 Methodology
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Intervalcohort designs and bias in the estimation of perprotocol effects: a simulation study
Trials volume 20, Article number: 552 (2019)
Abstract
Background
Randomized trials are considered the gold standard for making inferences about the causal effects of treatments. However, when protocol deviations occur, the baseline randomization of the trial is no longer sufficient to ensure unbiased estimation of the perprotocol effect: postrandomization, timevarying confounders must be sufficiently measured and adjusted for in the analysis. Given the historical emphasis on intentiontotreat effects in randomized trials, measurement of postrandomization confounders is typically infrequent. This may induce bias in estimates of the perprotocol effect, even using methods such as inverse probability weighting, which appropriately account for timevarying confounders affected by past treatment.
Methods/design
In order to concretely illustrate the potential magnitude of bias due to infrequent measurement of timevarying covariates, we simulated data from a very large trial with a survival outcome and timevarying confounding affected by past treatment. We generated the data such that the true underlying perprotocol effect is null and under varying degrees of confounding (strong, moderate, weak). In the simulated data, we estimated perprotocol survival curves and associated contrasts using inverse probability weighting under monthly measurement of the timevarying covariates (which constituted complete measurement in our simulation), yearly measurement, as well as 3 and 6month intervals.
Results
Using inverse probability weighting, we were able to recover the true null under the complete measurement scenario no matter the strength of confounding. Under yearly measurement intervals, the estimate of the perprotocol effect diverged from the null; inverse probability weighted estimates of the perprotocol 5year risk ratio based on yearly measurement were 1.19, 1.12, and 1.03 under strong, moderate, and weak confounding, respectively. Bias decreased with measurement interval length. Under all scenarios, inverse probability weighted estimators were considerably less biased than a naive estimator that ignored timevarying confounding completely.
Conclusions
Bias that arises from interval measurement designs highlights the need for planning in the design of randomized trials for collection of timevarying covariate data. This may come from more frequent inperson measurement or external sources (e.g., electronic medical record data). Such planning will provide improved estimates of the perprotocol effect through the use of methods that appropriately adjust for timevarying confounders.
Background
In randomized trials, the perprotocol effect is the effect that would have been estimated if all participants had adhered to their randomly assigned treatment strategies during the entire followup [1]. However, because adherence to the assigned treatment strategy is not in itself randomized, a naive comparison that excludes trial participants who fail to adhere to their assigned strategies will generally be biased [2].
For example, in a trial of a new treatment versus standard of care to treat coronary heart disease, adherers to the treatment may be individuals who also tend to take antihypertensive treatment. Thus, a lower rate of disease among adherers may simply reflect their higher uptake of antihypertensives rather than a benefit of the treatment under study. Therefore, analyses that attempt to estimate the perprotocol effect typically need to adjust for prognostic factors that, like antihypertensive use in our example, are also associated with adherence. That is, perprotocol analyses are observational analyses of the randomized trial data and therefore need to adjust for confounders.
In randomized trials of point interventions that are administered shortly after randomization (e.g., a onedose vaccination, a onetime screening test), adherence to the assigned intervention is fully determined at baseline and therefore can only be affected by baseline factors. The implication is that perprotocol analyses of point interventions only need to adjust for baseline confounders. On the other hand, in randomized trials of treatment strategies that are sustained during the followup (e.g., treatment for coronary heart disease, antiretroviral treatment for HIVpositive patients), adherence to the treatment strategy must also be sustained during the followup. The implication of this potentially timevarying adherence is that perprotocol analyses of sustained strategies need to adjust for timevarying confounders — timevarying prognostic factors that affect treatment decisions — as well as for baseline confounders — baseline prognostic factors that affect treatment decisions [3–6]. For example, in a randomized trial to estimate the effect of two antiretroviral therapies on mortality, an increased alcohol intake during the followup is a timevarying confounder because it affects both the risk of death and of nonadherence to the assigned treatment.
It follows that valid estimation of the perprotocol effect of sustained treatment strategies requires adequate data collection of treatment and confounders after randomization. Many randomized trials collect such postrandomization data, but most only do so at prespecified intervals (e.g., every 12 months). Because nonadherence may occur at any time during the followup, the confounders measured at the prespecified times may not be sufficient or relevant to adjust for nonadherence that took place at an unknown time between the prespecified measurement times.
In this paper, we review the impact of interval measurement on the estimation of perprotocol effects in randomized trials [7]. We conduct a simulation study to illustrate the potential magnitude of bias, even using causal inference methods for longitudinal settings such as inverse probability (IP) weighting [8], which appropriately account for timevarying confounders affected by past treatment.
