METHODS
Data source: SynPUF includes three years of freely available synthetic data from the Centers for Medicare and Medicaid Services.14 While variable associations are altered, SynPUF can illustrate applications of methods to claims data while allowing sharing of the cohort file. Note that we excluded some individuals from the base SynPUF cohort to create a more illustrative cohort (cohort creation code available upon request).
Causal questions of interest: We will be comparing effects of initiating aspirin or clopidogrel treatment within 30 days of MI (hereafter, “0-30 day”), initiating within 90 days (“0-90 day”), and initiating from 30-90 days (“30-90 day”) on 180-day risks of re-hospitalization or death in those naïve to aspirin and clopidogrel at the time of their MI.
Understanding the hypothetical interventions: While these treatment regimens are easy to articulate (“start by day 30” vs “start by day 90” vs “start from day 30 to 90”), exposure patterns underlying them are deceptively complex. This is also the case in other “representative interventions” that rely on the structure of the original data due to grace periods (i.e., windows).13, 15, 16 There are 31 days people can start treatment by day 30, 91 days by day 90, and 61 days between day 30 and 90. The hypothetical intervention underlying “start by X” regimens is making the population follow its ordinary start time distribution until X, then forcing everyone who has not started treatment by X to initiate at day X.Figure 1 illustrates how different initiation patterns within the study population can generate radically different hypothetical exposure patterns for the first 30 days of a “start by 30 days” regimen. The hypothetical intervention underlying “start between X and Y” regimens is even more complex and involves preventing anyone from initiating prior to X, allowing people to naturally initiate between X and Y, and forcing those who have yet to initiate by Y to initiate treatment on Y.
Because differences in time exposed between regimens can vary across populations, comparisons of seemingly identical regimens may represent distinct causal questions in different studies. Suppose we are examining populations A and B. In A, 50% of the population initiates on day 29 and 50% initiates on day 31. In B, 50% of the population initiates on day 0 and 50% initiates on day 90. In A, only 2 days of exposure in half the population separates “start by day 30” and “start between day 30 and 90.” In B, on the other hand, half the population is exposed for the first 90 days in “start by day 30” while none are exposed for the first 90 days in “start between day 30 and 90.” This makes information on the population’s initiation timings essential context for “start by day X” regimens unless the exposure under study has no effect on the outcome of interest.
CCW Overview: CCW studies include five essential steps:identifying the population of interest, cloning and assigning clones to regimens, censoring clones when they deviate from their assigned regimens, weighting clones to account for selection bias, and analyzing the weighted cohort.Figure 2 provides an overview of the first four steps (identifying the population, cloning, censoring, and weighting) in our example examining aspirin or clopidogrel initiation after myocardial infraction. Commented SAS and R code for these steps of the analysis, as well as the base cohort, is included in the GitHub repository.
Step 1-Identifying a study cohort: First, specify the index event, eligibility criteria, and outcome. In our example, the index event is hospital discharge with an ICD-9 diagnosis code for acute MI in the primary position. After identifying index dates, apply eligibility criteria: first, no prior codes for acute MI; second, no prior use of aspirin or clopidogrel; and third, prescription coverage during the year they experienced the MI. We should also identify the date of next hospitalization or death, whichever is earliest, as well as the date of their aspirin or clopidogrel prescription fill (if they filled one). We have now identified individuals discharged from the hospital after a MI with no history of MI, aspirin use, or clopidogrel use; followed them until subsequent hospitalization, death, or administrative censoring; and identified when (if ever) they initiated aspirin or clopidogrel after their MI.
Step 2-Cloning: Next, create copies (“clones ”) of the study cohort to assign to regimens of interest. In the example, we makethree clones and assign them to “0-30 day,” “0-90 day,” and “30-90 day” regimens. We must decide how to handle patients incompatible with a treatment regimen at baseline (e.g., patients with a prescription for aspirin on the day of hospital discharge are incompatible with the “30-90 day” regimen). When using CCW to estimate per-protocol effects of a treatment A in randomized trials that randomized patients to treatment A or placebo, there is no need to clone these individuals.17 In observational studies, however, failing to clone them can generate imbalances between the different treatment regimens (i.e., confounding).18
We can either address this imbalance by cloning them regardless and creating “time zero” censoring weights, by not cloning them into incompatible regimens and creating separate treatment weights (with weights potentially altering the target population), or by excluding individuals who are incompatible with one or more treatment regimens from all the regimens. To keep a consistent target population across our comparisons while maximizing sample size, we cloned everyone into all three regimens and gave individuals incompatible with their regimen at baseline a special “time 0 censoring” flag.
