The Role Of Prior Outcomes In Later Treatment Assignment

Why an Earlier Outcome Can Matter at the Next Treatment Decision

In longitudinal care, a treatment decision is often made after clinicians have observed how a patient is doing. A patient's response, symptom score, or laboratory result can influence whether treatment is started, continued, or changed. The same measurement may also predict the eventual clinical outcome. Thus, it can help determine who receives the next treatment and who is likely to have the final outcome.

The word “outcome” describes what a measurement records, not its causal role at every later time. A response measured after an earlier treatment can be a confounder of a subsequent treatment’s effect, provided it is associated with the later outcome and influences the later treatment choice. But it is not a baseline covariate for the effect of the earlier treatment: it was measured after that treatment and may itself have been changed by it.

Definition: Let $A_1$ denote an earlier treatment, $Y_1$ an outcome measured after $A_1$ but before a later treatment, $A_2$, and $Y_2$ the final outcome. The prior outcome $Y_1$ is a time-varying confounder for the effect of $A_2$ when it helps determine $A_2$ and is also related to $Y_2$, conditional on relevant measured history. Because $Y_1$ follows $A_1$, it is also a post-treatment variable with respect to $A_1$.

A simple causal structure is $A_1 \rightarrow Y_1 \rightarrow A_2 \rightarrow Y_2$, with an additional path $Y_1 \rightarrow Y_2$. The arrow from $Y_1$ to $A_2$ represents treatment selection based on the prior outcome; the arrow to $Y_2$ represents its prognostic role. These arrows need not mean that changing the recorded measurement itself would change the final outcome: $Y_1$ may also stand for underlying health status that the measurement reflects.

Worked Example: A Response Measurement Before a Treatment Change

Suppose a patient receives an initial treatment $A_1$. At the next visit, a response measurement $Y_1$ is recorded: $Y_1=1$ indicates poor response, and $Y_1=0$ indicates adequate response. A clinician is more likely to intensify treatment $A_2$ when $Y_1=1$. Poor response also predicts the final outcome $Y_2$.

The timing is $A_1$, then $Y_1$, then $A_2$, then $Y_2$. Since $Y_1$ is known before the $A_2$ decision, it can help explain why patients receive different $A_2$ values. Since $Y_1$ predicts $Y_2$, an unadjusted comparison of final outcomes by $A_2$ can mix the treatment contrast with differences in response status.

For the effect of $A_2$, $Y_1$ may therefore be a confounder. For the effect of $A_1$, however, $Y_1$ is not a baseline measure: it was recorded after $A_1$. Calling it “baseline” merely because it precedes the second treatment would confuse two different time origins.

Unequal Prior-Outcome Distributions Create Crude Associations

The following result makes the role of prior-outcome imbalance precise. Let $H$ be a binary prior outcome, such as poor versus adequate response. Suppose the final outcome $Y_2$ is binary and, within each $H$ stratum, its risk is the same for both values of $A_2$. Write this risk as $\mu_h=P(Y_2=1\mid H=h,A_2=a)$, which does not depend on $a$. If the treated and untreated groups have different proportions with $H=1$, their crude risks can still differ.

Result: Under the stated within-stratum equality, $$ P(Y_2=1\mid A_2=1)-P(Y_2=1\mid A_2=0) =(\mu_1-\mu_0)\{P(H=1\mid A_2=1)-P(H=1\mid A_2=0)\}. $$ Thus, the crude risk difference is the difference in prior-outcome risks multiplied by the imbalance in the prevalence of that prior outcome.

Proof. By the law of total probability,

P(Y_2=1\mid A_2=a) =\mu_1P(H=1\mid A_2=a)+\mu_0P(H=0\mid A_2=a).

Since $P(H=0\mid A_2=a)=1-P(H=1\mid A_2=a)$, this equals $\mu_0+(\mu_1-\mu_0)P(H=1\mid A_2=a)$. Subtract the expression for $a=0$ from the expression for $a=1$ to obtain the result. $\square$

Worked Example: A Crude Difference With No Within-Stratum Treatment Effect

Let $H=1$ indicate poor prior response. Suppose $P(H=1)=12/35$. The later treatment is more common among those with poor response: $P(A_2=1\mid H=1)=4/5$, while $P(A_2=1\mid H=0)=29/115$. Assume the final-outcome risks are $0.8$ for $H=1$ and $0.1$ for $H=0$, with no difference by $A_2$ within either stratum.

