When to Start, How to Classify, and Whom to Include: A Methodological Assessment and Illustrative Example of the Clone-Censor-Weight Approach for Evaluating Intervention Timing in Observational Studies

Abstract

Introduction

Observational studies evaluating the effect of timing of an intervention, such as early versus deferred drug treatment initiation or short versus long treatment duration, often suffer from bias due to misalignment between eligibility assessment, intervention assignment, and start of follow-up. The clone-censor-weight approach aligns these time points and allows for estimation of treatment effects under predefined timing strategies.

Methods

We assess the clone-censor-weight methodology and illustrate its application in an observational registry-based study of individuals with newly diagnosed diabetes, comparing infection risks under four strategies for initiation of glucose-lowering treatment: initiation within 15 days (Strategy 1), 15 days to 3 months (Strategy 2), 3 to 6 months (Strategy 3), or 6 to 12 months (Strategy 4) after diagnosis.

Results

The clone-censor-weight approach established the diabetes diagnosis as the index date across all strategies. The study example included 33,857 individuals with newly diagnosed diabetes. They were cloned and assigned to all four treatment strategies, where 6439 (19.0%) clones adhered to Strategy 1, 8419 (24.9%) to Strategy 2, 5550 (16.2%) to Strategy 3, and 7539 (22.3%) to Strategy 4. The weighted absolute 5-year risks of infection were 67.0% (95% CI 65.3–68.5) for Strategy 1, 65.7% (95% CI 64.1–66.9) for Strategy 2, 66.8% (95% CI 61.8–71.9) for Strategy 3, and 67.8% (95% CI 62.8–72.7) for Strategy 4.

Discussion

We have assessed the methodology and illustrated the clone-censor-weight approach in a study example evaluating intervention timing. Censoring weights should account for selection bias, estimating per-protocol effects under full adherence, but methodological challenges remain in ensuring that the weights adequately reflect both the target intervention strategies and the population they are intended to represent.

Introduction

Determining the causal effect of an intervention or treatment strategy is a key purpose of designing randomized trials. Some strategies involve a point intervention that is administered once at study entry (eg, vaccine A versus vaccine B). Other strategies involve interventions that are sustained over time.¹ This paper focuses on sustained interventions where the goal is to study the effect of timing of an intervention or treatment. Examples include initiating a treatment planned to last 6 months versus 12 months or comparing early versus deferred treatment initiation. In a randomized trial, individuals are randomly assigned to a specific intervention strategy at the time they become eligible. This ensures proper randomization and establishes a well-defined index date, aligning eligibility assessment with intervention assignment and start of follow-up.^2,3

Observational studies may also aim to examine the effect of the timing of an intervention. These studies often rely on data from healthcare registries or databases, where for example a specific date of surgery, or the date of filling a drug prescription at a pharmacy, is recorded. This makes it possible to approximate the date when the intervention was administered. However, unlike in a randomized trial, the reason why the intervention was administered at that specific time is typically unknown. In such data, intervention strategies may initially appear indistinguishable – for example for early versus deferred treatment initiation, where both groups are untreated before treatment begins. This can be addressed using target trial emulation;^4–10 a framework that explicitly mimics the design and analysis of a hypothetical randomized trial using observational data. The clone-censor-weight approach is a specific method often used within this framework.^10–16 For interventions where the timing of initiation is central, the approach enables valid comparisons by hypothetically assigning individuals to all possible intervention strategies once they become eligible for the intervention, for example at the date of a specific diagnosis. In the analysis data, each individual is copied, or cloned, and hypothetically assigned to all intervention strategies. This mimics the assignment in a randomized trial and ensures a well-defined index date, as all clones are followed from the day they are assigned to the treatment strategy – just as in a randomized trial.

In this paper, we assess the methodological rationale behind the clone-censor-weight approach, focusing on its application to sustained intervention strategies defined using time windows. We aim to describe how the clone-censor-weight approach can address the bias caused by misalignment between eligibility assessment, intervention assignment, and start of follow-up, but in doing so, it introduces new methodological challenges, including artificial censoring, a potentially unequal adherence burden, and reliance on inverse probability weighting, while leaving standard concerns such as residual confounding and selection bias, model specification, and data quality unresolved. To illustrate the clone-censor-weight approach, we apply it in an observational study example using nationwide Danish registry data. We estimate the risk of infection among individuals with newly diagnosed diabetes comparing strategies for initiating glucose-lowering treatment during distinct time windows after the diabetes diagnosis.