Methods
Simulation design
We simulated data from a hypothetical randomized trial to quantify the effect of a new drug treatment compared to the standard of care on 5year mortality risk.
Each individual is assigned to either the new drug treatment (Z=1) or to standard of care (Z=0) and followed until death or the administrative end of the study (60 months postrandomization), whichever comes first. We assume the exact month of death is known, as is common when studies link their data with death registries. For simplicity and without loss of generality, no individual is lost to followup.
Define t=0,…,60 as an index of followup month with t=0 the month of randomization (baseline). Let Y_{t} be an indicator of death by month t with Y_{0}≡0 for all individuals (all participants are alive and therefore at risk of the outcome at baseline) and A_{t} an indicator of whether the new drug treatment is taken in month t. An individual deviated from the protocol in the first month t in which A_{t}≠Z. In our simulated study approximately 40% of individuals in both arms deviated from the protocol at some point during the followup. Figure 1 shows the cumulative proportion of protocol deviations over the study period by treatment arm.
In randomized trials, treatment A_{t} will typically depend on both baseline (e.g., sex, race, baseline age) and postbaseline (e.g., lab measurements, concomitant medications) risk factors for the outcome (e.g., death). Let L_{t}=(L_{1t},L_{2t}) be a vector of such risk factors in month t, with L_{1t} a lab measurement (continuous) and L_{2t} the use of a concomitant medication (binary).
The causal diagram in Fig. 2 outlines the datagenerating process of our simulated study. The node U represents a vector of baseline unmeasured outcome risk factors that also may affect L_{t} (e.g., genetic factors) with no direct effect on treatment at any time (as depicted by the absence of an arrow from U into A_{t−1} or A_{t} in Fig. 2). As expected in many realistic settings, the timevarying covariates L_{t} also may be affected by past treatment adherence (as depicted by the arrow from A_{t−1} to L_{t} in Fig. 2). For example, adherence to the standard versus the new treatment may affect values of future lab measurements.
We generated the data such that 100,000 individuals are assigned to each arm. We quantified bias for a given approach by the difference between the effect estimate obtained by that approach in this very large sample and the true effect value. Had we used a smaller sample size (e.g., 100 individuals assigned to each arm), random variability could explain some differences between effect estimates and the true values of the effect (unless we had used the average over a large number of small samples, which is nearly equivalent to generating a single very large sample — this is illustrated in Additional file 2).
We generated the data such that both the causal effect of treatment A_{t} for all t and the direct effect of randomization (Z) not mediated through treatment are null, as shown in Fig. 2 by the absence of any causal paths (paths consisting of arrows going in the same direction) connecting Z, A_{t−1}, or A_{t} with the future outcome (Y_{t+1}). Therefore, both the intentiontotreat effect and the perprotocol effect are null.
Datagenerating models
We generated longitudinal data according to the following models for each subject i=1,…,200,000 (i=1,…,100,000 assigned Z_{i}=1 and i=100,001…,200,000 assigned Z_{i}=0): U_{i} was generated from a uniform distribution between 0 and 1. Then the following were generated for each month t=0 until t=59 or until Y_{t+1i}=1 was generated, whichever came first:

L_{1ti} was generated from a normal distribution such that \( L_{1ti}=6U_{i}A_{t1i}\text {cumavg}(\overline {A}_{t2i})+0.25\text {cumavg}(\overline {L}_{1t1i})+0.01t+\epsilon _{i}\) with ε_{i}∼N(0,σ=2), \(\text {cumavg}(\overline {A}_{t2i})\) is the cumulative average of (A_{0i},…,A_{t−2i}), and \(\text {cumavg}(\overline {L}_{1t1i})\) is the cumulative average of (L_{10i},…,L_{1t−1i}).

L_{2ti} was generated from a Bernoulli distribution with mean p_{L2i}, equal to the probability that L_{2t}=1 given individual i ’s treatment and covariate history and survival to t, defined such that \(\text {logit} (p_{L2i})=5+3U_{i}+1.25\text {cumavg}(\overline {L} _{1ti})+0.5L_{2t1i}+0.25A_{t1i}+0.25\text {cumavg}(\overline {A} _{t2i})+0.01t\).

For any individual i deviating from the protocol by t−1 (i.e., A_{t−1i}≠Z_{i}), we set A_{ti}=A_{t−1i} (once an individual stops complying we assume they stay noncompliant). Alternatively, for any individual i complying with the protocol through t−1 (i.e., all A_{ji}=Z_{i} for j<t), A_{ti} was generated from a Bernoulli distribution with mean p_{Ai}, equal to the probability that A_{t}=1 given individual i’s treatment and covariate history and survival to t, such that
$$ {}\text{logit}(p_{Ai})=\alpha_{0}+0.4\text{cumavg}(\overline{L} _{1ti})+0.35L_{2t1i}. $$(1)For individuals assigned Z_{i}=1 (active treatment), we set α_{0}=4.0. For individuals assigned Z_{i}=0 (standard of care), we set α_{0}=−6.5.