First calculate the joint proportions. For poor response, $P(H=1,A_2=1)=(12/35)(4/5)=48/175$, and $P(H=1,A_2=0)=12/35-48/175=12/175$. For adequate response, $P(H=0)=23/35$, so $P(H=0,A_2=1)=(23/35)(29/115)=29/175$, and $P(H=0,A_2=0)=86/175$.

The treated proportion is $(48+29)/175=77/175=0.44$, and the untreated proportion is $(12+86)/175=98/175=0.56$. The treated group’s event proportion is $0.8(48/175)+0.1(29/175)=41.3/175=0.236$. Its risk is therefore $0.236/0.44=59/110=0.53636\ldots$.

The untreated group’s event proportion is $0.8(12/175)+0.1(86/175)=18.2/175=0.104$. Its risk is $0.104/0.56=13/70=0.18571\ldots$. The crude risk difference is $59/110-13/70=27/77=0.350649\ldots$, or approximately 0.351.

Yet within $H=1$, both treatment groups have risk $0.8$, and within $H=0$, both have risk $0.1$. The crude difference arises because $P(H=1\mid A_2=1)=48/77$, whereas $P(H=1\mid A_2=0)=12/98$. It is not evidence of an $A_2$ effect in this constructed example.

When a Later-Treatment Contrast Can Be Identified

A prior outcome’s confounding role does not mean that every comparison adjusted for it is automatically causal. A causal interpretation requires assumptions about treatment assignment, the measurement history, and the treatment probabilities. The next result states a simple, discrete-history version for a later-treatment contrast.

Theorem: Fix an earlier treatment value $a_1$. Assume consistency, meaning that a person's observed $Y_2$ equals $Y_2(a_1,a_2)$ when that person receives $(A_1,A_2)=(a_1,a_2)$. Assume conditional exchangeability for the later treatment: $A_2$ is independent of $Y_2(a_1,a_2)$ given $A_1,Y_1,L_0$, where $L_0$ is measured baseline history. Assume positivity: every relevant history $(L_0=l,Y_1=y)$ among people with $A_1=a_1$ has positive probability of receiving $A_2=a_2$. Then, for histories with positive probability, $$ E[Y_2(a_1,a_2)\mid A_1=a_1,L_0=l,Y_1=y] =E[Y_2\mid A_1=a_1,L_0=l,Y_1=y,A_2=a_2]. $$

Proof. Conditional exchangeability implies that, within the specified history, the mean potential outcome under $a_2$ is the same among those who do and do not receive $a_2$. In particular,

E[Y_2(a_1,a_2)\mid A_1=a_1,L_0=l,Y_1=y] =E[Y_2(a_1,a_2)\mid A_1=a_1,L_0=l,Y_1=y,A_2=a_2].

Positivity ensures that this treatment subgroup exists in the history under consideration. By consistency, within that subgroup $Y_2(a_1,a_2)=Y_2$. Substitution gives the stated equality. $\square$

This result concerns comparisons at the later decision, within measured histories. To obtain a full-population effect of a treatment regime that also sets $A_1$, further assumptions and averaging over baseline and intermediate histories are needed. The result does not license treating $Y_1$ as a pre-$A_1$ confounder.

Worked Example: The Same Measure Is Post-Treatment and Predictive

Suppose $A_1$ is randomized, with $P(A_1=1)=1/2$. The probability of poor response $Y_1=1$ is $0.6$ under $A_1=1$ and $0.2$ under $A_1=0$. The probability of receiving $A_2=1$ is $0.8$ after poor response and $0.2$ after adequate response. Suppose the final-outcome risks do not depend on $A_2$: they are $0.8$ for $(A_1,Y_1)=(1,1)$, $0.3$ for $(1,0)$, $0.6$ for $(0,1)$, and $0.1$ for $(0,0)$.

Among those with $A_1=1$, the probability of later treatment is $0.6(0.8)+0.4(0.2)=0.56$. Among those with $A_1=0$, it is $0.2(0.8)+0.8(0.2)=0.32$. The response measurement predicts later treatment; it is observed before that decision.

