATERIALS AND METHODS |
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In a time-dependent Cox model, the conditional hazard of cardiovascular death at time t as a function of recent aspirin use (as opposed to randomized aspirin assignment), A(t), and baseline covariates, V, is
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To eliminate or reduce this bias from an analysis of observed exposure, we use inverse-probability-of-treatment weights (11, 13
). Let L(t) be a vector of time-dependent covariates, some of which may be time-dependent confounders as described above, with
representing covariate history. To adjust for these covariates, we weight each subject's contribution to the risk set at time t by the "stabilized" time-dependent weight
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![]() | (2) |
To adjust for censoring by mortality from other causes or by termination of the aspirin arm of the study, a similar procedure is used to estimate inverse-probability-of-censoring weights, CWi(t). These weights are multiplied by the above weights to create an overall weight for each subject in each time period, SWi(t) = AWi(t) x CWi(t).
We may then use pooled logistic regression (14), weighted by SWi(t), to estimate the discrete-time survival model in the form
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![]() | (3) |
The time-dependent weights SWi(t) induce a within-subject correlation in the final model. Therefore, we used the ROBUST SAS software system macro to obtain robust, or empirical, variance estimates (17). These robust estimates are equivalent to generalized estimating equation estimates (18
) with an independent working covariance matrix but are generated more rapidly in large data sets than the generalized estimating equation estimates provided by the SAS software program GENMOD (17
). These robust variance estimates have been found to be conservative (i.e., larger than the true variance) (11
). Therefore, we also generated an estimate of the variance of our final hazard ratio by use of a simple nonparametric bootstrap procedure, estimating both the weights and rate ratios in 100 bootstrap samples (19
).
For comparison to the estimates derived from the marginal structural models, we also estimated the effects of aspirin from standard intention-to-treat and as-treated analyses. For comparability, we used pooled logistic regression in these analyses, both with and without the usual adjustment for time-varying covariates in time-dependent models.
Physicians' Health Study data
A description of the subjects and methods, as well as results of the intention-to-treat analysis of the randomized aspirin component of the Physicians' Health Study, have been published previously (1, 20
). Briefly, beginning in 1982, a 2 x 2 factorial design was used to randomize 22,071 US male physicians to 325 mg of aspirin every other day or placebo and 50 mg of ß-carotene every other day or placebo. Eligible participants were aged 4084 years and had no history of cardiovascular disease or cancer (21
). Every 6 months for the first year, then annually, participants were sent a supply of monthly calendar packs containing the study agents, with a brief questionnaire asking about their compliance with the treatment regimen as well as occurrence of any relevant events, including potential side effects. By the end of the aspirin phase of the study in January 1988, participants had been followed for an average of 60 months (range, 4677 months), and mortality and morbidity information on the primary endpoints was virtually complete. The ß-carotene component of the trial continued to its scheduled end in December 1995. The present analysis includes follow-up through the end of the aspirin component in 1988; however, since the final aspirin report was published in 1989, any remaining information regarding events occurring prior to termination of the aspirin arm of the study has been updated.
Observed aspirin use each year was computed from the compliance information provided on the annual questionnaires. Participants were asked about their use of the white pills containing either active aspirin or placebo as well as their use of nonstudy aspirin. This information was combined to estimate average aspirin use during the previous 12 months. In these analyses, the aspirin variable was classified as use for at least 90 days per year or use of at least half the study dose. At this level, some inhibition of platelet aggregation, and possible cardiovascular protection, would still be expected.
All reported study endpoints were reviewed by an endpoints committee of physicians, and only confirmed events were used in final analyses (1). Confirmed cardiovascular mortality was the endpoint in these analyses. However, any reports of nonfatal cardiovascular events including MI, stroke, coronary artery bypass graft (CABG), percutaneous transluminal coronary angioplasty (PTCA), transient ischemic attack, and angina, and other reports of cardiovascular disease (such as artery surgery, intermittent claudication, pulmonary embolism, deep vein thrombosis, or atrial fibrillation), were considered as time-varying covariates whether confirmed later or not, since even those cardiovascular events that did not meet study criteria for confirmation could affect a participant's personal choice about using aspirin. Other predictors of aspirin use considered included randomized aspirin assignment; being unblinded to study treatment; known or suspected cardiovascular risk factors, such as age, body mass index, hypertension, family history of MI, smoking, exercise, consumption of alcohol, and use of multivitamins and vitamin E; potential side effects, including gastric symptoms and bleeding disorders, assessed as gastrointestinal bleeds, easy bruising, and other bleeds; and diagnosis of other diseases, including diabetes, cancer, chronic obstructive pulmonary disease, liver disease, and arthritis.
