Confounding By Indication Across Repeated Treatment Decisions

Why Indication Can Recur at Every Visit

Treatment is often prescribed because a patient’s current condition calls for it. A patient whose symptoms worsen may be more likely to receive treatment and more likely to have a poor outcome, even if the treatment itself helps. This is confounding by indication: the clinical reason for treatment also carries information about prognosis.

With repeated decisions, the relevant indication can change over time. A patient’s current symptoms may reflect disease progression, earlier treatment, or both. Those symptoms can then influence the next treatment decision and predict the eventual outcome. Comparing patients according to treatment received at one visit, or adjusting only for baseline status, can therefore leave later indications unaccounted for.

Use $A_t$ for treatment at visit $t$, $L_t$ for measured clinical status just before that visit’s treatment decision, and $Y$ for the eventual outcome. Write $\bar A_t=(A_1,\ldots,A_t)$ and $\bar L_t=(L_1,\ldots,L_t)$ for treatment and covariate histories. A history available just before the decision at visit $t$ includes prior treatments and current pre-treatment covariates; it must not include measurements taken after $A_t$.

Definition: Confounding by indication at visit $t$ occurs when clinical information available before $A_t$ helps determine treatment and is also prognostic for the outcome. Across repeated decisions, the indication may change: a later $L_t$ can predict $A_t$ and $Y$, while also having been affected by earlier treatment.

The key timing distinction is that $L_t$ is measured before $A_t$, whereas $L_{t+1}$ follows $A_t$. Thus $L_t$ can be an indication for the current treatment, while its value may also carry consequences of earlier treatment. The earlier material on treatment-confounder feedback describes why that ordering matters for adjustment.

A Simple Bias Calculation

The basic distortion can be derived without a complicated model. Fix the history before a treatment decision, denoting it by $H$, and suppose $S$ is a binary symptom measured before that decision but not included in $H$. Consider the additive conditional mean model

E[Y\mid A,S,H]=\alpha(H)+\tau A+\gamma S.

Here $\tau$ is the treatment contrast at a fixed symptom level and history; $\gamma$ is the symptom’s prognostic contribution. Assume this conditional mean model is correct and the relevant expectations are finite.

Result: Within a fixed history $H$, the observed treated-minus-untreated mean difference is $$ E[Y\mid A=1,H]-E[Y\mid A=0,H] =\tau+\gamma\{P(S=1\mid A=1,H)-P(S=1\mid A=0,H)\}. $$

To verify the identity, take the conditional expectation of the model separately in the two treatment groups:

\begin{aligned} E[Y\mid A=1,H] &=\alpha(H)+\tau+\gamma E[S\mid A=1,H],\\ E[Y\mid A=0,H] &=\alpha(H)+\gamma E[S\mid A=0,H]. \end{aligned}

Subtracting cancels $\alpha(H)$. Since $S$ is binary, $E[S\mid A=a,H]=P(S=1\mid A=a,H)$, giving the stated expression. If severe symptoms increase the outcome ($\gamma>0$) and are more common among treated patients, the second term is positive. The observed contrast is then less favorable than $\tau$ when lower outcomes are beneficial. This calculation describes an association; interpreting $\tau$ causally also requires appropriate causal assumptions.

Worked Example: A Symptom-Driven Treatment Decision

At a visit, suppose half of patients have severe symptoms. Clinicians treat 80% of patients with severe symptoms and 20% of those without severe symptoms. Let the outcome be a symptom score for which lower is better, with conditional mean $E[Y\mid A,S]=10+4S-3A$. Find the observed treatment contrast and compare it with the fixed-symptom treatment contrast.

The treated proportion is $0.5(0.8)+0.5(0.2)=0.5$. Among treated patients, the proportion with severe symptoms is $0.5(0.8)/0.5=0.8$. The untreated proportion is also $0.5$, and the severe-symptom proportion among untreated patients is $0.5(0.2)/0.5=0.2$.

The treated mean is $10+4(0.8)-3=10.2$. The untreated mean is $10+4(0.2)=10.8$. The observed difference is $10.2-10.8=-0.6$, while the treatment contrast at either fixed symptom level is $-3$. Equivalently, the bias identity gives $-3+4(0.8-0.2)=-0.6$. The treatment appears to help by only 0.6 points in the crude comparison because the treated group contains more severely symptomatic patients.