The overall final-outcome risk under $A_1=1$ is $0.6(0.8)+0.4(0.3)=0.60$. Under $A_1=0$, it is $0.2(0.6)+0.8(0.1)=0.20$. Thus the risk difference for $A_1$ is $0.40$ in this setup. Within either response stratum, the risk difference comparing $A_1=1$ with $A_1=0$ is $0.20$: for poor response, $0.8-0.6=0.2$; for adequate response, $0.3-0.1=0.2$. The different overall and stratum-specific contrasts reflect that $A_1$ changes the distribution of $Y_1$.

The lesson is about time order and role, not a recommendation to adjust or not adjust for $Y_1$ in every model. $Y_1$ is available to predict $A_2$, but it is downstream of $A_1$. A comparison targeting the earlier treatment’s total effect must account for the fact that changing $A_1$ can change $Y_1$; simply treating $Y_1$ as an ordinary baseline covariate changes what is being compared.

Diagnostics, Alternatives, and Limitations

A useful first diagnostic is to lay out the timeline explicitly: when was each treatment assigned, when was the prior outcome measured, and when was the final outcome assessed? Then check whether the prior outcome predicts the next treatment and whether it is prognostic for the final outcome after accounting for measured history. These checks describe the observed data; they do not establish that all confounding has been removed.

Inspect treatment frequencies across prior-outcome and baseline-history strata. If some histories almost always receive one treatment, positivity may be weak; if a treatment is never observed for a history, the relevant conditional comparison cannot be estimated from those data without extrapolation. Also examine whether the outcome measure was recorded before the treatment decision in practice, not merely according to its nominal visit label.

Approach	What it uses	Main concern in this setting
Baseline-only adjustment	Pre-treatment covariates	May leave the later treatment confounded by the observed prior outcome.
Adjustment for prior outcome in a later-treatment comparison	Measured history available before $A_2$	Needs adequate confounder measurement, exchangeability, and positivity; it does not make $Y_1$ baseline for $A_1$.
Longitudinal g-methods, including marginal structural models	Repeated treatment and covariate histories	Can target regime effects under their assumptions, but cannot repair unmeasured confounding or unsupported treatment histories.

A common mistake is to reason, “$Y_1$ is measured before $A_2$, so it is a baseline variable and can be adjusted for in any treatment analysis.” The correction is to name the time at which “baseline” is defined. $Y_1$ precedes $A_2$, so it may be needed to address confounding of $A_2$. It follows $A_1$, so it is post-treatment for the earlier treatment’s effect.

Another mistake is to infer a causal treatment effect from a crude difference when the treatment groups have different prior-outcome distributions. The numerical example showed a crude difference of about $0.351$ despite no $A_2$ effect within either prior-response group. Conversely, finding little crude imbalance does not prove the absence of confounding: other measured or unmeasured features of health may still influence treatment and outcome.

Finally, recorded outcomes can be noisy proxies for the clinical state guiding treatment. Measurement error may leave residual confounding even after conditioning on the recorded value. The assumptions of consistency, conditional exchangeability, and positivity are substantive requirements, not consequences of including $Y_1$ in a regression.

Check Your Understanding

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

A symptom score is recorded after the first treatment and before the second. It predicts both the second treatment and the final outcome. What is its role for each treatment?
In the binary-stratum result, what makes the crude risk difference zero even if the prior outcome predicts the final outcome?
In the numerical example, why is the crude risk difference not the effect of $A_2$ within the response groups?
What does a history with no observations receiving $A_2=1$ imply for a conditional comparison at that history?
Why is it incorrect to call an outcome measured after $A_1$ a baseline covariate for the effect of $A_1$?

Solutions. (1) It may be a time-varying confounder for $A_2$, while remaining a post-treatment variable for $A_1$. (2) Either the outcome risks are equal across strata, so $\mu_1-\mu_0=0$, or the strata have equal prevalence in treated and untreated groups, so the prevalence difference is zero. (3) The stratum-specific risks are equal across $A_2$; the crude groups differ because their proportions with poor response differ. The correctly rounded crude difference is approximately $0.351$. (4) Positivity fails there, so the conditional outcome under $A_2=1$ cannot be learned from that history without extrapolation. (5) It was measured after $A_1$ and may be affected by $A_1$, so it is not a pre-treatment baseline measurement for that effect.

The Role Of Prior Outcomes In Later Treatment Assignment

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