Reports of nonfatal events were accumulated and were carried forward over time, so that indicators, for example, of past nonfatal MI, represented ever having had the event. Other risk factors were updated periodically throughout the study, and the last available information was carried forward, including over missing questionnaires. Because exposure and covariate information was assessed on annual questionnaires only, some consideration was given to the timing of events (22). To predict aspirin use in a given year, only risk factors, side effects, and other diseases reported in prior years were included. However, because of the strong and immediate effect of nonfatal cardiovascular events on aspirin use, indicators for occurrence of such events in the current as well as prior years were included. In separate sensitivity analyses, we included only those cardiovascular events reported in prior years or used both current and prior reports for all predictors in models for aspirin use.
Pooled logistic regression analyses predicting aspirin use and censoring in each year were used to estimate the weights. For the numerator of AWi(t), models including previous aspirin use and time were used. For the denominator, all potential predictors of aspirin use described above were included in the logistic models. Lagged variables for previous aspirin use, nonfatal cardiovascular events, and possible side effects were also included. Because of strong interactions with both randomized aspirin assignment and previous use of aspirin, the probability of aspirin use was estimated separately within strata defined by these variables. We excluded the first year of observation from these analyses because of the lagging, particularly by previous aspirin use. Because 124 participants in a pilot study of the Physicians' Health Study, later randomized into the trial, received a slightly different set of questionnaires and schedule of risk factor information, these participants were excluded from current analyses. After elimination of deaths during the first year of follow-up (n = 54) and participants for whom there was no follow-up compliance information (n = 77), 21,816 participants remained for these analyses.
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RESULTS |
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Use of aspirin was strongly associated with several factors, including intermediate nonfatal cardiovascular events, cardiovascular risk factors, purported side effects of aspirin, and other diseases. Predictors of aspirin use varied by both randomized assignment and by use of aspirin in the previous time period. Among those participants in the placebo group, predictors of starting aspirin use differed from those for continuing aspirin use once started (table 2). Among those participants not using aspirin in the previous year, occurrence of nonfatal cardiovascular events was a strong predictor of the initiation of nonstudy aspirin use. Reporting an MI, CABG, PTCA, stroke, or transient ischemic attack in the current year (k) all greatly increased the probability of using aspirin during that time period, as expected. The effect of these nonfatal events on aspirin use diminished over time, as evidenced by a lower odds ratio for events occurring in prior years (k - 1). Aspirin use was increased among those with cardiovascular risk factors, including smoking and family history of MI. Aspirin use or nonuse was also predicted by occurrence of other diseases considered but not by symptoms and side effects.
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Among those participants randomized to the active aspirin group (table 3), predictors of use again differed by whether the participant had been using aspirin in the previous year (k - 1). Among those who were using their assigned aspirin (ASAk - 1 = 1), those who experienced a stroke or "other" type of cardiovascular disease, as well as those who were unblinded to the study medication, were more likely to discontinue use. In addition, those who experienced symptoms or side effects of aspirin use or who developed another serious disease were more likely to stop. Those participants who were older, who exercised more, and who never smoked were more likely to continue to use active aspirin. Among those in the active group who had previously stopped using aspirin, there were fewer predictors of restarting aspirin use. These predictors included occurrence of "other" cardiovascular disease, hypertension, family history of MI, and occurrence of easy bruising, arthritis, and headache.
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In an intention-to-treat analysis, we found no effect of randomized aspirin assignment on cardiovascular mortality in this group (RR = 1.00, 95 percent confidence interval (CI): 0.72, 1.38) (table 4), consistent with the published final results of the trial (1). This null finding remained after adjustment for intervening nonfatal events and cardiovascular risk factors using conventional time-varying covariates and also after adjustment for all predictors of aspirin use examined in tables 2 and 3. As-treated analyses of actual aspirin use led to a nonsignificant estimated 10 percent reduction in risk of cardiovascular mortality among those using aspirin (RR = 0.90, 95 percent CI: 0.65, 1.25). Adjustment for cardiovascular events and risk factors decreased the rate ratio to 0.86 (95 percent CI: 0.61, 1.22), and additional adjustment for all aspirin predictors reduced it further to 0.81 (95 percent CI: 0.57, 1.15), which remained nonsignificant.
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DISCUSSION |
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A similar problem occurs in the as-treated analysis. Since MI and other intervening nonfatal events are intermediate variables in the causal pathway to cardiovascular mortality, controlling for them by using the usual methods is not appropriate. In these data, the as-treated analysis led to a nonsignificant estimated reduction in risk of 10 percent, or 14 percent after adjustment for cardiovascular risk factors. After adjustment for all other predictors of aspirin use, the estimated reduction increased to 19 percent.
The marginal structural model attempts to adjust for intervening events by applying time-varying inverse-probability-of-treatment weights. This method weights the data to form a pseudopopulation in which these intermediate events are no longer associated with future exposure. The marginal structural model thus estimates the net or total effect of aspirin use versus nonuse including intervening pathways through nonfatal cardiovascular events. Use of this model led to an estimated 26 percent reduction in cardiovascular mortality with aspirin use, an effect larger than that estimated from either the intention-to-treat or as-treated analysis. Such an increased beneficial treatment effect often occurs in studies controlling for confounding by indication (23, 24
).