Observational Study Example

We designed a study example using nationwide Danish registry data, which can be linked at the individual level using a unique personal identification number assigned to all residents.^17,18 Prescription data were obtained from the Danish Register of Medicinal Product Statistics, which includes all prescriptions filled at community pharmacies since 1994. We also linked to the Danish National Patient Registry for hospital diagnoses and outpatient contacts; the Register of Laboratory Results for Research for laboratory measurements; and the Danish Civil Registration System for vital status and date of death (Supplementary Appendix 1).

Individuals with diabetes have an increased risk of common infections, and poor glycemic control is a known risk factor.¹⁹ In our observational study example, we hypothesized that early initiation of glucose-lowering treatment in patients with newly diagnosed diabetes (leading to earlier glycemic control) may reduce the risk of subsequent infection compared to deferred treatment initiation. Our focus is not on the effect of the treatment itself (treatment versus no treatment) as this has already been established,¹⁹ but the effect of the timing of the treatment initiation (early versus deferred treatment initiation). Individuals were included on the day of their diabetes diagnosis (Figure 1). This date served as the study entry date. The target trial protocol, including eligibility criteria, study specifications, and data descriptions, is outlined in Supplementary Appendix 1.⁵ We designed this observational study example to illustrate the implementation and interpretation of the approach and to support the methodological discussion. As such, the example is intended for methodological illustration rather than to yield fully clinically interpretable causal estimates.

Figure 1.

Flowchart showing the study population, along with the cloning, treatment assignment, and check for deviation and adherence within the four treatment strategies. Details about the eligibility criteria are provided in the target trial protocol (Supplementary Appendix 1).

Treatment Strategies

We defined four disjoint treatment strategies, each characterized by a distinct treatment window for initiating glucose-lowering treatment within a 1-year treatment assessment period: 1) immediate initiation of glucose-lowering treatment, with a prescription filled within 15 days after diabetes diagnosis; 2) remain untreated the first 15 days, followed by a prescription filled between 15 days and 3 months after diagnosis; 3) remain untreated the first 3 months, followed by a prescription filled between 3 and 6 months after diagnosis; or 4) remain untreated the first 6 months, followed by a prescription filled between 6 and 12 months after diagnosis (Figure 2). These treatment strategies are considered sustained interventions, as “remain untreated” is an intentional part of the planned intervention, and the overall treatment strategy is thus administered over time.^1,11,13 We defined the treatment strategies as treatment initiation indicated by a registration of a first redeemed glucose-lowering drug prescription, assuming no treatment if no prescription was present. This is usually considered as a well-defined exposure for the causal consistency assumption in the case of a point intervention.²⁰

Figure 2.

Index date, day 0, was defined as the date of the diabetes diagnosis. The first year after the index date was used to assess the treatment strategies. Follow-up was initiated at index date and ended after a total of five years. The first clone for Individual ID1 was censored after 15 days because treatment was not initiated before the end of the treatment window. Similarly, the second clone was censored after 3 months. As the individual initiated treatment during the treatment window from 3 months to 6 months, this complies with Strategy 3, and this clone is therefore not censored. The fourth clone was censored because treatment was initiated already before the treatment window. The individual had an infection during follow-up, but this infection counts only for Clone 3, who followed the assigned treatment strategy, as the other clones were already censored at the time of the outcome. For individual ID2, whose treatment pattern was similar to that of ID1, the outcome occurred in the period from 15 days to 3 months after diagnosis. As Clone 2, Clone 3, and Clone 4 were still considered eligible for their treatment strategies (ie, the individual had not yet deviated from Strategy 2, Strategy 3, and Strategy 4), the outcome was included for all three clones. The data included in Supplementary Appendix 2 show how the hypothetical individuals, ID1 and ID2, would be represented in the analysis data. ID3 was similar to ID1, but had no outcome and was therefore followed for the entire five years of follow-up in Strategy 3. ID4 did not initiate treatment during the treatment assessment period, and was therefore censored at the end of each treatment window.

Clone-Censor-Weight

In the following section, we present the rationale behind the clone-censor-weight approach, illustrated through our observational study example.

