What a Difference from a Target Trial Means
An observational emulation is designed around a specified target trial: its eligibility rules, treatment strategies, assignment procedures, follow-up, outcomes, and analysis plan. In practice, the available data and care setting may depart from that specification. Interpreting the resulting estimate requires asking which feature differs and what quantity the emulation actually estimates. A difference from a randomized trial is not, by itself, evidence of bias: it may reflect a changed population or intervention, imperfect outcome ascertainment, or failure to identify the intended causal effect.
For a treatment strategy \(a\), write \(Y^a\) for the outcome that would be observed under that strategy at the prespecified horizon. The target trial’s risk in its target population is \(R^*(a)=E^*[Y^a]\), where \(E^*\) denotes expectation over that population. Its risk difference comparing strategies \(1\) and \(0\) is \(\Delta^*=R^*(1)-R^*(0)\). An emulation may aim at this same contrast, or it may answer a different question because its population, treatment delivery, follow-up, or outcome measurement differs.
These categories can coexist, but they are not interchangeable. For example, using a broader eligible population can change the population-average effect even if the causal risks are correctly estimated for that broader population. Conversely, a poorly measured confounder can bias an estimate of the original target effect even when the protocol features appear aligned.
Four Dimensions to Compare
The comparison should be made feature by feature, not by treating “the randomized trial” as a single benchmark. The target trial is a specification; the emulation is an implementation in a particular data source. The following dimensions often explain why their reported contrasts differ.
- Population. Compare eligibility criteria, calendar time, setting, and the people represented by the data. If treatment effects vary across people, averaging over a different population can change the risk difference. A different population can also threaten identification if some target-population covariate profiles are absent from the emulation.
- Treatment delivery. Compare the target strategies with treatment actually represented in the emulation. Assignment to initiate treatment, initiation within a grace period, and sustained adherence are distinct interventions. If the emulation captures a policy of encouraging treatment rather than receipt of treatment, its contrast may be a policy effect rather than the effect of receipt.
- Follow-up. Compare time zero, the outcome horizon, administrative end of observation, and loss to follow-up. A six-month risk and a twelve-month risk are different quantities. Appropriate adjustment for censoring can recover a full-horizon risk under assumptions; merely observing outcomes for a different duration does not do so.
- Measurement. Compare how treatment, eligibility covariates, and outcomes are recorded. A different outcome definition or measurement instrument can change the observed endpoint. Error in covariates used for adjustment can instead compromise identification, even if the causal outcome is conceptually unchanged.
A fifth question runs across all four: does the analysis identify the estimand it claims to estimate? For an observational emulation, causal interpretation generally requires consistency with the stated strategies, adequate treatment positivity, and exchangeability given the measured history; handling loss to follow-up also requires appropriate assumptions. Randomization in a target trial addresses treatment assignment confounding by design, but it does not automatically make results transportable to a different population or repair mismatched outcome measurement.
Standardizing Across Populations
A simple result clarifies when a population difference changes a risk and how to translate between populations. Let \(S=1\) indicate membership in the emulation source and \(S=*\) membership in the target population. Let \(X\) be measured baseline covariates and define \(\mu_a(x)=E[Y^a\mid X=x,S=1]\). To transport this conditional risk to the target, assume conditional transportability, \(E[Y^a\mid X=x,S=*]=\mu_a(x)\), and positivity: every \(x\) occurring in the target population has positive probability in the source. Also assume the strategy \(a\) and outcome are consistently defined in both populations.
Proof. By iterated expectation in the target population, $$ E^*[Y^a]=E^*\!\left[E[Y^a\mid X,S=*]\right]. $$ Conditional transportability replaces the inner expectation by \(\mu_a(X)\), giving \(E^*[Y^a]=E^*[\mu_a(X)]\). The positivity condition ensures that the source data can inform \(\mu_a(x)\) at the target covariate values; it does not itself guarantee transportability. \(\square\)
The result explains why “adjusting for covariates” does not automatically make two population-average effects comparable. The conditional risks must be averaged over the population named by the estimand. If treatment effects vary over \(X\), changing the averaging distribution can change the contrast. If conditional transportability fails, standardizing source estimates is not enough.
Worked Example: A Different Covariate Mix
Suppose \(X\) is a binary risk group, and conditional risks under treatment strategies are the same in the source and target populations. The target population is 50% high-risk, while the emulation source is 80% high-risk. Under strategy 0, the risks are 0.10 for low-risk and 0.30 for high-risk people; under strategy 1, they are 0.05 and 0.20.