Note that the marginal structural model and the intention-to-treat analyses essentially estimate different contrasts, both of which are valid comparisons. If it were true that everyone who experienced an MI was subsequently treated with aspirin, under perfect compliance, the intention-to-treat analysis would compare cardiovascular mortality among those who use aspirin both before and after an MI with that among those who do not use aspirin until they experience an MI but then use aspirin for secondary prevention. This is also a valid clinical question, and, to the extent that MI is subsequently treated with aspirin, particularly in the placebo group, this is the question addressed by the intention-to-treat analysis. This comparison indicates little overall difference in cardiovascular mortality but, of course, a significant reduction in nonfatal MI with aspirin use. In contrast, the marginal structural model analysis attempts to answer the question of whether aspirin would be associated with cardiovascular death if intervening MI did not influence subsequent aspirin use.
The marginal structural model has limitations, however. Foremost is the fact that it makes the strong assumption of no unmeasured confounders. Estimated parameters from the marginal structural model can be used to estimate causal effects only if all relevant covariates are measured in the data and are controlled adequately in the analysis, including having appropriate and inclusive models for predicting exposure to construct the stabilized weights. Methods that do not make this assumption are available (25), but they may have less power to detect treatment effects. The marginal structural model can correctly adjust for measured time-varying confounders that are affected by exposure, which is not true of standard methods such as regression or stratification.
These types of "causal" models, particularly those using population weighting schemes, hold much potential for further analyses of both randomized trial and observational data. They have been developed to adjust for censoring and compliance by using inverse probability of censoring weights (26) as well as analyses of time-varying confounders, as presented here. Alternative procedures include G-estimation (27
, 28
) and the G-computation algorithm (29
). As the technical details and methods of fitting are developed further, these models are likely to prove very useful in data analysis and interpretation, including in secondary analyses of randomized trials. Although such models can never replace well-designed and carefully conducted randomized trials, they can serve as an adjunct method and provide additional information or elucidate mechanisms. In many situations, they can estimate effects that cannot be studied through randomization for ethical reasons. As such, models such as these may soon hold an important place in the toolbox of quantitative epidemiologic methods.
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APPENDIX |
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Compliance in year 1 was assumed to be perfect and, among those with no MI in year 1, was set to 95 percent in year 2 in each randomized group. After an MI occurred, the chance of a person using aspirin in year 2 was set to 80 percent, regardless of randomized assignment. Multiplying these probabilities in a population of 200,000 randomized persons led to the frequency distribution labeled N in appendix figure 1.
In a standard intention-to-treat analysis, the probability of MI death anytime during follow-up was 0.0049 among those randomized to placebo and 0.0025 among those randomized to aspirin, leading to an estimated rate ratio of 0.52. When nonfatal MI was ignored in an observational analysis of time-varying aspirin use, the as-treated rate ratio estimate was 0.66. This value is higher than the one in the intention-to-treat analysis, since those who experienced an MI were likely to start using aspirin but had a higher risk of MI death. After adjustment for nonfatal MI, the as-treated rate ratio became 0.50. Censoring at nonfatal MI also led to an estimate of 0.50.
Although the true rate ratio for primary and secondary prevention (conditioning on prior MI) was set to 0.5 in these data, it is not necessarily the "causal" risk ratio desired over the 2-year interval. Suppose we wanted to estimate the effect of aspirin on MI death in a randomized trial under perfect compliance, that is, if everyone stayed on his or her assigned treatment regardless of intervening nonfatal events. When the same event probabilities are applied, the frequency distribution for the various paths in this counterfactual population is also shown in appendix figure 1. No change in aspirin use would occur, and fewer paths would be followed. This "causal" risk ratio would be estimated as 0.43, lower than the conditional value of 0.5. The difference occurs because although aspirin reduces MI death in 1 year by 50 percent, it also reduces nonfatal MI, leading to additional lowering of risk in year 2.
A marginal structural model was applied to these data by using the methodology described previously. When the stabilized weights (SW) shown in appendix figure 1 were used, the estimated rate ratio was 0.44, close to the true causal risk ratio. The method reweights the population so that nonfatal MI is no longer associated with subsequent aspirin use. In the crude data for survivors assigned to aspirin, the probability of using aspirin in year 2 was 80 percent for those with a nonfatal MI in year 1 and 95 percent for those without. The corresponding probabilities for those assigned to placebo were 80 percent and 5 percent. In the counterfactual population with perfect compliance, these probabilities were 100 percent for all assigned to aspirin and 0 percent for all assigned to placebo, regardless of intervening nonfatal MI. In the reweighted population, the probability of using aspirin in year 2 was 95 percent for all those assigned to aspirin and 6 percent for those not, regardless of nonfatal MI. The marginal structural model thus reweights population frequencies to eliminate the association of MI with subsequent aspirin use.
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ACKNOWLEDGMENTS |
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The authors thank Drs. Miguel Hernán and Jamie Robins for their helpful suggestions.
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NOTES |
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REFERENCES |
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