The death indicator Y_{t+1i} was generated from a Bernoulli distribution with mean p_{Yi}, equal to the probability that Y_{t+1}=1 given individual i’s treatment and covariate history and survival to t, such that
$$ \text{logit}(p_{Yi})=\theta_{0}+\theta_{1}U_{i}. $$(2)
We considered three versions of this datagenerating mechanism, varying the values of θ_{0} and θ_{1} in the model (2). As we explain in the section Defining and estimating the perprotocol effect, given our datagenerating models, the magnitude of θ_{1} determines the magnitude of timevarying confounding (and θ_{0} the baseline event rate). We considered the following variations: “strong confounding” θ_{1}=8(θ_{0}=−11), “moderate confounding” θ_{1}=3(θ_{0}=−7), and “weak confounding” θ_{1}=0.5(θ_{0}=−6). We also considered three variations of the “strong confounding” scenario under different choices of α_{0} in model (1) that reduced the chance of deviating from the protocol in both arms. Table 1 displays the cumulative proportion of protocol deviations by the end of the study period by treatment arm resulting from different choices of α_{0}.
R code implementing this simulation design is provided in Additional file 1.
Defining and estimating the intentiontotreat effect
We can define the intentiontotreat effect for any followup month t+1=1,…,60 as a contrast of the cumulative risks in arm Z=1, Pr[Y_{t+1}=1Z=1] versus in arm Z=0, Pr[Y_{t+1}=1Z=0]. Our data generation, under all scenarios, is consistent with no confounding for the effect of Z on survival, as illustrated in Fig. 2 by the absence of any open backdoor paths (open paths consisting of arrows going in different directions and, therefore, noncausal paths) [9] connecting the treatment arm indicator Z and the future outcome Y_{t+1}. As a result, and because of the absence of loss to followup, a simple comparison of the estimated risks (i.e., cumulative incidences) in arm Z=1 versus arm Z=0 is an unbiased estimator of the intentiontotreat effect Pr[Y_{t+1}=1Z=1] versus Pr[Y_{t+1}=1Z=0] at any postrandomization time t+1=1,…,60.
We are able to recover the true intentiontotreat effect in our study, regardless of the presence of protocol deviations, because unbiased estimation of the intentiontotreat effect only relies on the random assignment of Z and no loss to followup. In contrast, unbiased estimation of the perprotocol effect requires additional assumptions.
Defining and estimating the perprotocol effect
Let \(Y_{t+1}^{\overline {a}=\overline {1}}\) denote an individual’s indicator of death by month t+1, had she, possibly contrary to fact, continuously followed the protocol in arm Z=1. Similarly, let \(Y_{t+1}^{\overline {a}= \overline {0}}\) denote this outcome by month t+1, had she, instead, continuously followed the protocol in arm Z=0. We can then formally define the perprotocol effect at month t+1 as a contrast of the counterfactual risks:
Note that, because Z was randomly assigned, we could alternatively define the perprotocol contrast as \(\Pr \left [Y_{t+1}^{\overline {a}=\overline {1}}=1\right ] \text {versus} \Pr \left [Y_{t+1}^{\overline {a}=\overline {0}}=1\right ]\) (unconditional on Z). Many randomized trials include a “naive” perprotocol analysis in which the survival curves are estimated after censoring participants at the time that they deviate from the protocol. This “naive” approach generally fails to recover the true perprotocol effect because it fails to account for confounding for the effect of received treatment due to risk factors that affect both future adherence and survival. In Fig. 2, such confounding is represented by open backdoor paths connecting A_{t−1} and A_{t} to Y_{t+1}, e.g., the path A_{t}←L_{t}←U→Y_{t+1}. The datagenerating models we have described previously ensure the presence of this path by the dependence of A_{t} on past values of the timevarying risk factors (L_{0},…,L_{t}), the dependence of L_{t} on U, and the dependence of Y_{t+1} on U. As described in the section “Datagenerating models”, we varied the degree of confounding (strong, moderate, or weak) by varying the magnitude of the parameter θ_{1} in the model (2), which quantifies the strength of the dependence of Y_{t+1} on U.