Alignment of Eligibility, Treatment Assignment, and Follow-Up Start

To emulate the treatment assignment that would occur at the time of randomization in a randomized trial, all treatment strategies are hypothetically assigned at the time of the diabetes diagnosis. To do so, we created a data set with four copies of all data from each individual. Each copy is considered a clone, and each clone was then assigned to one of the four treatment strategies at the time of the diabetes diagnosis, regardless of the actual treatment status during follow-up. This mimics the treatment assignment structure of the target trial by allowing every clone to be assigned to every treatment strategy at the time of diabetes diagnosis. To enhance the likelihood that the causal positivity assumption holds (ie, that all individuals have a non-zero probability of receiving each treatment²⁰), our study population was restricted to individuals with newly diagnosed diabetes who in clinical practice would likely initiate glucose-lowering treatment within the first year. We excluded individuals with markers of advanced age or frailty, who were unlikely to be eligible for such treatment due to short life expectancy, high risk of hypoglycemia, or other contraindications. We also excluded individuals almost certain to receive immediate glucose-lowering therapy, such as those with markedly elevated haemoglobin A1c (HbA1c) levels. All remaining individuals were therefore eligible for all four treatment strategies (Supplementary Appendix 1). As the individuals were cloned and hypothetically assigned to all treatment strategies, the four treatment groups were identical with respect to all characteristics at baseline (not just in expectation as in a randomized trial). The cloning therefore removes baseline confounding and ensures that the causal exchangeability assumption holds (at baseline).²⁰ In addition, as all clones were assigned to a treatment strategy at the diabetes diagnosis date, we have aligned the time of eligibility assessment, intervention assignment, and start of follow-up.^2,3

Enforced Adherence Through Artificial Censoring

As a consequence of the cloning, individual data contribute equally to all four treatment groups, and a standard intention-to-treat analysis of the cloned data would therefore yield identical event rates in the four treatment strategies.¹⁰ We therefore rely on a per-protocol analysis, censoring clones in a given treatment group when they deviate from the assigned treatment strategy. As a result, the individual no longer contributes equally across all treatment groups, and it corresponds to modeling full adherence to the assigned strategy. As illustrated in Figure 2, clones were censored at treatment initiation, if they initiated prior to the treatment window in the assigned treatment strategy. Clones were also censored at the end of the treatment window if they did not initiate during the treatment window in the assigned treatment strategy. Clones complying with their assigned treatment strategy were not censored (Figure 2). As part of the analysis, we have thus introduced this censoring mechanism to the data, and we refer to it as “artificial” censoring, to highlight the distinction from the “classical” censoring (eg, death, emigration, loss to follow-up, or end of study).^13,15 If the decision regarding treatment initiation was either completely random (as in a randomized trial) or was based on patient characteristics not associated with the outcome (eg, geographic regions or birth cohorts affected differently by treatment policies), the artificial censoring would not induce selection bias during follow-up.¹⁵ However, treatment initiation is most likely determined based on individual characteristics potentially also affecting the outcome (ie, characteristics that may be confounders). In our example, individuals who were diagnosed with diabetes at a relatively young age, who were obese and insulin resistant, or already showed subtle signs of diabetes complications, could be likely candidates for earlier and more aggressive glucose-lowering treatment than other individuals, but they would also have a high expected baseline risk of infections. Therefore, while artificial censoring is necessary to enforce adherence and obtain meaningful per-protocol analyses, it also introduces selection bias because censoring cannot be assumed to be non-informative.²¹

Selection Induced by Artificial Censoring

One way to account for the selection bias introduced by the artificial censoring is to apply inverse probability of censoring weighting.²¹ As the selection changes the population over time, the weights are continuously updated to reweight the remaining clones. Clones who remain in the study and resemble those who were censored are given more weight, thereby compensating for those that were censored. The weights are usually determined as the inverse of the probability of being artificially censored from the data.^21,22 The two most commonly used methods to estimate the probabilities are the survival setup with a product-limit estimation, eg, using a multivariable Cox model combining the linear predictor and the baseline hazard to fit the survival curve, and the multivariable pooled logistic regression, multiplying probabilities of deviation in small intervals to approximate the survival curve. Either way, the model should include patient characteristics associated with the outcome and the treatment strategies,²¹ and both baseline covariates and time-varying covariates can be included in the censoring model.¹² Under the assumption that all relevant confounders are adequately captured by the variables included in the censoring model, the weighted sample represents a pseudopopulation where the censoring mechanism, which is in fact the treatment assignment, is independent of the outcome. To reduce the influence of extreme weights, the weights can be stabilised, eg, by adding the marginal probability of being artificially censored to the numerator.^12,21 This probability can be estimated using the same methods but without including any covariates in the model. In addition, extreme weights (stabilised as well as unstabilised) may also be truncated at pre-specified percentiles (eg, the 99th percentile). We refer to eg, Willems et al,^21,22 for more information about dependent censoring.

