Observational Target-Trial Emulation

Sort eligible people into the aspirin group if they fill at least three prescriptions after time zero, and clock follow-up from eligibility. Starting the clock at eligibility is the right place to start it. The rest of that design is a disaster, and it has a name. A 2016 paper in the Journal of Clinical Epidemiology files it as “Emulation failure 4: time zero is set at eligibility, but treatment strategy is assigned after time zero (classical immortal time bias)”. The paper builds the smallest version of it as a worked example.

The group labels were written later. That is the whole problem, and the authors put the consequence in one line: “If it takes at least a year after time zero to fill three prescriptions, this emulation approach ensures that individuals in the aspirin group have a guaranteed survival of at least 1 year.” To be filed under aspirin, a patient had to still be alive and still under observation on the day of the third fill. Anyone who died before then never got the chance to be counted as treated, and went into the comparison group instead. The treated group was assembled partly out of people who had already survived. Some of what the analysis reports as a benefit of aspirin is the benefit of not having died before the label was assigned.

Nothing about the prescription records is wrong. The classification used information from after the clock started, and no amount of adjustment repairs that.

So the repair has to be structural, and it is mechanical. In 2020 Maringe and colleagues put it in a single sentence: “Two exact copies (clones) of each patient's record are created: one clone is allocated to the intervention arm of the emulated trial, the other clone is allocated to the control arm.” Both copies enter at eligibility, before anyone knows what the patient will do. Run both forward. The moment a copy's real behaviour contradicts the strategy it was given, cut it off there. Now no label depends on the future, because every label was written at the start line.

The same paper prices the repair. The patients are 2,309 English patients aged 70-89 with early-stage lung cancer, under a six-month grace period for surgery. The naive analysis put the one-year survival benefit at 22.4% (95% CI 18.1-26.9). Cloning alone brought it to 17.3% (95% CI 14.6-20.1). Inverse-probability-of-censoring weights brought it to 11.4% (95% CI 7.9-15.3). The RMST gain fell from 33 days (95% CI 14-48) to 13 days (95% CI 8-20).

The bill arrives with the clones. The copies that get cut are not cut at random, so the ones still running have to be reweighted to speak for them. That is the step that moved the estimate again, from 17.3% to 11.4%.

The discipline that would have caught the aspirin mistake is dull, published, and comes first. Hernán and Robins set it out in 2016, and their abstract states the whole programme in one sentence: “Causal inference from large observational databases (big data) can be viewed as an attempt to emulate a randomized experiment—the target experiment or target trial—that would answer the question of interest.”

Table 1 of that paper enumerates seven components of the target trial protocol. You write them before touching the database. Eligibility criteria; the treatment strategies being compared, including their start and end times; assignment procedures; the follow-up period; the outcome of interest; the causal contrast(s) of interest; and the analysis plan. The time zero this lesson keeps insisting on is not a separate invention. It is the start time carried inside the second component. What the lesson calls the estimand is the sixth.

Only then do you turn to the records and ask, line by line, what stands in for each item. Eligibility becomes a query. Time zero becomes a date. The outcome becomes an event and a timestamp.

Assignment is the line with no honest counterpart, and the whole method exists to cover for it.

When the strategies involve timing or a window, the covering move is the one from the first section, and it has a fixed shape. Find the eligibility times, which may be a single baseline per person or a fresh entry at every date they qualify. Clone each eligible person into every plan still compatible with them at that moment. Keep each clone alive while the observed history keeps fitting its plan. Censor the clone when the history stops fitting. Then weight the survivors for the censoring and compare the strategies.

What you get out of that sequence is an analysis whose group labels are all written at time zero. What you do not get is randomisation. Everything now rests on three things. That you measured the time-varying factors that predict deviation and censoring. That someone is left following each plan in every corner of the population you are describing. And that the treatment histories are accurate about when things happened, not merely whether they happened.

All four have already appeared, and each has a published definition narrower than the way the word gets used. They are worth pinning down against the thing each is most often confused with. Most of the errors in this design are somebody using one of these words loosely.

Longitudinal data is often described as rich when what is meant is that it is large. Many rows per person is not the same thing as knowing when the treatment started. The protocol you wrote decides which fields matter. If those fields are thin the emulation fails no matter how many rows there are.