Even though there is confounding for the perprotocol effect, the data generation mechanism in our study still allows unbiased estimation of the perprotocol effect as long as the study actually recorded all monthly covariates L_{t} and treatments A_{t}. Graphically, in Fig. 2 there are no open backdoor paths connecting A_{t−1} and A_{t} to Y_{t+1}conditional on past timevarying covariate changes [9]. For example, the open backdoor path A_{t}←L_{t}←U→Y_{t+1} is blocked by conditioning on L_{t}. Note that the measurement of the variable U is unnecessary to adjust for confounding when the variables L_{t} are measured in all t.
However, valid estimation of the perprotocol effect (3) requires the use of adjustment methods that, like IP weighting, can handle the fact that L_{t} is affected by past treatment [3, 4, 10]. We give a detailed description of the IP weighting algorithm in Additional file 2 and the R code in Additional file 1. Briefly, this approach involves: (1) as in the naive analysis, censoring participants when they deviate from their assigned protocol; (2) estimating IP weights which, at each time, are either 0 for censored participants or the reciprocal of the cumulative product of the timevarying probabilities of adherence to the protocol given the participant’s measured confounder history up to that time for uncensored participants; and (3) estimating IP weighted survival curves. Risk differences and risk ratios can then be estimated by the complement of the IP weighted survival estimates. In addition to full measurement of the timevarying covariates, the validity of this approach also relies on correct specification of the model for the adherence probabilities in step 2.
Estimating the perprotocol effect under interval measurement
In practice, many randomized trials are conducted as interval cohorts such that adherence and covariates are recorded only at regular, scheduled followup times. When there are gaps between measurement times, the full history of treatment and covariate changes over the followup will not be completely observed and, generally, there will be unmeasured confounding; that is, under our datagenerating assumption represented by Fig. 2, open backdoor paths will remain after conditioning on only the measured past. Also, the full history of treatment changes will be only partially observed. Under a nonnull scenario, failure to measure interim treatment changes may produce an additional source of unmeasured confounding for treatment effects even at measured times; e.g., in Fig. 2, were there an arrow from A_{t−1} into Y_{t+1}, then an unblockable open backdoor path (by failure to measure A_{t−1}) connecting A_{t} and Y_{t+1} would be present. Partial knowledge of treatment changes thus also requires some form of imputation to estimate the perprotocol effect which is defined by counterfactual intervention in all months, not only months in which measurements are taken. Any imputation method may rest on strong assumptions, for example, imputation under the assumption that treatment does not change during measurement gaps or under missing at random (MAR) assumptions [11].
Suppose, without loss of generality, that the interval between measurements is constant throughout the followup, e.g., m months. We computed an IP weighted estimator of the perprotocol effect (3) and corresponding estimates of the counterfactual survival curves had all participants continuously complied with the protocol in each treatment arm under an intervalcohort scenario with m=12, that is, a scenario in which treatment and covariate changes are measured only at baseline and then every 12 months. In interim months, treatment and covariates were set to the last measured value and the contribution to the weight cumulative product set to 1 for all subjects at these times. In this scenario, there will be residual confounding by failure to adjust for timevarying covariates at unmeasured times. At measured times, IP weights can only be based on the inverse probability that a subject continues to adhere in month s given her partially measured confounder history. This probability is unknown under our datagenerating mechanism (because we generated each A_{t} from the full history). Thus, we would also expect some bias due to model misspecification under this scenario. Here we chose to model adherence based on the cumulative average of past measured values of the continuous timevarying covariate (based on only the baseline and every 12month measurement) and the current value of the binary covariate (as the value from the previous month, the true value needed, will not be measured in this case).
Results
Intentiontotreat effect estimates
Figure 3 shows the estimated intentiontotreat survival curves Pr[Y_{t+1}=0Z=1] and Pr[Y_{t+1}=0Z=0] based on the the cumulative proportion of deaths in each arm by each followup month. Results are shown for the “strong confounding” scenario and the main study of approximately 40% deviators per arm (Scenario 0 in Table 1). As expected, there is no bias in these estimates of the intentiontotreat effect; the curves completely overlap, which is consistent with the fact that the true intentiontotreat effect is null in all months t+1.
Naive versus IP weighted perprotocol effect estimates under full measurement
As illustrated by the top panel of Fig. 4, in our study a “naive” unweighted estimator that ignores timevarying confounders fails to recover the true null perprotocol effect because the curves do not overlap. Rather the estimates of the perprotocol 5year risk difference and risk ratio for standard versus new treatment are 0.11 and 1.77, respectively. The bottom panel of Fig. 4 shows IP weighted estimates of the perprotocol effect under full measurement of the timevarying covariates (m=0). As expected, the estimated survival curves completely overlap, consistent with the truth, which is null. Figure 4 depicts results only under strong confounding. As expected, survival estimates across treatment arms under the naive approach that ignores confounding become closer as the strength of confounding weakens, while IP weighted estimates of the survival curves completely overlap under all scenarios (weak and moderate results are not shown).