How the Indication Changes Across Visits

Repeated decisions add a second source of structure: an earlier treatment may change the clinical status that prompts a later treatment. For example, effective initial therapy might reduce symptoms, while persistent or recurrent symptoms could lead clinicians to intensify treatment. At the later visit, comparing $A_2=1$ with $A_2=0$ without accounting for $L_2$ compares patients with different indications. Adjusting for baseline status alone does not generally make those current indications alike.

The sequential exchangeability assumption gives a precise way to describe what would be needed for measured histories to contain the relevant indications. Let $Y^{\bar a}$ denote the outcome that would occur under treatment sequence $\bar a$. At each decision $t$, sequential exchangeability requires, for every treatment sequence of interest,

A_t \mathbin{\perp\!\!\!\perp} Y^{\bar a}\mid \bar A_{t-1},\bar L_t.

This is an assumption, not a consequence of having measured many covariates. It says that, among patients with the same measured past treatments and covariate history, the current treatment assignment carries no further information about the potential outcome. It can fail if clinicians act on unrecorded severity, if symptoms are measured poorly, or if treatment choices depend on prognostic information absent from the data. A causal interpretation also requires consistency and positivity: the observed outcome agrees with the outcome under the treatment actually received, and each treatment option being compared has positive probability within histories relevant to the comparison.

Worked Example: A Prior Treatment Changes the Later Indication

Suppose $A_1$ is assigned with probability $0.5$. The chance of severe symptoms at the next visit is $0.6$ when $A_1=0$ and $0.2$ when $A_1=1$. At that later visit, the chance of receiving $A_2=1$ is $0.8$ with severe symptoms and $0.2$ without them. Calculate how the later treatment probability differs by prior treatment and how symptom severity is distributed among later-treated patients.

For $A_1=0$, the probability of $A_2=1$ is $0.6(0.8)+0.4(0.2)=0.56$. For $A_1=1$, it is $0.2(0.8)+0.8(0.2)=0.32$. Thus the first treatment changes the distribution of the later indication, which in turn changes the chance of the second treatment.

Across both prior-treatment groups, $P(L_2=1)=0.5(0.6)+0.5(0.2)=0.4$. The overall probability of $A_2=1$ is $0.5(0.56)+0.5(0.32)=0.44$. The joint probability of severe symptoms and later treatment is $0.5(0.6)(0.8)+0.5(0.2)(0.8)=0.32$. Therefore $P(L_2=1\mid A_2=1)=0.32/0.44$, approximately $0.727$. By contrast, $P(A_2=0)=0.56$, and $P(L_2=1,A_2=0)=0.4-0.32=0.08$, so $P(L_2=1\mid A_2=0)=0.08/0.56$, approximately $0.143$.

The later-treated group is much more likely to have severe symptoms. A comparison by $A_2$ alone therefore mixes the effect of the second treatment with differences in current illness. The calculation also shows why treatment histories matter: $A_1$ helps shape $L_2$, and $L_2$ helps shape $A_2$.

Unequal Symptom Distributions Distort Pooled Comparisons

A useful general identity makes the source of the pooled distortion explicit. For symptom strata $s$, define $m_a(s)=E[Y\mid A=a,S=s]$. Then

E[Y\mid A=1]-E[Y\mid A=0] =\sum_s P(S=s\mid A=1)m_1(s) -\sum_s P(S=s\mid A=0)m_0(s).

This follows by applying the law of total expectation separately within the treated and untreated groups. The two sums use different weights whenever treatment groups have different symptom distributions. Consequently, the pooled difference need not equal a comparison using a common symptom distribution, even if the within-symptom treatment contrasts are constant. This is a description of the observed data; interpreting a common-weight contrast causally requires adequate control of confounding and suitable assumptions.

Worked Example: Pooled Versus Symptom-Standardized Means

Consider 100 treated and 30 untreated patients. Among treated patients, 20 have mild symptoms with mean outcome 7 and 80 have severe symptoms with mean 11. Among untreated patients, 10 have mild symptoms with mean 10 and 20 have severe symptoms with mean 14. Compute the pooled difference and a comparison standardized to equal proportions of mild and severe symptoms.

