The Seven Components Of A Target Trial

Why Specify a Target Trial?

An observational data set records what happened under care as it was delivered. A causal question, however, asks what would happen under alternative treatment strategies. A target trial makes that comparison concrete by stating the trial one would ideally conduct, including who could enter, what strategies would be compared, and how outcomes would be measured. An observational analysis can then be designed to emulate that trial as closely as the data allow.

The protocol is not a guarantee that an observational estimate is causal. It makes the intended comparison explicit, exposes ambiguities, and helps reveal where data or assumptions are inadequate. Seven components organize this work: eligibility, treatment strategies, assignment, time zero, follow-up, outcomes, and analysis. They must fit together: a treatment contrast that depends on future information, for example, can conflict with the start of outcome follow-up.

The Seven Components and Their Connections

1. Eligibility criteria say which people could enter the target trial. Eligibility should be defined using information available at entry, rather than later events that are consequences of treatment or follow-up. The criteria determine the population to which the question applies. They should be specific enough that a person’s eligibility can be assessed at the trial’s entry point.

2. Treatment strategies state what participants would be assigned to do. Each strategy needs a sufficiently clear definition to distinguish it from the alternative. A comparison of “start treatment A at enrollment” with “start treatment B at enrollment” is more interpretable than a comparison of vague labels such as “treated” and “untreated.” Strategies may include rules about continued care, but those rules must be specified if they are part of the causal question.

3. Assignment procedures state how the trial would allocate eligible participants to strategies. In a randomized target trial, this includes the randomization procedure and allocation ratio. In an observational emulation, treatment received is generally not randomly assigned. The analyst must describe how the observed treatment groups arose and address the possibility that participant characteristics influenced both treatment and outcome. Assignment in the hypothetical trial and treatment selection in the data are different concepts.

4. Time zero is the common start point for eligibility, assignment, and follow-up. At that point, a participant must be eligible, their assigned strategy must be determined, and outcome observation must begin according to the protocol. Aligning these events helps ensure that the groups are compared from a common point, rather than giving one group a different opportunity to accumulate outcomes.

5. Follow-up specifies how long participants are observed and how observation ends—for example, at a fixed horizon, an outcome, death, or loss of data. A fixed horizon makes the timing of the outcome comparison explicit. If observation ends early for some people, the analysis must account for incomplete outcome information under assumptions appropriate to the censoring process.

6. Outcomes define the events or measurements used to assess the consequences of the strategies. The protocol should make clear what counts as an outcome and when it is assessed. The same outcome definition and observation window should be applied across strategies; otherwise apparent differences may reflect measurement or ascertainment rather than treatment.

7. Analysis specifies the causal contrast of interest and the procedure for estimating it. For example, a protocol might target the difference between the one-year risks under two strategies in the eligible population. Let \(Y^a\) denote the outcome that would be observed under strategy \(a\). A risk-difference estimand can be written \(E[Y^1]-E[Y^0]\), with the population over which the expectation is taken stated explicitly. The analysis plan also states how observed data will be used to estimate that contrast and how uncertainty will be quantified.

Assumptions Behind Causal Interpretation

The protocol clarifies the question, but causal interpretation of an observational estimate also requires assumptions. For a simple comparison of two strategies, the potential outcomes \(Y^1\) and \(Y^0\) represent each person’s outcomes under the respective strategies. Only one is observed for a person, so the unobserved counterfactual must be inferred from other participants and the design assumptions.

• Consistency: for a person who follows strategy \(a\), the observed outcome equals \(Y^a\). This is difficult to interpret if a strategy is too vague to identify which versions of treatment it includes.
• Conditional exchangeability: after conditioning on measured pre-treatment covariates \(X\), treatment choice is independent of the potential outcomes. In potential-outcome notation, this is \((Y^1,Y^0)\perp A\mid X\). It is an assumption, not something established merely by adjusting for a list of covariates.
• Positivity: within relevant covariate strata in the target population, each strategy has a positive probability of being received: \(0<P(A=a\mid X=x)<1\) for both strategies \(a\).
• No interference: one person’s outcome under a strategy does not depend on other people’s treatment assignments, unless such dependence is explicitly part of the treatment strategies and estimand.