IP weighted perprotocol effect estimates under interval measurement
In the intervalmeasurement scenario, we are generally unable to recover the truth of no perprotocol effect. In our study, IP weighted perprotocol effect estimates under m=12 diverged from the null as the strength of confounding increased. Specifically, Fig. 5 shows that differences in the survival curves increase with the strength of confounding, which results in 5year risk difference/risk ratio estimates of 0.034/1.19 under strong confounding, 0.028/1.12 under moderate confounding, and 0.01/1.03 under weak confounding in our large sample.
Figure 6 illustrates that, even under strong confounding, bias decreases with more frequent measurement; estimates of the 5year risk difference get closer to the truth of zero with decreasing m. Specifically, the IP weighted estimates of the risk difference/risk ratio were 0.017/1.02 under m=3,0.029/1.04 under m=6, and 0.034/1.19 under m=12.
Finally, Fig. 7 illustrates that, even under strong confounding and long interval measurement (m=12), bias diminishes with decreasing nonadherence. Specifically, when the proportion of deviators decreased from approximately 40% (Scenario 0 in Table 1) to 20% (Scenario 1 in Table 1), the IP weighted estimates of the risk difference/risk ratio were closer to the null. Bias was negligible, with risk difference/ratio estimates of 0.004/1.005, when there were fewer than 10% deviators per arm (Scenario 2 in Table 1).
Discussion
We used a simulation to study bias in the estimation of perprotocol effects in randomized trials with intervalcohort designs. Bias arose even using methods such as IP weighting, which appropriately adjust for timevarying confounders. However, IP weighted estimates were less biased than estimates from a naive analysis that ignored timevarying confounding.
We considered the simple case of perprotocol effects defined by static treatment strategies (e.g., always take the new treatment versus always take the standard treatment), but our approach could also be applied to dynamic strategies under which treatment changes in response to prespecified events (e.g., a drug toxicity) [12–14]. Also, we considered a simulation without censoring by loss to followup. Censoring may prevent unbiased estimation of both perprotocol and intentiontotreat effects without sufficient and appropriate adjustment for baseline and timevarying covariates [10, 15].
The bias created by interval measurement in the estimation of timevarying treatment effects has been previously highlighted in the computer science literature [16] and in epidemiological studies such as the Framingham Heart Study and the Nurses’ Health Study [7, 17]. In practice, the interval length required to make the bias negligible will depend on the frequency with which treatment and confounders can change. For example, in studies of treatments that rarely change more than once per month (like the one in our simulation), an interval length of one month will likely suffice. In other studies, measures of more frequent covariate changes may be necessary. In addition to more frequent inperson followup, complementary data sources such as electronic health records and pill cap monitors can help capture these changes.
Conclusions
The bias that arises from interval measurement highlights the need for randomized trials designed to collect postbaseline data on timevarying prognostic factors and adherence. This data may be obtained from various sources (e.g., more frequent inperson followup, electronic health records, pill cap monitors). Such planning, aided by the use of causal diagrams representing subject matter knowledge and assumptions, will ultimately provide improved estimates of the perprotocol effect, an informative complement to the intentiontotreat effect.
Availability of data and materials
Not applicable.
Abbreviations
 IP:

Inverse probability
 MAR:

Missing at random
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Acknowledgements
The authors thank Adam Young for assistance with increasing the computational efficiency of the R code.
Funding
This work was funded by PatientCentered Outcomes Research Institute (PCORI) grant 2086435098419 and National Institutes of Health (NIH) grant NIH R37 AI102634.
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MAH and JGY conceived the idea for the manuscript. JGY and MAH designed the simulation and analysis plan and wrote the manuscript. RV and JGY wrote the R code for the simulation and IP weighted estimation. EJM contributed to the simulation design. RV and EJM reviewed and commented on the manuscript. All authors read and approved the final manuscript.
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Additional files
Additional file 1
R code to implement the simulation and IP weighted estimation procedures. (R 23 kb)
Additional file 2
Technical details of the IP weighted estimation algorithm and comparison of bias calculation using a single large sample versus average of many small samples. (PDF 166 kb)
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Young, J.G., Vatsa, R., Murray, E.J. et al. Intervalcohort designs and bias in the estimation of perprotocol effects: a simulation study. Trials 20, 552 (2019). https://doi.org/10.1186/s130630193577z
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DOI: https://doi.org/10.1186/s130630193577z