Outcome Analysis Under Each Treatment Strategy

The outcome of interest can be assessed in a per-protocol analysis using the cloned and weighted data set. Depending on the aim of the study, several statistical models and estimation procedures can be used, provided they accommodate time-updated weights.¹² As an example, the hazard ratio can be estimated from a weighted Cox proportional hazards model, and the absolute risks can be estimated from the weighted cumulative incidence or from the complement of a weighted Kaplan–Meier estimator. When calculating weighted survival curves, the stabilised and unstabilised weights will often result in the same survival probabilities as the marginal probabilities cancel out.²² For other estimation procedures, the choice of weight may influence the outcome model.¹² Regardless of the estimand, confidence interval estimation must account for the repeated inclusion of individuals and the correlation among the weighted observations. One approach is bootstrapping, although it may not be feasible in large data sets because of the computational burden. The corrected sandwich estimator has been suggested as a valid method for estimating confidence intervals for inverse probability weighted Cox models.²³

Implementation of the Clone-Censor-Weight Approach

The original data in our observational study example included information on ID, study entry date, date of first glucose-lowering drug prescription, status and date of outcome and classical censoring, along with potential covariates to include in the censoring model (Supplementary Appendix 2). Each row in the data set represented one unique individual. The individuals were cloned, and four identical copies were generated along with a variable indicating the clone/assigned treatment strategy. For each clone, the deviation status and date were added within each treatment strategy (Supplementary Appendix 2). As the censoring weights are estimated during follow-up, data were transformed from wide format with one row per clone to counting process data on long format, ie, with multiple rows per clone based on time intervals between two event times in the full population (Supplementary Appendix 2).^15,22 We estimated the censoring weights by estimating the probability of being uncensored at the end of each time interval. We used a Cox model and extracted and combined the linear predictor and estimated baseline hazard (Supplementary Appendix 3).²² Our censoring model included age, sex, and baseline HbA1c. The unstabilised weights were calculated as the inverse of the probabilities from the Cox model. The stabilised weights were calculated using the marginal probabilities of remaining uncensored, ie, probabilities from a Cox model without covariates, as the numerator (Supplementary Figure 1). Both the stabilised and the unstabilised weights were truncated at the 99^th percentile. Using data on long format, including the weights for each time period, allows for estimation of the weighted hazard ratio, the weighted survival curves, and the weighted cumulative incidence curves. The weights ensure that these estimates represent the full population under full adherence to the assigned treatment strategy (Supplementary Figure 2). We estimated the weighted cumulative incidences with death as a competing event, whereas death was considered a censoring event in the Kaplan–Meier analysis. To estimate confidence intervals, we ran the analyses with R = 200 replicates in a bootstrap analysis using the normal approximation. In Supplementary Appendix 3, we have included extracts of code from SAS and R to outline the clone-censor-weight approach. We also refer to Maringe et al,¹⁵ Duchesneau et al,¹⁶ Willems et al,^21,22 and Webster-Clark et al²⁴ for other studies where relevant code is included.

Comparison with Commonly Used Approaches

We also analyzed data using time-dependent Cox regression and a landmark analysis. These methods represent commonly applied methods in observational studies and therefore provide a useful point of comparison. The approaches rely on different modeling assumptions, target different causal estimands, and address time-related biases in distinct ways.

First, we used a time-dependent Cox regression model, which accounts for changes in treatment status over time by updating exposure during follow-up. All individuals in the population were included in the analysis, and follow-up started at the index date, which was defined as the date of diabetes diagnosis. All individuals were considered untreated until a prescription was filled, at which point the exposure status changed based on the time since diagnosis. The treatment strategies were used to define the exposure groups, and prescriptions filled within 15 days after diabetes diagnosis were used as the reference category. The model estimated the hazard ratio adjusted for the baseline confounders age, sex, and HbA1c value.

Second, we conducted a landmark analysis, aligning treatment assignment and the start of follow-up at the landmark time, defined as one year after diabetes diagnosis. Individuals were assigned to exposure groups based on their observed treatment status at the end of the 1-year treatment assessment period. The analysis only included individuals who initiated treatment during the first year and were still at risk of the outcome, ie, had neither been censored nor experienced the event during the first year. We estimated the cumulative incidences along with the hazard ratio for the subsequent four years, adjusting for age, sex, and HbA1c at the diabetes diagnosis date.

