Subsequent Therapy and the Target Treatment Effect

Why the Target Effect Depends on Subsequent Therapy

After randomization, a participant may begin another treatment before the endpoint is measured. The new therapy might be started because the assigned treatment was ineffective, poorly tolerated, or no longer appropriate. It can then affect the endpoint directly. Consequently, the observed outcome reflects both randomized assignment and what happened afterward.

The analysis question is not simply whether to “adjust for” subsequent therapy. It is first to decide which treatment effect is relevant. A treatment-policy question asks about the effect of assignment in a setting where subsequent therapy may occur as it does in practice. A hypothetical question asks what the effect of assignment would have been if subsequent therapy had not been initiated. These are distinct target effects, even when they use the same participants, endpoint, and follow-up time.

Definition: Let \(A\) denote randomized assignment, with \(A=1\) for the experimental treatment and \(A=0\) for control. Let \(S^a\) describe whether, under assignment \(a\), a participant would initiate subsequent therapy before the endpoint, and let \(Y^{a,S^a}\) denote the endpoint under assignment \(a\) and the subsequent-therapy course that would naturally follow it. The treatment-policy effect on a mean-difference scale is \(\theta_{\mathrm{TP}}=E(Y^{1,S^1})-E(Y^{0,S^0})\). The hypothetical no-initiation effect is \(\theta_{\mathrm{H}}=E(Y^{1,0})-E(Y^{0,0})\), where \(Y^{a,0}\) is the endpoint that would occur under assignment \(a\) if subsequent therapy were not initiated. These definitions assume that higher endpoint values are better; reverse the contrast or interpretation when lower values are better.

The treatment-policy effect is about the randomized treatment strategies as implemented, including the subsequent care that follows each assignment. It is not necessarily the pharmacologic effect of remaining on the assigned treatment. The hypothetical effect concerns a different intervention: assignment to each trial arm while preventing subsequent therapy through the endpoint. It does not mean “the effect among participants who happened not to start therapy,” because that group is selected after randomization.

Specify the Event and the Counterfactual Question

A usable estimand requires a precise event definition. State which therapies count as subsequent therapy, when initiation is considered to occur, and the period during which initiation matters. For example, “any systemic treatment for the same condition begun after the assigned study drug is stopped and before the week-24 assessment” is more operational than “additional treatment.” Different drugs, indications, or timing rules may represent meaningfully different events.

The target should also specify the endpoint and its measurement time. For a continuous symptom score, the hypothetical question might be the mean week-24 score under each randomized assignment if no qualifying subsequent therapy were started before week 24. A trial should not silently change that question to an effect during treatment or to an effect among therapy non-initiators. Other estimand attributes, such as the target population and population-level summary, should remain explicit as established in the earlier material on the five attributes of a clinical trial estimand.

Worked Example: The Assignment Effect When Therapy Is Allowed

Hypothetical data. In a trial, higher week-24 symptom-function scores are better. There are 100 participants in each randomized arm. Subsequent therapy is started by 30 experimental-arm participants and 20 control-arm participants. The observed total scores, including scores collected after therapy initiation, are 6,600 in the experimental arm and 6,000 in control.

For the treatment-policy effect, retain each participant’s week-24 outcome regardless of subsequent-therapy initiation. The arm means are

\bar{Y}_{1,\mathrm{obs}}=\frac{6600}{100}=66,\qquad \bar{Y}_{0,\mathrm{obs}}=\frac{6000}{100}=60.

The observed mean difference is \(66-60=6\) score points in favor of assignment to the experimental treatment. In a randomized trial, this contrast targets the treatment-policy effect when outcomes are measured as specified and the usual consistency and follow-up requirements hold. It includes the consequences of the different subsequent-therapy patterns in the two arms.

This calculation does not tell us the hypothetical no-initiation effect. The 6-point difference cannot be relabeled as the effect that would have occurred had nobody started subsequent therapy: outcomes after therapy initiation may have changed, and the people who initiated therapy may differ prognostically from those who did not.

What Randomization Does—and Does Not—Identify

Randomization makes treatment assignment independent of participants’ potential outcomes at baseline. With consistency—meaning the observed outcome equals the potential outcome corresponding to the assignment and subsequent-therapy course actually experienced—and no interference between participants, the observed arm mean identifies the treatment-policy mean:

E(Y\mid A=a)=E(Y^{a,S^a}\mid A=a)=E(Y^{a,S^a}).

