Why Subclassify a Cohort?
In an observational cohort, people receiving treatment may differ systematically from those who do not. Subclassification uses the propensity score to group people with similar estimated probabilities of treatment, then compares outcomes within those groups. Combining the within-group contrasts can adjust for measured differences, provided the groups contain both treatment arms and the relevant confounding has been controlled.
Subclassification is not individual matching: a person need not be paired with a particular person in the other treatment arm. It is a form of stratification. Its practical appeal is that balance and support can be inspected separately in each part of the score distribution. Its limitation is equally important: grouping scores into intervals does not guarantee that covariates are balanced, and a weighted contrast is only as credible as the assumptions and diagnostics supporting its component comparisons.
In practice, \(e(X)\) is usually estimated from a treatment-assignment model, and people are assigned to intervals of their estimated scores. Boundaries might be based on score quantiles or selected to produce useful balance. There is no universal number of subclasses that guarantees adequate adjustment. The intervals must be evaluated using the covariates and treatment representation within them, not chosen or accepted solely because a conventional number of groups was used.
Assumptions and the Target Contrast
Write \(Y(1)\) and \(Y(0)\) for the outcomes a person would have under treatment and no treatment, respectively. The observed outcome is \(Y=A Y(1)+(1-A)Y(0)\), under consistency: the observed outcome equals the potential outcome under the treatment actually received. A causal interpretation also requires that treatment assignment be unconfounded within the subclasses used and that both treatment options be represented in every such subclass.
The conditioning variable \(H\) is a coarsening of the propensity score. Even if the true propensity score balances covariates at an exact score value, people with different scores inside a broad interval can still differ. Thus, acceptable balance within intervals is important evidence about the adequacy of the chosen partition, but measured balance cannot establish exchangeability with respect to unmeasured confounders.
For the average treatment effect in the cohort, let \(q_h=P(H=h)\) be the proportion of the target cohort in subclass \(h\). The estimand and its sample analogue are:
Here \(N_h\) is the number of cohort members in subclass \(h\), \(N\) is the total cohort size, and \(\bar{Y}_{ah}\) is the observed mean outcome for treatment group \(a\) in that subclass. The weights \(N_h/N\) give each subclass its share of the full cohort. The estimate targets the cohort’s average treatment effect when the identification conditions hold for that cohort and its subclasses. Different weights generally answer a different question.
Worked Example: Forming Subclasses and Checking Balance
Worked Example: Forming Subclasses and Checking Balance
Hypothetical cohort. A team estimates treatment propensities from pretreatment age, disease severity, and comorbidity, then divides 300 people into three score intervals. The table gives the number treated and untreated in each interval.
| Subclass | Estimated-score interval | Treated | Untreated | Total |
|---|---|---|---|---|
| Low | 0.05–0.20 | 30 | 50 | 80 |
| Middle | 0.20–0.45 | 60 | 60 | 120 |
| High | 0.45–0.80 | 70 | 30 | 100 |
All three subclasses contain treated and untreated people, so the observed treatment contrast is defined in each one. That count check does not by itself show adequate overlap: estimated scores and covariate distributions should also be examined within each subclass. For example, a few untreated people with scores near 0.80 would not provide strong comparative support for many treated people near that boundary.
Suppose in the low-score subclass, 30% of treated people and 28% of untreated people have comorbidity. The standardized mean difference for this binary covariate is the difference in proportions divided by the pooled Bernoulli standard deviation. The pooled proportion is:
The pooled standard deviation is \(\sqrt{0.2875(1-0.2875)}\approx0.4526\), so the standardized difference is:
The difference is about 0.044 standard deviations in this subclass. This is a small measured imbalance, but it is not proof of exchangeability. The same checks should be made for other relevant covariates in each subclass; acceptable overall balance can conceal poor balance in a particular interval.
Combining Subclass-Specific Outcome Contrasts
For a binary outcome, the within-subclass contrast can be a risk difference. The weighted average is then expressed in percentage points, which are often easier to interpret than a standardized statistic. The next example calculates the cohort-weighted contrast from observed hypothetical counts.
Worked Example: A Cohort-Weighted Risk Difference
In a hypothetical cohort, the outcome is an adverse event during a specified follow-up period. The following counts are observed in the same three subclasses.
| Subclass | Treated with event / treated | Untreated with event / untreated | Risk difference | Cohort weight |
|---|---|---|---|---|
| Low | 6/30 = 0.20 | 15/50 = 0.30 | −0.10 | 80/300 |
| Middle | 21/60 = 0.35 | 24/60 = 0.40 | −0.05 | 120/300 |
| High | 21/70 = 0.30 | 15/30 = 0.50 | −0.20 | 100/300 |
The estimated cohort risk difference weights each within-subclass difference by that subclass’s share of all 300 people:
Under the stated identification conditions, the estimate corresponds to an 11.33-percentage-point lower average risk under treatment than under no treatment in this cohort. The negative sign indicates lower risk in the treated condition. This is an estimated causal contrast only if the assumptions are credible; the arithmetic alone does not establish that treatment caused the difference.