All analyses were conducted using SAS version 9.4 (SAS Institute Inc, Cary, North Carolina) and R version 4.4.1 (R Core Team, 2020).

Results

A total of 33,857 individuals were included in the study population after assessing the inclusion criteria on the date of diabetes diagnosis (Figure 1). The median age was 61.0 years (IQR 54.2–67.9), 14,676 (43.3%) were female, and the median HbA1c was 50.0 mmol/mol (IQR 48.0–54.0) (Supplementary Table 1). Follow-up began at the diagnosis date, and during a median of 4.7 years (IQR 3.1–5.0) of follow-up, a total of 20,352 (60.1%) individuals had an infection. Close to half of the infections, 9095 (44.7%), occurred during the first year. A total of 17,049 (50.4%) individuals initiated glucose-lowering treatment during the first year after the diabetes diagnosis, and observed median time to treatment initiation was 27 days (IQR 11–100) (Supplementary Figure 3). All individuals were cloned and assigned to the four treatment strategies. Of the 33,857 clones assigned to each strategy, 6439 (19.0%) clones adhered to Strategy 1, 8419 (24.9%) adhered to Strategy 2, 5550 (16.2%) adhered to Strategy 3, and 7539 (22.3%) adhered to Strategy 4 (Figure 1). To model full adherence (per-protocol estimate) to the assigned strategy, adhering clones were weighted to account for the clones deviating from the treatment strategy (Supplementary Figure 2). Thus, the weighted absolute 5-year risks of infection, accounting for age, sex, and baseline HbA1c, were 67.0% (95% CI 65.3–68.5) for Strategy1, 65.7% (95% CI 64.1–66.9) for Strategy 2, 66.8% (95% CI 61.8–71.9) for Strategy 3, and 67.8% (95% CI 62.8–72.7) for Strategy 4 (Figure 3 and Table 1). The weighted cumulative incidence curves were similar to the complement of the weighted Kaplan–Meier curves, as only 428 (1.3%) of the individuals died without a prior infection (Figure 3 and Supplementary Figure 4). Using Strategy 1 as reference, hazard ratios for timing strategies 2 to 4 were all close to 1.0 (eg, HR using stabilised weights: 0.96 (95% CI 0.92–1.00) for Strategy 2, 0.99 (95% CI 0.92–1.08) for Strategy 3, and 0.97 (95% CI 0.90–1.03) for Strategy 4) (Table 1).

Figure 3.

Weighted cumulative incidence curves accounting for age, sex, and baseline HbA1c for the four treatment strategies. The curves were equal for stabilised and unstabilised weights.

Table 1.

Results from the analysis using the clone-censor-weight approach, along with results from the standard approaches (time-dependent Cox regression and landmark analysis)

Treatment Strategy (Clone)	Clone-Censor-Weight Approacha (N = 33,857 with 20,885 Outcomesb)					Time-Dependent Cox Analysis (N = 33,857 with 20,352 Outcomesc)	Landmark Analysis (N = 12,305 with 5590 Outcomes)
	5-year 1-KM (Kaplan–Meier)	5-year Cumulative Incidence	Hazard Ratio, Stabilised Weights	Hazard Ratio, Unstabilised Weights	Hazard Ratio, no Weights	Hazard Ratio	Hazard Ratio (Four Years)	5-year Cumulative Incidence (Four Years)
Strategy 1 (1–15 days)	67.48 (65.84–69.04)	66.95 (65.32–68.51)	Ref.	Ref.	Ref.	Ref.	Ref.	53.36 (51.56–55.14)
Strategy 2 (15 days to 3 months)	66.42 (64.84–67.69)	65.65 (64.09–66.92)	0.96 (0.92–1.00)	0.95 (0.90–1.00)	1.00 (0.96–1.04)	0.97 (0.93–1.02)	0.97 (0.92–1.04)	54.10 (52.42–55.75)
Strategy 3 (3–6 months)	67.21 (62.08–72.36)	66.80 (61.80–71.94)	0.99 (0.92–1.08)	1.01 (0.89–1.15)	1.02 (0.98–1.06)	1.02 (0.95–1.10)	0.97 (0.88–1.06)	54.19 (51.15–57.13)
Strategy 4 (6–12 months)	68.34 (63.19–73.38)	67.80 (62.75–72.73)	0.97 (0.90–1.03)	0.97 (0.84–1.08)	1.03 (0.99–1.07)	1.09 (1.01–1.17)	1.05 (0.97–1.15)	58.41 (55.50–61.20)