The first equality uses consistency. The second uses random assignment. Taking the difference between the two randomized-arm means therefore identifies \(\theta_{\mathrm{TP}}\), subject to complete and appropriate outcome ascertainment. This is the key justification for using the randomized comparison for a treatment-policy question.

For the hypothetical effect, randomization alone is not enough. Subsequent-therapy initiation occurs after assignment and may depend on evolving symptoms, response, adverse effects, or other prognostic information. Among participants with the same assignment, those who start therapy can therefore have different potential outcomes from those who do not. Simply excluding initiators, censoring them, or comparing observed non-initiators breaks the protection of baseline randomization.

Identification conditions for a simple hypothetical analysis: In addition to consistency and randomization, a one-decision formulation generally requires (1) conditional exchangeability of initiation: after conditioning on measured pre-initiation history \(L\), initiation is not associated with the potential endpoint under no initiation; and (2) positivity: at each relevant history and assignment, there is a nonzero chance of not initiating subsequent therapy. The history \(L\) must include relevant prognostic information measured before the initiation decision. These assumptions are not guaranteed by randomization.

For a single initiation decision with history \(L\) measured beforehand, the hypothetical mean under assignment \(a\) can be identified by standardizing the no-initiation outcomes over the history distribution under that assignment:

E(Y^{a,0}) = \sum_l E(Y\mid A=a,L=l,S=0)\,P(L^a=l).

Here \(P(L^a=l)\) is the distribution of the pre-initiation history that would arise under assignment \(a\), whether or not the participant later starts therapy. The conditional mean among observed non-initiators stands in for the no-initiation outcome at that history only under conditional exchangeability and consistency. Positivity is needed so that those conditional means are informed by participants who did not initiate therapy at each relevant history. With repeated decisions or time-varying histories, the corresponding identification argument must account for the sequence of histories and decisions; this one-decision expression is not automatically adequate.

Why Restricting to Non-Initiators Can Mislead

Worked Example: Selection Changes the Comparison

Hypothetical data. Suppose the target population has equal proportions of low- and high-risk participants. Within each risk group, the mean score under no subsequent therapy would be 82 and 62 points, respectively, for experimental assignment, and 78 and 58 points for control. Thus, the no-initiation treatment difference is 4 points in each risk group.

Assume the observed participants who did not initiate subsequent therapy are distributed differently by risk: in the experimental arm, 20 are low-risk and 20 are high-risk; in control, 80 are low-risk and 20 are high-risk. Their unstandardized mean scores are

\bar{Y}_{1,S=0}=\frac{20(82)+20(62)}{40} =\frac{2880}{40}=72,

\bar{Y}_{0,S=0}=\frac{80(78)+20(58)}{100} =\frac{7400}{100}=74.

The restricted comparison is \(72-74=-2\) points, apparently favoring control. But the groups have different risk compositions because initiation is related to post-randomization circumstances. That comparison does not estimate the no-initiation effect in the target population.

Standardizing both arms to the target population’s 50% low-risk and 50% high-risk distribution gives

\mu_{1,0}=0.5(82)+0.5(62)=72,\qquad \mu_{0,0}=0.5(78)+0.5(58)=68,

so the hypothetical contrast is \(72-68=4\) points. This standardization recovers the target only if the risk groups capture the relevant confounding of initiation and outcome, the values are measured before initiation, and positivity and consistency hold. The example shows why dropping initiators is not equivalent to setting initiation to “no” for everyone.

Worked Formulation and Standardization

Worked Example: A Hypothetical Effect With Measured History

Hypothetical data. In a second illustration, the target population is 60% low-risk and 40% high-risk before the subsequent-therapy decision. For simplicity, this history distribution is the same under either randomized assignment. Among participants who did not start subsequent therapy, the mean scores are 74 and 60 for low- and high-risk participants assigned experimental treatment, and 68 and 50 for the corresponding control participants. Assume the risk category is measured before initiation, captures all relevant prognosis for the decision, and both initiation choices are possible in each category.

The hypothetical mean under experimental assignment is calculated by applying the target risk distribution to the no-initiation conditional means:

E(Y^{1,0})=0.60(74)+0.40(60)=44.4+24=68.4.

