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