Notes: ^aConfidence intervals for the clone-censor-weight approach were estimated using R = 200 bootstrap replicates. ^bIn the clone-censor-weight approach, an outcome can be counted multiple times as it is included for all clones who were not censored at the time of the outcome (Figure 2). ^cIn the time-dependent Cox analysis, all 20,352 outcomes were included, however, only 16,977 outcomes were attributed to the treatment strategies, as the remaining outcomes happened while the individual was considered “untreated” (either before treatment initiation or if treatment initiation either never happened or happened after the treatment assessment year). All estimates except the non-weighted hazard ratio from the clone-censor-weight approach and the cumulative incidence in the landmark analysis were corrected for age, sex and baseline HbA1c value. In the time-dependent Cox regression and landmark analysis, the treatment strategies were used to define the exposure groups, and treatment initiation within the first 15 days after diabetes diagnosis was used as the reference category.

In the time-dependent Cox analysis, all 33,857 individuals were included, and all the 20,352 outcomes contributed to the analysis (Table 1). However, only the 16,977 outcomes occurring after treatment initiation were attributed to the exposure categories. Outcomes occurring before treatment initiation contributed to the unexposed category which was not part of the treatment strategies in our study example. Compared to Strategy 1, the HRs adjusted for age, sex, and baseline HbA1c were 0.97 (95% CI 0.93–1.02) for Strategy 2, 1.02 (95% CI 0.95–1.10) for Strategy 3, and 1.09 (95% CI 1.01–1.17) for Strategy 4.

In the landmark analysis, the population was restricted to the 12,305 individuals who both initiated treatment and were neither censored nor had the event during the first year. This analysis included 5590 outcomes. Because the landmark time was set at one year after diabetes diagnosis, the estimated risks were based on the subsequent four years of follow-up (ie, in the period up to five years after diabetes diagnosis) and were 53.4% (95% CI 51.6–55.1), 54.1% (95% CI 52.4–55.8), 54.2% (95% CI 51.2–57.1), and 58.4% (95% CI 55.5–61.2) under treatment strategies 1–4, respectively (Table 1 and Supplementary Figure 5).

Discussion

In this study, we emulated a target trial examining the effect of the timing of glucose-lowering treatment initiation on the risk of subsequent infection. Using this observational study example, we assessed the methodology behind the clone-censor-weight approach. Cloning helps establish a well-defined index date and removes baseline confounding, albeit at the expense of selection bias introduced by informative censoring. Weighting accounts for this selection by reweighting individuals who complied with their assigned treatment strategy.

When to Start

In a well-conducted randomized trial, eligibility criteria, intervention assignment, and the start of follow-up are inherently aligned by design. This might not be possible when observational data are used to study treatment strategies that are sustained over time. A naïve approach is to start follow-up at study entry (eg, diabetes diagnosis) and then classify individuals according to their future observed treatment strategy. Or alternatively, to start follow-up when the individual’s treatment strategy is fully observed. It is well-known, that these approaches can introduce bias and lead to selection and/or misclassification issues due to the lack of a well-defined index date.^2,3,10,16 Instead, we addressed this using the clone-censor-weight approach.^2,3,25,26 All individuals are followed from the study entry date, where, as in the randomized trial, eligibility criteria are assessed, individuals are assigned to an intervention strategy, and follow-up is started. This is the key contribution of the clone-censor-weight approach: the establishment of a well-defined index date through alignment of eligibility assessment, intervention assignment, and start of follow-up. A simpler approach is to shift the index date, as done in the landmark analysis, start follow-up after the entire treatment assessment period and then use the observed treatment status. The approach is straightforward and easy to comprehend, but it answers a different causal question by conditioning on treatment status at a fixed time point.² Also, the landmark analysis does not allow for outcomes occurring during the treatment assessment period. In our study example, 45% of the outcomes occurred during the first year. Individuals with these early outcomes were excluded from the landmark analysis, as they were no longer at risk of the outcome at the shifted index date. In the clone-censor-weight analysis, these outcomes are included for all clones where the data remained consistent with the treatment strategy (Figure 2). The approach is thus mimicking the intention-to-treat outcome analysis in a randomized trial, where outcomes are assessed based on initial randomization, independent of subsequent treatment decisions.^27,28 As individuals were cloned at baseline, the intention-to-treat analysis is in fact uninformative with the clone-censor-weight approach, and the analysis had to be changed to a per-protocol analysis to yield valid estimates. In other situations, the simplicity of the landmark analysis and the option to estimate intention-to-treat effects outweighs the potential drawbacks.