Step 3-Censoring: Next, censor the clones. Censoring clones reduces their follow-up to when they met censoring criteria, sets their outcome to 0, and assigns a censoring flag. Censoring criteria can vary across regimens but, for initiation windows, will generally occur due tostarting treatment too early or failing to start treatment by the end of the window. In the “0-30 day” regimen, for example, observations can only be censored on day 30 for not initiating treatment. In the “30-90 day” regimen, patients can be censored for initiating between day 0 and 30 (getting a censoring flag for starting early) or for failing to start on day 90 (getting a censoring flag for not starting). This results in three time-to-event data sets with one observation per individual with censored follow-up times, outcomes, and censoring flags. Note that if there are other censoring criteria researchers should consider (e.g., discontinuing or switching treatment), additional flags are necessary.
Step 4-Weighting: If there are factors are associated with both censoring and the outcome, censoring will generate selection bias .19-21 If older individuals are more likely to initiate prior to day 30 than younger individuals, for example, a disproportionate number of older individuals will remain post day 30 after censoring. To account for this, weight remaining participants by their inverse of their probability of remaining uncensored (i.e., inverse probability of censoring weights, IPCW) when censoring occurs. This typically involves creating longitudinal data sets containing information on individuals over time.
Weighting regimens with intervals including time 0: Assuming no other informative censoring, creating IPCW for regimens with windows beginning at time 0 (e.g., “0-30 day” and “0-90 day”) requires up to two observations per patient, one during the window (e.g., 0-30 days for “0-30 day”) and one starting the day the window closes (e.g., day 30+ for “0-30 day”). Patients with follow-up ending during the window (whether due to administrative censoring or outcomes) receive one observation. Patients followed for longer than the window that initiate during the window receive two observations, one covering the window and one starting the day the window closes and lasting until the end of follow-up. Patients followed for longer than the window that do not initiate within the window generate two observations: one for the window and one whose follow-up starts the day the window closes with 0 days of follow-up (to calculate weights). Importantly, time-varying covariates (e.g., age) are updated for each observation.
We then need to estimate the probability of remaining uncensored for failing to start treatment in the second observation conditional on measured covariates L (here, age, sex, and renal disease), as well as past exposure history Xhist . The uncensored second observations will receive weights equal to 1 divided by this probability, or:
\(\text{IPCW}_{i}=1/(Pr(Censor_{\text{nostart}}=0|L,X_{\text{hist}})\).
We can estimate the probability of remaining uncensored in those unexposed before the final day of the interval by using a multivariable logistic regression model. Note that all individuals who initiate treatment prior to the final day have a 100% probability of remaining uncensored on day 30 conditional on exposure history, meaning they should technically receive weights of 1 .
While it may seem intuitive to give those who initiated prior to the end of the window IPCW weights besides 1, that approach allows day 0 initiators to act as counterfactuals for people censored at day 30 and ignores when they would hypothetically have started treatment (seeAppendix 1 ). If exposure effects are time-varying or exposure has an effect at the covariates used to construct censoring weights at day 30, this will bias estimates. Unfortunately, using only those who initiate the final day of the interval may not always be feasible (in our case, there are only 5 initiators on day 30 and 4 on day 90). To address this without completely ignoring time-varying effects, we fit the model in those who initiated near the end of the interval (i.e., after day 23 or 83). As this approach will introduce some selection bias in the presence of time-varying exposure effects, the definition of “recent start” should be varied in sensitivity analyses.
Weighting regimens with intervals starting after time 0: Weighting for the “30-90 day” regimen is more complex. While creating IPCW at 90 days works identically to the “90 day” regimen, the first 30 days must be handled differently. First, address day 0 initiators by creating an IPCW model at time 0 ensuring the t0 population reflects the target population. Next, we handle those censored between day 1 and 30 for starting treatment. The simplest approach is breaking day 0-29 into one-day intervals and fitting a pooled multivariable logistic regression model with adjustment for the start of the interval (resulting in similar results to using a Cox model to identify these probabilities).22 Longer intervals help avoid computational issues in large cohorts at the cost of potential model misspecification. Interval-specific IPCW can then be combined into cumulative IPCW by multiplication.
After creating weights, we removed intervals with 0 days of follow-up from the data set, resulting in three data sets of longitudinal data on clones adherent to each regimen without selection bias from measured variables.
Step 5-Analysis of the weighted data: Analyses can be performed using any approaches suitable for use in weighted interval censored data. We used weighted Kaplan-Meier methods to estimate potential outcomes under each regimen at 180 days and calculated risk differences. The best way to obtain confidence intervals here is generally bootstrapping the base cohort and re-running cloning, censoring, and weighting steps.23
The analysis phase also includes visualizing exposure patterns underlying regimens and evaluating IPCW performance. We estimated cumulative proportions of the population exposed in each regimen, calculated standardized mean differences (SMDs) in baseline covariates between recent initiators and those censored due to a failure to initiate before and after IPCW at day 30 (in “0-30 day”) or day 90 (in “0-90 day” and “30-90 day”), and compared the total size of the recent initiators after weighting to the total size of the cohort used to calculate weights (analogous to checking the mean of stabilized weights) to check for potential positivity violations.24