The treated pooled mean is $\{20(7)+80(11)\}/100=(140+880)/100=10.2$. The untreated pooled mean is $\{10(10)+20(14)\}/30=(100+280)/30=12.667$, to three decimal places. Thus the pooled treated-minus-untreated difference is $10.2-12.667=-2.467$, approximately.

For equal symptom weights, the treated mean is $\{7+11\}/2=9$, and the untreated mean is $\{10+14\}/2=12$. The equally weighted difference is $9-12=-3$. Within both symptom strata the treatment contrast is $-3$, but the pooled contrast is less negative because severe symptoms account for $80/100=0.8$ of treated patients and $20/30\approx0.667$ of untreated patients. Equal weighting is an arithmetic illustration here, not a claim that this particular standardization identifies a causal effect in every study.

Recognizing the Problem and Choosing a Comparison

Several checks can reveal whether confounding by indication is a serious concern. First, establish the measurement order: was clinical status recorded before the treatment decision it is meant to explain? Second, compare the distributions of current symptoms across treatment groups, within relevant prior-treatment histories. Third, ask clinicians whether decisions depend on severity, deterioration, or other prognostic information that the data do not capture. Large symptom imbalances are a warning, although balance in recorded variables cannot rule out unmeasured confounding.

The main alternatives answer different questions. A crude comparison by current treatment does not account for differing indications. A baseline-adjusted comparison can address baseline differences but will not, by itself, balance symptoms that evolve after baseline. A comparison adjusted or stratified by current pre-treatment status can address that visit’s measured indication, but its interpretation depends on exactly which history is held fixed and on the causal question. A longitudinal causal analysis, including marginal structural models, is designed for settings where treatment and covariates evolve together; naming that approach does not remove the need to define the target comparison or defend its assumptions.

There are limits to what these checks and adjustments can accomplish. If severe symptoms are recorded only after treatment, treating them as the indication for that same decision reverses the time order. If important symptoms are unmeasured, a model using recorded covariates may leave confounding. If some treatment option is almost never given to a particular symptom-history group, positivity is doubtful and the data provide little support for that comparison. Finally, confounding by indication is not proof that treatment is harmful: a treatment given to sicker patients can be beneficial and still have worse observed outcomes.

Common mistake: “The treated group had worse outcomes, so treatment caused harm; adjusting for baseline severity should fix the comparison.” This reasoning ignores symptoms that changed after baseline and guided later decisions. The correction is to order measurements and treatment decisions in time, identify each visit’s pre-treatment indication, and recognize that a baseline-only adjustment does not necessarily control later confounding.

A practical interpretation should therefore separate three statements: who received treatment, what their observed outcomes were, and what would have happened under a different treatment history. The first two are descriptive. The third is causal and requires adequate measurement of indications, appropriate treatment-history comparisons, and the assumptions stated above.

Check Your Understanding

Answer each question, then compare with the brief solutions below.

If severe symptoms predict a higher outcome and are more common among treated patients, what sign does the symptom-imbalance term have in the additive bias identity?
Why can adjustment for baseline severity fail to control confounding at a later treatment decision?
In the pooled-versus-standardized example, which group had the larger proportion of severe symptoms, and how did this affect the pooled contrast?
Name two assumptions, beyond a correct description of measured symptom imbalance, needed for causal interpretation of treatment-history comparisons.

Solutions. (1) The term is positive because both $\gamma$ and $P(S=1\mid A=1,H)-P(S=1\mid A=0,H)$ are positive; for a lower-is-better outcome, this makes a beneficial negative treatment contrast appear less favorable. (2) Later severity may have changed since baseline and may predict both the current treatment and outcome, so baseline status does not ensure comparable current indications. (3) The treated group had the larger severe-symptom proportion, $0.8$ versus approximately $0.667$; its worse prognostic mix moved the pooled contrast from $-3$ to approximately $-2.467$. (4) Examples include sequential exchangeability, consistency, and positivity; any two are sufficient.