For control,

E(Y^{0,0})=0.60(68)+0.40(50)=40.8+20=60.8.

The standardized hypothetical effect is \(68.4-60.8=7.6\) score points in favor of experimental assignment under the no-initiation scenario. The arithmetic is straightforward; the substantive work is defending the assumptions that let the observed no-initiation outcomes represent the counterfactual outcomes for everyone. If important prognostic reasons for initiation were not measured, this calculation may not identify the intended effect.

Diagnostics, Alternatives, and Limitations

Diagnostics cannot prove the identification assumptions, but they can reveal problems that make a hypothetical interpretation less credible. Examine how initiation rates vary across arms and across measured prognostic histories. Check whether some history groups have few or no non-initiators; such gaps indicate weak or failed positivity and make standardization rely heavily on extrapolation. Review whether the recorded history captures the information available when therapy decisions were made, and whether initiation dates, treatment definitions, and endpoint timing are sufficiently complete.

Large differences between treatment-policy and hypothetical results may be clinically meaningful: subsequent therapy may materially alter outcomes, or the hypothetical analysis may be sensitive to its assumptions. They are not, by themselves, proof that either target is wrong. Sensitivity to unmeasured prognostic factors and to the definition of “no subsequent therapy” should be considered when a hypothetical effect is central to the decision.

Target question	How subsequent therapy is handled	Interpretation
Treatment policy	Include outcomes regardless of initiation	Effect of randomized assignment with subsequent care occurring as it does under each assignment
Hypothetical no initiation	Target outcomes under a specified scenario in which initiation is prevented	Counterfactual effect under that scenario, requiring additional identification assumptions
Observed non-initiators only	Restrict the analysis to participants who did not initiate	A selected-group comparison; it is not automatically either target effect

The treatment-policy contrast is often the more direct answer when the decision concerns assignment in usual care and subsequent therapy is part of that care. The hypothetical contrast may be useful when the scientific question specifically concerns outcomes without subsequent therapy, but it depends on assumptions that cannot be secured by randomization alone. A composite strategy instead changes how the event or outcome is represented, while a principal-stratum question targets a post-randomization subgroup; neither should be substituted for a no-initiation hypothetical question without changing the clinical interpretation.

Common Mistakes

Calling an observed randomized comparison a no-subsequent-therapy effect. The randomized comparison that retains post-initiation outcomes targets the treatment-policy effect, not automatically the hypothetical effect.
Dropping everyone who initiates therapy. Initiation may depend on prognosis and response, so this creates selected groups that need not remain comparable.
Adjusting for initiation as if it were a baseline covariate. Initiation is post-randomization and may be related to evolving outcomes. Adjustment requires a clearly specified target and appropriate assumptions, not routine covariate adjustment.
Leaving “no subsequent therapy” vague. The counterfactual scenario must define which therapies are prevented and during what period; otherwise the target is not well specified.

Key takeaway: Treatment-policy and hypothetical effects answer different questions. Randomization directly supports the effect of assignment with subsequent therapy included as it occurs; a hypothetical effect without initiation requires explicit counterfactual definition and additional assumptions about the process governing initiation.

Check Your Understanding

Answer each question, then compare your reasoning with the solutions.

A trial retains week-16 outcomes for everyone, including participants who start another therapy. Which target does the randomized arm comparison address?
Why does randomization not, by itself, identify the effect that would occur if no participant started subsequent therapy?
In a hypothetical standardization, the target population is 25% low-risk and 75% high-risk. Under no initiation, experimental means are 80 and 56, and control means are 76 and 50. Calculate the standardized contrast.
Name two assumptions needed to use observed outcomes among non-initiators to identify a hypothetical no-initiation effect.

Solutions. (1) The treatment-policy effect, because outcomes are included regardless of subsequent-therapy initiation. (2) Initiation occurs after randomization and may depend on prognosis or evolving response, so randomized assignment does not make initiators and non-initiators comparable. (3) Experimental mean \(=0.25(80)+0.75(56)=20+42=62\); control mean \(=0.25(76)+0.75(50)=19+37.5=56.5\). The standardized contrast is \(62-56.5=5.5\) outcome units in favor of experimental assignment. (4) Examples are conditional exchangeability of initiation given measured pre-initiation history, positivity of not initiating at relevant histories, and consistency of the defined no-initiation scenario.