Target risks. Under strategy 0, \(R^*(0)=0.50(0.10)+0.50(0.30)=0.05+0.15=0.20\). Under strategy 1, \(R^*(1)=0.50(0.05)+0.50(0.20)=0.025+0.10=0.125\). The target risk difference is \(0.125-0.20=-0.075\).
Source risks. Under strategy 0, the source risk is \(0.20(0.10)+0.80(0.30)=0.02+0.24=0.26\). Under strategy 1, it is \(0.20(0.05)+0.80(0.20)=0.01+0.16=0.17\). The source risk difference is \(0.17-0.26=-0.09\).
Both contrasts use the same conditional risks; the population-average risks differ because the covariate distributions differ. Standardizing the conditional risks to the target mix recovers \(-0.075\), provided the stated transportability and support assumptions hold.
Decomposing a Reported Difference
A useful accounting device is to change one protocol component at a time while holding the others fixed. Let \(\theta(p,g,h,m)\) denote a specified risk or risk contrast under a common outcome mechanism, where \(p\) denotes the population distribution, \(g\) treatment delivery, \(h\) follow-up, and \(m\) measurement. Use stars for target-trial components and \(E\) for emulation components. The total difference can be written exactly as
Derivation. Add the four bracketed terms. Every intermediate quantity appears once with a plus sign and once with a minus sign, so they cancel. The remaining terms are precisely the emulation quantity minus the target quantity. This identity is arithmetic; it does not assert that the components are causally independent or that each bracket is uniquely attributable to a protocol feature. In general, the contributions depend on the order in which components are changed, because population and treatment delivery, for example, can interact.
For a causal interpretation of each bracket, the comparisons must be well-defined: one needs a common outcome mechanism and a clear definition of what changes while the other features are held fixed. If a difference in measurement also changes which people are eligible, a clean one-component comparison may not be available. The decomposition is then a diagnostic aid, not an automatic causal attribution.
Worked Example: Treatment Delivery Is Not the Assigned Strategy
Suppose the target contrast compares full receipt of strategies 1 and 0, with risks 0.10 and 0.20, respectively. In an emulation of two treatment policies, 80% of people in the policy-1 group receive strategy 1 and 20% receive strategy 0; in the policy-0 group, 10% receive strategy 1 and 90% receive strategy 0. Assume, for this calculation, that the risks depend only on the strategy received and that these proportions are otherwise comparable.
The target risk difference for full receipt is \(0.10-0.20=-0.10\). In the policy-1 group, the risk is \(0.80(0.10)+0.20(0.20)=0.08+0.04=0.12\). In the policy-0 group, it is \(0.10(0.10)+0.90(0.20)=0.01+0.18=0.19\). The policy risk difference is \(0.12-0.19=-0.07\).
The policy contrast is less negative than the full-receipt contrast because treatment delivery differs from the target strategies. It is not automatically a biased estimate of the policy effect. It is a different intervention contrast; confounding or other identification failures could still affect its estimate.
Follow-Up and Measurement Can Change the Endpoint
Follow-up differences should be interpreted relative to the outcome horizon. A target twelve-month cumulative risk is not generally interchangeable with a risk measured only among people still observed at six months. If follow-up is censored before twelve months, methods that account for censoring can target the twelve-month risk under their assumptions; otherwise, the reported quantity may be a selected risk among observed participants. In particular, “no recorded event” is not necessarily “no event.”
Worked Example: A Shorter Horizon
Assume, solely for illustration, a constant event hazard of \(0.02\) per month under strategy 0 and \(0.01\) per month under strategy 1, with complete follow-up and no competing events. Under a constant hazard \(\lambda\), the cumulative risk at time \(t\) is \(1-\exp(-\lambda t)\).
At six months, the risks are \(1-\exp(-0.02\cdot6)=1-\exp(-0.12)\approx0.1131\) and \(1-\exp(-0.01\cdot6)=1-\exp(-0.06)\approx0.0582\); the risk difference is about \(-0.0549\). At twelve months, they are \(1-\exp(-0.24)\approx0.2134\) and \(1-\exp(-0.12)\approx0.1131\); the risk difference is about \(-0.1003\). These are different horizon-specific effects, not competing estimates of the same risk difference.