How to Classify

In the beginning of the follow-up period, individuals in observational data may be compatible with multiple treatment strategies until the actual treatment pattern emerges (eg, initiate 3–6 months or initiate 6–12 months after diabetes diagnosis), complicating the assignment of their data to one specific strategy.¹⁴ The clone-censor-weight approach addresses this by assigning each individual to all strategies at study entry, censoring each clone upon deviation, and weighting the data in a per-protocol analysis. Outcomes are thus attributed to a treatment strategy as long as the clone has not yet deviated from it. Alternatively, the time-dependent Cox analysis, which also uses study entry date as starting point, represents an as-treated analysis: outcomes are assigned to the treatment strategy the individual is following at the time the outcome occurs.^3,12 In the as-treated analysis, outcomes occurring prior to treatment initiation are not attributed to any of the treatment strategies, as the individual is considered “untreated”. Consequently, the as-treated analysis introduces selection, as it requires outcome free survival up until eg, 6 months, in order to estimate the effect of initiating treatment in the 6–12 months period. The time-dependent Cox analysis therefore answers a different causal question, as it estimates the effect of treatment under a model where treatment status can change over time. Unexposed, or untreated, time is right censored at treatment initiation, whereas individuals contributing to a given treatment group must survive and remain event-free until the corresponding treatment window, resulting in delayed entry (left truncation) into the exposed groups. In our study example, treatment initiation after the 1-year treatment assessment period was not considered a treatment strategy of interest. In the time-dependent Cox analysis, these individuals would be considered “unexposed” in line with individuals with an outcome prior to treatment initiation and individuals who never initiate treatment.

We are estimating the effect of when treatment should be initiated – which is in principle the same as estimating the effect of the “duration of non-treatment”. Thus, studies investigating the effect of duration of treatment and/or initiation of treatment can methodologically be considered two sides of the same coin. A treatment strategy for treatment duration could for example be defined as “remain treated the first 15 days and then stop during the period 15 days to 3 months”, which aligns with the treatment initiation strategies in our study example. Treatment is planned to be initiated during predefined treatment windows, requiring individuals to first refrain from treatment before the treatment window and then initiate treatment during the treatment window. This implicitly defines a treatment strategy not only in terms of when treatment should be initiated but also in terms of how treatment uptake is assumed to occur within the window.^1,11,24 A strategy defined by treatment initiation within a predefined time window would intuitively imply a roughly uniform uptake throughout the interval, such that the proportion of individuals treated increases gradually throughout the window rather than abruptly at the end (Supplementary Figure 2). This may have important implications for the interpretation of the target intervention, as the weighting procedure may not adequately reflect the treatment uptake pattern implied by the treatment strategy. In short, individuals who do not initiate within the treatment window are essential “reclassified” or “forced” to initiate at the end of the treatment window (or after a certain grace period), as their data are censored and “replaced” by data from weighted individuals who in fact did initiate during the treatment window. Consequently, concerns regarding the consistency assumption may arise, and treatment uptake may need to be incorporated into the weighting procedure (Supplementary Figures 2 and 3). We did not make any corrections to our weights but refer to eg, Huitfeldt et al,¹ Cain et al,¹¹ and Webster-Clark et al^24,29 for more details. We believe that further methodological research is needed to better understand how treatment uptake patterns within predefined windows should be incorporated into the weighting procedure. Also, we did not check the validity of our estimated weights, as there is (at least to our knowledge) no consensus on how to accurately do so. Standardized mean differences have been proposed as a possible measure of validity regarding covariate balance, however, they should not be estimated across clones (as with inverse probability of treatment weighting) but rather across time within each clone. The validity of the clone-censor-weight approach relies on correct specification of the censoring model. It is therefore crucial to determine which confounders to include in the model and, as in standard analyses, this can be challenging. The purpose of the weighting procedure is to reweight the remaining clones such that they represent the full population originally assigned to each treatment strategy prior to artificial censoring. By doing so, the weights aim to restore baseline comparability (covariate balance) and thus support the exchangeability assumption among the remaining clones. It is not only a matter of identifying relevant confounders but also of having access to their values and being able to appropriately adjust for them. This applies to both baseline and time-dependent confounders, which may evolve during follow-up and influence both subsequent treatment decisions and the outcome. The censoring weights compensate for the artificial censoring introduced by the clone-censor-weight approach, not for selection due to other causes. The outcome itself can potentially also cause selection during follow-up.^14,30 It could be the case that only those without the outcome (eg, mortality) in the early phase were eligible for treatment initiation in the later phase. Additional weights controlling for outcome selection, competing events, loss to follow-up, etc, can be estimated in a similar way and combined to a total weight.

