From a Trial Question to an Emulation Plan
A nontrial comparison is easier to interpret when its design begins with a trial that could, in principle, have been conducted. That hypothetical trial makes explicit who would be eligible, which treatment strategies would be compared, when follow-up would begin, and how outcomes would be defined. The observational analysis then asks how closely available nontrial data can reproduce those design choices. Writing down the protocol first helps expose mismatches before an outcome comparison is calculated.
This is the central task of target trial emulation: specify a hypothetical trial and map its design onto the records and treatment choices actually observed. Emulation is a design discipline, not a guarantee that the resulting comparison has the protection against confounding provided by random assignment. It also does not make an unsuitable data source suitable; whether a source can support the required definitions is a separate assessment.
The protocol should be written before inspecting comparative outcomes. Otherwise, choices such as who counts as eligible or what counts as an outcome may be influenced, even unintentionally, by the observed results. The aim is not to claim that observational data are randomized. It is to make the intended comparison and its departures from a randomized design inspectable.
The Protocol-to-Data Map
A useful protocol describes the same core elements that would be specified for a randomized trial. In an emulation, each element must also have an operational rule: a rule that can be applied to the nontrial records without using future information to define baseline status.
Define the clinical population and the point at which eligibility is assessed. Specify criteria that can be determined using information available by that point.
State the alternatives precisely enough to distinguish them in the data. A strategy may describe starting a specified treatment, a comparator strategy, or a treatment policy over time.
In the hypothetical trial, state how eligible people would be assigned. In the emulation, state how observed treatment records identify the corresponding strategy group. These are not the same mechanism: observational treatment choices are not randomized assignment.
Set the common start of eligibility, treatment assignment or classification, and outcome follow-up. State which recorded date represents that point for each person.
Specify the follow-up horizon and when observation ends, and define the outcome in operational terms. The emulation must apply compatible rules in each strategy group.
The previous material on the external-control estimand concerns the quantity the comparison is intended to estimate. The protocol map adds a design blueprint for making that quantity correspond to a well-defined trial question. A clearly stated estimand cannot rescue an emulation in which one group starts follow-up at treatment initiation and the other starts months earlier.
Several causal assumptions are relevant to interpreting the resulting comparison. Consistency means that, for a person who follows a specified strategy, the observed outcome corresponds to that strategy’s potential outcome; this requires the strategy to be defined clearly enough to avoid materially different versions being treated as identical. Conditional exchangeability means that, conditional on measured baseline covariates, strategy choice is independent of the potential outcomes being compared. Positivity means that, at each relevant covariate pattern, there is a positive probability of receiving each strategy under comparison. A no-interference assumption additionally rules out one person’s treatment changing another person’s outcome in a way relevant to the analysis. These assumptions are not established merely by writing a protocol; they require substantive justification and suitable data.
Worked Examples
Worked Example: Specifying a Hypothetical Trial for a Treatment Initiation Question
Suppose a hypothetical, two-arm trial would compare initiating Drug A with initiating standard therapy among adults with a specified condition who have not previously received either treatment. The primary outcome is whether a hospitalization for the condition occurs within 180 days. Translate that question into an emulation outline.
Eligibility. Define the population as adults who meet the condition definition, have no prior use of either treatment under the protocol’s look-back rule, and are eligible for both strategies at the treatment decision. Eligibility is assessed on the date of that decision, not on a date selected later because an outcome occurred.
Strategies and assignment. The trial would assign each eligible person to initiate Drug A or standard therapy. In nontrial records, the emulation classifies people according to which strategy they actually initiate at the decision point. That observed classification does not imply random assignment. If treatment can be delayed or the recorded date is ambiguous, the protocol and the available records may not match well enough to implement this rule.
Time zero and follow-up. Set time zero to the eligible treatment decision and begin follow-up on that same date for both groups. Follow each person for 180 days, subject to a prespecified end-of-observation rule. Define the outcome as at least one qualifying hospitalization during that interval.