Measurement differences also require precise interpretation. If the target outcome is the true event but the emulation records a misclassified outcome, the measured risk need not equal the true risk even when follow-up is complete. Conversely, if the target trial itself defines the outcome using the same imperfect instrument, reproducing that instrument may align the estimand more closely than replacing it with a different measure. The right comparison is with the protocol’s outcome definition, not with an abstract claim that one measure is “better.”
Worked Example: Misclassification Changes the Measured Contrast
Suppose the true risks are 0.20 under strategy 0 and 0.10 under strategy 1. The recorded outcome has sensitivity 0.80 and specificity 0.90 in both groups. For true risk \(r\), the probability of a recorded positive outcome is \(0.80r+0.10(1-r)\), because false positives occur with probability \(1-0.90=0.10\).
For strategy 0, the recorded risk is \(0.80(0.20)+0.10(0.80)=0.16+0.08=0.24\). For strategy 1, it is \(0.80(0.10)+0.10(0.90)=0.08+0.09=0.17\). The true risk difference is \(0.10-0.20=-0.10\), whereas the recorded risk difference is \(0.17-0.24=-0.07\). Thus even nondifferential misclassification has changed the contrast on the risk-difference scale.
Diagnostics, Alternatives, and Limits
A practical comparison begins with a protocol table and asks, for each feature, what the target trial specified, what the data actually record, and what the analysis estimates. Check eligibility and covariate distributions; verify that treatment timing and adherence correspond to the named strategies; plot or tabulate follow-up and missingness by strategy; and inspect outcome definitions, validation data, and measurement frequency. These checks identify mismatches; they do not prove causal identification.
The main alternatives answer different questions. Direct comparison reports the emulation estimate as defined, while explicitly stating its population, strategies, horizon, and measured outcome. Standardization or transport reweights conditional risks to a chosen population, when conditional transportability and support are credible. Protocol restriction narrows the analysis to people and periods that more closely match the target, potentially changing the target population and reducing precision. Sensitivity analysis varies assumptions about uncertain components, but cannot make unsupported data informative by itself.
A common mistake is to reason, “The emulation used a different population, so its estimate is biased relative to the trial.” That conclusion is too quick. If the emulation correctly estimates its own population-average effect, the estimate may be valid for that population but differ from the target-population effect. The correction is to name the estimand, examine effect variation and transport assumptions, and standardize if justified. The reverse mistake is to call every discrepancy “just a different estimand”: poor confounding control, informative loss to follow-up, or differential outcome error may instead bias an estimate of the intended quantity.
No decomposition can eliminate limitations in the underlying data. Lack of support means the target population includes covariate profiles for which the source offers no relevant information. Unrecorded treatment details may prevent defining the intended strategy. Incomplete outcome validation may leave measurement error uncertain. A transparent interpretation states which differences are observed, which assumptions permit correction, and which remain unresolved.
Check Your Understanding
For each question, identify the relevant distinction and then compare your reasoning with the solutions.
- An emulation has a higher proportion of high-risk patients than its target trial. What additional condition permits standardizing source risks to the target population?
- The target trial compares sustained treatment with no treatment, but the emulation contrasts two policies with incomplete adherence. Is the resulting contrast necessarily biased for the policy effect?
- An emulation reports a six-month risk, while the target trial specifies twelve months. Name one way to estimate the target horizon and one key concern if this is not done.
- With sensitivity 0.90 and specificity 0.95 in both groups, compute the recorded risk when true risk is 0.10.
- Why does the four-part decomposition not provide a unique causal attribution for each protocol difference?
Solutions. (1) Conditional transportability of the strategy-specific outcome risk given measured covariates, plus source support for target covariate profiles, is needed. Standardization alone does not establish these conditions. (2) No. The emulation may estimate the policy effect if its analysis identifies that policy contrast; it is not automatically estimating the sustained-treatment effect. Confounding or other failures can still bias it. (3) One can use a method that adjusts for censoring to estimate the twelve-month risk, assuming its censoring conditions hold. Without correction, the six-month risk is a different horizon-specific quantity, and incomplete follow-up may also select who contributes outcomes. (4) The recorded risk is \(0.90(0.10)+(1-0.95)(0.90)=0.09+0.045=0.135\). (5) The algebraic contribution of a component depends on which other components have already been changed; interactions mean the order can change the bracketed contributions, although their sum remains the same.