Whom to Include

We restricted the population to individuals, not just eligible for treatment, but eligible for all predefined treatment strategies. This restriction served to mimic randomization in a randomized trial, where individuals could be assigned to any of the treatment strategies at the index date. In addition, restricting the population in this way increases the plausibility of the positivity assumption by ensuring that all individuals could, in principle, follow each of the treatment strategies under consideration. Individuals never initiating treatment (or initiating after the first year) were included in our study population, as they were initially eligible for treatment. These individuals were censored at the end of each treatment initiation window as they deviated from the treatment strategies, and the per-protocol estimate models full adherence to the assigned strategy. Whereas treatment strategy 1 only restricts an individual the first 15 days (initiate within 15 days), treatment strategy 4 restricts individuals up to a year after diabetes diagnosis (do not initiate the first 6 months and then initiate during the next 6 months). This unequal adherence burden may introduce additional selection, as individuals assigned to some treatment strategies must remain adherent for considerably longer than individuals assigned to other strategies. Yet, the per-protocol nature of the estimate means we determine the effect in those who completed the study as intended (ie, followed their assigned treatment strategy), providing insights into the efficacy of the treatment strategy when followed correctly.³⁰ One way to reduce differences in the unequal adherence burden across strategies would be to define treatment strategies that also specify continued treatment use after initiation, in order for all strategies to require adherence for the full year. However, such strategies would address a different research question, and the focus of our study was the effect of timing of treatment initiation rather than the effect of sustained treatment use following initiation.

The clone-censor-weight approach allows estimation of weighted absolute risks under each strategy, offering clinically interpretable measures of what would happen if these interventions were implemented. Beyond the population-level estimates, the approach also supports individualized prediction under interventions.³¹ This involves estimating the risk for a specific individual if they were to follow a given treatment strategy, conditional on their baseline characteristics. Such predictions are increasingly important for personalized decision-making. The clone-censor-weight approach makes these predictions possible because it mimics randomization and enforces adherence to predefined strategies.³²

Conclusion

Comparing treatment strategies involving interventions sustained over time is often of interest but challenging. As always, choosing the right study approach depends on the study question, along with factors such as, eg, the distribution of the exposure and the outcome, the amount of confounding, the desired estimand, and the necessary assumptions. However, the clone-censor-weight approach establishes a well-defined index date aligning eligibility assessment, intervention assignment, and start of follow-up. The approach averts misclassification of follow-up time but introduces selection bias during follow-up and requires weighted analyses. While it does not support intention-to-treat analyses, it provides clinically relevant estimates, as it allows for estimation of absolute treatment effects adjusted for both baseline and time-dependent confounding. Despite its utility, the approach still demands careful evaluation, as methodological challenges remain in ensuring that the weighting procedure adequately represents both the target intervention strategies and the populations it is intended to represent.

Funding Statement

This study received funding from the Independent Research Fund Denmark (project number 4308-00084B).

Abbreviations

HbA1c, Haemoglobin A1c.

Data Sharing Statement

The data used in this study are owned and managed by Statistics Denmark. In accordance with Danish law and data protection policies, the data used in this study were anonymized, and were stored and analyzed on a secured server. The data are available to researchers from research environments pre-approved by Statistics Denmark after project approval by the Danish Data Protection Agency and Statistics Denmark. Researchers can apply for access to data when the request is approved by the Danish Data Protection Agency (https://www.datatilsynet.dk). Essential parts of the computing code are available in the Supplementary Information.

Ethics Approval and Consent to Participate

According to Danish legislation, ethical approval or informed consent from participants is not required for registry-based, observational studies. All data originated from registries, and no data were specifically collected for this project. This study was registered at Aarhus University’s repository (no. 2022-0367531/810).

Author Contributions

All authors made a significant contribution to the work reported, whether that is in the conception, study design, execution, acquisition of data, analysis and interpretation, or in all these areas; took part in drafting, revising or critically reviewing the article; gave final approval of the version to be published; have agreed on the journal to which the article has been submitted; and agree to be accountable for all aspects of the work.

Disclosure

The authors declare that they have no competing interests.