Numerical illustration. Assume, hypothetically, that the emulation identifies 120 people initiating Drug A and 120 initiating standard therapy, with complete observation through day 180. Suppose 18 and 30 people, respectively, have at least one qualifying hospitalization. The observed risks are
In this hypothetical data set, the observed 180-day hospitalization risk is 10 percentage points lower in the Drug A group. This is a descriptive comparison, not evidence by itself that Drug A caused the difference: treatment choice may reflect baseline prognosis, and the assumptions needed for a causal interpretation have not been demonstrated.
Worked Example: Why Eligibility and Follow-Up Need the Same Time Zero
Suppose a hypothetical protocol asks about starting a new treatment at the date a patient first meets eligibility. An analyst instead classifies people as treated if they start the drug within 30 days after eligibility, but begins follow-up on the eligibility date. Consider 100 people classified as treated under this rule. For illustration, assume 20 have an outcome during the first 30 days, before starting; 80 remain outcome-free and start on day 30; and 12 of those 80 have an outcome during the following 90 days.
If the protocol’s treatment strategy is initiate at time zero, the 20 people who experience an outcome before starting did not follow that strategy at the required time. If the analyst nevertheless assigns them to the treated group because they started later, the group definition uses future treatment information. In this example, the observed treated-group count over the full 120 days is \(20+12=32\) outcomes among 100 people, or
But that fraction combines outcomes occurring before treatment initiation with outcomes after initiation; it does not represent risk under a strategy of initiating at time zero. If the target strategy instead allows initiation at any time within 30 days, that grace period must be part of the protocol and implemented consistently, rather than silently added to the data rule.
The design issue is temporal: future survival or outcome-free time must not be used to decide who belonged to a strategy group at baseline. For a strategy requiring immediate initiation, the eligibility date, strategy classification, and follow-up start should coincide. For a strategy with a permitted delay, a method must handle the interval in a way that corresponds to that defined strategy. The count of 32 is calculated correctly for the stated, flawed grouping rule, but it answers neither question cleanly.
Worked Example: Making a Fixed-Horizon Outcome Rule Operational
Consider a hypothetical emulation comparing two strategies, with the outcome defined as a first qualifying hospitalization within 90 days after time zero. Among 50 people in Strategy A, 7 have an event by day 90. Among 50 in Strategy B, 11 have an event by day 90. Assume all 100 have outcome information through day 90 and that the event definition is applied identically.
The observed risks and risk difference are
Thus the observed 90-day risk is 8 percentage points lower in Strategy A. This calculation is interpretable as a comparison of risks under the stated horizon because the example stipulates complete, common follow-up and a common outcome rule. In real nontrial records, those stipulations require scrutiny: people may leave observation early, and the recorded event may not map perfectly to the protocol’s clinical definition. Those issues cannot be repaired by arithmetic alone.
Why Time Alignment Matters
The central timing requirement can be justified directly. Let \(E_i\) be the date person \(i\) first satisfies eligibility, \(A_i\) the date the observed treatment strategy is assigned or initiated under the emulation rule, and \(F_i\) the date follow-up begins. A simple baseline-initiation protocol intends these events to occur at one common decision point:
If follow-up begins at eligibility but strategy membership is determined by a later initiation, group membership depends on what happens after follow-up has already started. A person who must remain alive and outcome-free until initiation has, by definition, contributed such time to the group. This creates a period in which the later-treated group is selected using future information. Conversely, starting one group’s follow-up at initiation and another group’s at eligibility gives the groups different risk windows. Either mismatch changes the comparison from the protocol question.
The equality above is not a claim that every treatment strategy must require same-day initiation. A protocol may explicitly allow a grace period or describe ongoing treatment. The justification is that the start of eligibility, strategy assignment, and outcome assessment must have a coherent relationship specified in advance. If they cannot be aligned exactly, the discrepancy and the method used to represent the strategy need to be explicit.