Put the ideal trial in one column and what the data offers in the next, then the analysis that connects them, then the gap. One row per protocol component. The components are not yours to choose. Use the seven Hernán and Robins enumerate: eligibility criteria; the treatment strategies being compared, with their start and end times; assignment procedures; the follow-up period; the outcome of interest; the “causal contrast(s) of interest”; and the analysis plan. Give time zero its own row if it helps you see it, but know that it belongs to the strategies row above it.

The point of the layout is that the mismatches end up written next to the things they are mismatches with, where you cannot avoid reading them together.

The aspirin emulation never had such a document. Had it existed, the follow-up row would have said the clock starts at eligibility. The assignment row directly above would have said the group is decided by three prescriptions filled afterwards. The contradiction — emulation failure 4, “classical immortal time bias” — would have been visible on the page before a single patient was pulled. Write the dossier first and it is a design tool. Write it afterwards and it becomes a list of excuses.

The first way is the aspirin way: let the window run, see what the patient did, then write the label. It is the most natural thing to do with a database, and it is the one that fails. The label depends on surviving long enough to earn it — a guaranteed year of life for anyone who took a year to reach the third prescription.

The second way removes the window entirely. Cain and colleagues laid out a grid of regimes over the French Hospital Database on HIV: “initiate treatment within m months after the recorded CD4 cell count first drops below x cells/mm3”, with x from 200 to 500 in steps of 10. This is the arm of that design where m equals 0. Start on the day the threshold is crossed, and treat any later start as a different strategy. The labels are now honest, since everything is decided at time zero. The difficulty is that hardly anyone starts on the first day. So the comparison is made among a small and unusual group, and in some corners of the population there is nobody following that plan at all. The timing problem is gone and a support problem has replaced it.

The third way keeps the window and pays for it. It is the same grid with m equal to 3 months, or the six-month window for surgery in the lung-cancer emulation. Clone at eligibility, let the clone assigned to early initiation run through the grace period, and censor it if the patient reaches the end of the window without starting. Labels are written at time zero, and the strategy still resembles something a clinician would recognise. The price is the censoring weights and every assumption behind them. That is a real cost — most of the distance between 17.3% and 11.4% — but it is a cost you can inspect. The first way's is not.

The estimate is about the strategies you specified, in the population the eligible records represent. It holds if the measured history is enough to make the compared groups exchangeable, if people following each plan are actually present throughout that population, if the measurements say what they appear to say, and if the censoring model is right about why clones were cut.

How much that discipline buys has been measured. The RCT-DUPLICATE initiative emulated 30 completed and 2 ongoing randomised trials in three US claims databases. It reported in JAMA in 2023 an overall Pearson correlation of 0.82 (95% CI 0.64-0.91) with the trials, 75% statistical-significance agreement and 66% estimate agreement. The interesting number is what happens when you split that pool by how well the design could be reproduced. Among the 16 trials whose design could be closely emulated the correlation was 0.93 (95% CI 0.79-0.97), with 88% estimate agreement. Among the 16 where key design elements could not be emulated it was 0.53 (95% CI 0.00-0.83), with 50% estimate agreement. Their conclusion: “Real-world evidence studies can reach similar conclusions as RCTs when design and measurements can be closely emulated, but this may be difficult to achieve.”

When the design does fit, the payoff is not subtle. The Nurses' Health Study was re-analysed as a sequence of nested trials, with the labels written at the start line. The intention-to-treat hazard ratios for coronary heart disease came out at 1.42 (95% CI 0.92-2.20) in the first two years and 0.96 (0.78-1.18) over the whole follow-up. That is close to the Women's Health Initiative randomised results. It is the opposite of the protective association the same cohort had previously produced.

So the report should carry the full list of conditions, alongside every point where the emulation departed from the ideal trial. A reader who is told the mismatches can decide which side of the 88%/50% split this analysis is on. A reader who is only told the estimate cannot.

When the key histories are missing, or when a sustained strategy has no one left following it by the end of the horizon, the choices are to shorten the horizon, to simplify the policy into something the data supports, or to decline the emulation and say so.

The aspirin emulation did not fail because the database was inadequate. It failed because nobody wrote down which trial the analysis was standing in for. Nothing forced anyone to notice that the treated group had been chosen with the help of the future.