Why the Weights Define the Estimand
Subclassification produces a set of stratum-specific contrasts, not a single effect with a self-evident target. The weights determine how those contrasts are averaged. To see the consequence, keep the previous example’s stratum-specific differences but weight them by the distribution of treated cohort members instead of the full cohort. This describes a treated-group target (an ATT-type contrast), not the full-cohort target.
Worked Example: Changing the Target Population
The proportions of treated people in the low, middle, and high subclasses are \(30/160\), \(60/160\), and \(70/160\), because there are 160 treated people in total. Standardizing the same stratum-specific risk differences to that distribution gives:
This is a 12.50-percentage-point lower average risk standardized to the treated group’s subclass distribution, compared with 11.33 percentage points for the full cohort. The values differ because the high-score subclass, which has the largest estimated contrast here, makes up a larger fraction of treated people than of the full cohort. A population-specific interpretation also requires that the stratum contrasts identify the relevant effects for that target; the weights do not repair failed exchangeability or absent treatment support.
Justification of the Within-Subclass Contrast
The identifying step can be shown directly. Fix a subclass \(h\) with positive probability of receiving each treatment. By consistency, among people actually treated, the observed outcome equals \(Y(1)\); among untreated people, it equals \(Y(0)\). Conditional exchangeability within \(h\) makes treatment independent of both potential outcomes in that subclass. Therefore:
The positivity condition matters to this argument: if \(P(A=1\mid H=h)=0\), the treated conditional mean in the first line is not defined from observed data; if \(P(A=0\mid H=h)=0\), the same is true of the untreated mean. When both probabilities are positive, subtracting the equalities gives:
Finally, weighting these subclass effects by \(q_h=P(H=h)\) averages over the target cohort’s subclass distribution. This yields the stated cohort estimand. The justification does not say that estimated propensity scores automatically make treatment exchangeable within broad intervals; that remains an assumption requiring substantive reasoning and measured-covariate diagnostics.
Diagnostics, Alternatives, and Limitations
Before interpreting the weighted contrast, inspect the subclass structure and the covariate distributions. Useful checks include:
- Treatment support: verify that both groups occur in every subclass used, and inspect score ranges within each treatment arm rather than relying only on counts.
- Within-subclass balance: compare pretreatment covariates between treatment groups in every subclass using standardized differences and suitable distributional summaries. Review important nonlinearities and interactions, not only covariate means.
- Subclass size and precision: small groups can yield unstable outcome means. A stratum with one or two people in an arm may technically have both arms but provide a weak comparison.
- Sensitivity to boundaries: compare defensible alternative partitions. Large changes in the estimate or balance can signal that coarse grouping leaves substantial residual differences.
- Reporting and inference: report how scores were estimated, how boundaries were selected, counts by treatment within each subclass, balance diagnostics, the target weights, and the outcome contrast. Uncertainty procedures should account for the estimation of the propensity score and construction of the subclasses; a bootstrap that resamples people and repeats those steps is one possible approach.
Subclassification is often compared with matching and regression adjustment. Matching constructs pairs or sets according to a matching rule and may change the retained sample and target population. Subclassification retains people in score intervals and standardizes the interval contrasts using explicit weights. Regression adjustment models the outcome conditional on covariates and obtains a contrast from that model; its performance depends on outcome-model specification. These approaches have different diagnostics, assumptions, and target populations, so one is not automatically preferable in every cohort.
A common mistake is to conclude that five subclasses, or any other conventional number, guarantee removal of confounding because the propensity score was used. The correction is to check balance and treatment support within the actual subclasses, justify the target weights, and state the identifying assumptions. If meaningful imbalance persists, one should not present the pooled contrast as though subclassification had resolved it. If a subclass has no comparison group, its contrast is not identified from that data; excluding it changes the target population and must be made explicit.
Check Your Understanding
Answer each question, then compare your reasoning with the solutions below.
- In a subclass, every person is untreated. Can the within-subclass treatment effect be estimated from the observed outcomes? Why?
- Two subclasses have estimated effects of −0.04 and −0.16. They contain 75 and 25 people, respectively. Calculate the cohort-weighted estimate.
- Why does good overall covariate balance not guarantee good balance within every subclass?
- In the risk-difference example, what population does weighting by the treated subclass proportions target, and why can its estimate differ from the cohort-weighted result?
Solutions. (1) No. The treated conditional outcome mean is unavailable in that subclass, and positivity fails because \(P(A=1\mid H=h)=0\). (2) The cohort weights are \(75/100\) and \(25/100\), so the estimate is \(0.75(-0.04)+0.25(-0.16)=-0.030-0.040=-0.070\), or a 7-percentage-point lower outcome under treatment on the stated contrast scale. (3) Imbalances in different subclasses can cancel when summarized overall; the relevant within-stratum comparisons may still be confounded. (4) It targets the treated group’s subclass distribution. Its weights differ from the full cohort’s weights, so strata with different effects contribute differently to the average.