These assumptions are not interchangeable. A clear eligibility rule does not ensure exchangeability, and adjustment for confounding does not resolve a lack of treatment overlap. Likewise, a protocol cannot make an ambiguous treatment strategy satisfy consistency by naming it more carefully after the data have been analyzed.

Time Zero and Future-Based Treatment Classification

Time-zero alignment deserves particular attention when treatment is defined using information recorded after follow-up begins. Suppose a study classifies participants as “treated” if they receive a prescription within 30 days after diagnosis, but counts deaths starting on the diagnosis date. A person classified as treated must be alive and observable until their actual prescription date. A person who dies before any prescription cannot later be classified as treated under this rule. Thus, the groups are defined using future information, and early deaths are necessarily excluded from the eventual-treated group.

This can create immortal-time bias for death: the interval before a person’s qualifying prescription is a period during which they must remain alive to be classified as treated. Counting deaths from diagnosis while assigning people retrospectively by future treatment can therefore make the eventual-treated group appear to have lower mortality, even if the strategy itself has no beneficial effect. The issue is not that every treated person must remain alive for the whole 30-day window. Someone prescribed on day 1 need not survive to day 30. The guaranteed interval is only up to that person’s actual prescription date.

Nor does future treatment classification mechanically guarantee an event-free interval for every outcome. A nonfatal event on day 10 does not necessarily prevent a prescription on day 20. If the protocol allows that person to qualify as treated, the person can have the event before treatment and still enter the eventual-treated group. Bias depends on the outcome and the precise treatment-classification rule: an earlier outcome creates a guaranteed event-free interval only when that outcome, or a rule requiring event-free survival, prevents later qualification for treatment.

A protocol should therefore make the time origin and treatment strategies coherent. For example, if the scientific question concerns initiation at diagnosis, define strategies that can be assigned at diagnosis and compare them from that time. If treatment is allowed to begin during a grace period, the analysis must respect the strategies and their timing rather than naively grouping people by future initiation. The suitable design and analysis depend on that specification.

Putting the Components Together

The components are best checked as a connected design, not as seven unrelated fields to fill in. In particular, ask whether eligibility is known at time zero, whether the strategies could be assigned at that time, and whether outcome observation begins comparably in both groups. Then check whether the outcome and horizon answer the stated question, and whether the planned estimator targets the intended population and contrast.

Diagnostics, Alternatives, and Limits

Protocol diagnostics are checks for mismatches that can invalidate or change the question, rather than a single numerical test. Look for treatment status defined by future events, eligibility assessed after the start of outcome counting, different outcome ascertainment across groups, and an analysis population that differs from the population named in the estimand. In the observed data, also inspect whether both strategies occur across the relevant covariate patterns; if some types of eligible people almost always receive one strategy, positivity may be doubtful.

The main alternative is not simply “use regression instead.” A randomized target trial assigns strategies by design; an observational emulation must rely on measured data and assumptions to handle treatment selection. Propensity score methods and outcome-regression approaches are possible analytic tools for specified observational contrasts, but neither repairs a poorly defined protocol or unmeasured confounding by itself. The protocol is also distinct from a particular estimator: the same target contrast may be approached with different methods, each with its own requirements.

A target trial cannot recover information that was never recorded. If the data lack treatment timing, a required covariate, or a valid outcome measure, an emulation may be impossible or may answer a narrower question. Nor does a well-written protocol prove consistency, exchangeability, positivity, or correct outcome measurement. Its value is to make these requirements visible and to prevent a numerical result from being mistaken for an answer to a question the data did not support.

Common Mistakes

• Mixing the hypothetical assignment with observed treatment. An observational study does not become randomized because its protocol describes random allocation. State what the target trial would do and separately explain how treatment arose in the data.
• Starting outcome counting before future-based group classification is resolved. This can create an immortal interval for death or another outcome that prevents later treatment qualification. Assess the exact outcome and rule; do not claim that every outcome is mechanically event-free before treatment.
• Calling an estimator an estimand. A model or matching procedure is a way to estimate a target, not a complete statement of the target. Name the population, strategies, outcome, horizon, and contrast.
• Treating a protocol as proof of identification. Clear specifications improve design but do not establish the observational assumptions required for causal interpretation.