Diagnostics, Alternatives, and Limits
Before estimating a contrast, inspect whether each protocol element can actually be implemented. Useful design checks include asking whether every person’s eligibility can be assessed using information available at time zero, whether the treatment strategies can be distinguished as specified, whether the chosen time origin is recorded comparably in both groups, and whether the outcome window is the same. Check also that the protocol does not define one group using post-baseline information while treating the other as a baseline group.
Several warning signs deserve particular attention:
- Different clinical entry points. If one group enters follow-up at diagnosis and another at treatment initiation, their time at risk may not represent the same clinical decision.
- Eligibility defined with future facts. Requiring a person to survive, remain event-free, or persist in care for a period after time zero can select people based on post-baseline experience.
- Vague strategies. Labels such as “usual care” or “treated” can combine materially different actions. If the observed records cannot distinguish the intended alternatives, the emulation may not correspond to the protocol.
- Outcome rules that vary by group. Different code lists, observation windows, or event-counting rules can produce an apparent difference even when underlying clinical outcomes are comparable.
- Thin support for a strategy. If some clinically relevant patient profiles appear only in one strategy group, the positivity assumption may fail for those profiles; a model cannot create genuine comparative information where none exists.
A randomized trial is the main alternative when it is feasible and appropriate: random assignment is designed to balance measured and unmeasured baseline causes of treatment choice in expectation. A target-trial emulation uses observed treatment choices and therefore requires additional justification for exchangeability, alongside clear alignment of protocol and data. A naive historical comparison may use earlier outcomes without explicitly aligning eligibility, treatment decision, and follow-up; emulation makes those design choices visible but does not automatically remove calendar-time differences or unmeasured confounding. Bayesian borrowing can quantify how external information contributes to an analysis, but it does not fix a poorly specified or noncomparable emulation.
The method has limits. A written protocol cannot recover variables that were never recorded, establish that treatment groups are exchangeable, or make an outcome measure valid by definition. A carefully planned emulation can clarify what the data do and do not represent; it cannot convert observational assignment into randomization. Conclusions should therefore distinguish the observed contrast from a causal interpretation and state the assumptions that connect them.
Common Mistakes
- Wrong reasoning: “The treated patients eventually received the drug, so they can be called treated from the date they first qualified.” Correction: Classification by later treatment uses future information. Define a strategy and time zero that make membership meaningful from the start, including an explicit approach if a grace period is part of the strategy.
- Wrong reasoning: “Both groups have the same number of follow-up days, so their outcomes are comparable.” Correction: Equal duration alone is insufficient if the groups start from different clinical decision points or use different eligibility and outcome rules.
- Wrong reasoning: “A target-trial protocol removes confounding.” Correction: The protocol clarifies the comparison; causal interpretation still depends on assumptions such as conditional exchangeability, consistency, and positivity.
Check Your Understanding
Answer each question, then compare your reasoning with the solutions below.
- What is the difference between the target trial’s assignment procedure and treatment classification in an emulation?
- A study defines the treated group by starting therapy within 14 days after eligibility but begins follow-up on eligibility day. What is the design concern?
- Name two assumptions needed for a causal interpretation of an emulated comparison, and state each briefly.
- In a hypothetical comparison, 9 of 60 people in one group and 15 of 60 in another experience the outcome by day 90. Calculate the observed risk difference, first group minus second group.
- Why is a common outcome definition important even if both strategy groups have the same follow-up duration?
Solutions. 1. The target trial specifies how random assignment would occur; the emulation classifies people from observed treatment records, which are not randomized. 2. Group membership depends on treatment initiation after follow-up starts, so it uses future information and may include pre-initiation time in the treated group. The strategy and time origin need to be specified coherently. 3. For example, conditional exchangeability requires no residual association between strategy choice and potential outcomes after conditioning on measured baseline covariates; positivity requires a positive probability of each strategy at relevant covariate patterns. 4. The risks are \(9/60=0.150\) and \(15/60=0.250\); the risk difference is \(0.150-0.250=-0.100\), or 10 percentage points lower in the first group. This is an observed comparison, not automatically a causal effect. 5. Different event rules can count different outcomes, so a difference could reflect measurement rather than a difference in the clinical outcome of interest.