Estimating Average Causal Effects Under General Interference

This work addresses the fundamental challenge of estimating causal effects when the Stable Unit Treatment Value Assumption (SUTVA) is violated—specifically, when one unit's treatment assignment affects another unit's outcome. This "interference" problem arises pervasively in settings where units interact: vaccine trials where herd immunity means an unvaccinated person's infection risk depends on neighbors' vaccination status, educational interventions where peer effects amplify or dampen program impacts, and social programs where treatment spillovers across households bias naive comparisons. Existing approaches either assumed no interference (rendering estimates biased and inconsistent) or required complete knowledge of the network structure and full randomization over all possible treatment assignments (computationally infeasible for large populations). This paper provides a rigorous experimental design framework based on partial interference—the assumption that interference occurs only within pre-specified clusters, with no interference across clusters. It delivers unbiased estimators for both direct effects (the effect of one's own treatment) and spillover effects (the effect of others' treatments on one's outcome), along with asymptotic normality results that enable valid inference. The key innovation is showing that with careful design—specifically, two-stage randomization where clusters are first assigned to treatment intensity conditions and then units within clusters are randomized—one can recover these effects without modeling the full interference structure.

The core idea is to decompose the causal estimand into components that can be identified through a two-stage randomization design, avoiding the need to model the full interference structure. The intuition proceeds in three steps.

Step 1: Define the estimands of interest. The paper focuses on two types of average causal effects. The direct effect is the average effect of one's own treatment on one's outcome, holding fixed the treatment assignments of others in the cluster. The spillover effect (or indirect effect) is the average effect of others' treatments on one's outcome, holding fixed one's own treatment. More precisely, for a cluster of size (m), let (Z_i) be the treatment of unit (i) and (\mathbf{Z}{-i}) be the vector of treatments for all other units in the cluster. The potential outcome for unit (i) is (Y_i(z_i, \mathbf{z}{-i})). The average direct effect (ADE) is:

[ ADE = \mathbb{E}[Y_i(1, \mathbf{Z}{-i}) - Y_i(0, \mathbf{Z}{-i})] ]

where the expectation is over the distribution of (\mathbf{Z}_{-i}) induced by the randomization design. The average spillover effect (ASE) is:

[ ASE = \mathbb{E}[Y_i(z, \mathbf{Z}{-i}^{(1)}) - Y_i(z, \mathbf{Z}{-i}^{(0)})] ]

where (\mathbf{Z}{-i}^{(1)}) and (\mathbf{Z}{-i}^{(0)}) represent two different distributions of others' treatments (e.g., high vs. low treatment prevalence in the cluster).

Step 2: Design the two-stage randomization. The key design innovation is to randomize at two levels. First, clusters are randomly assigned to different "treatment intensity" conditions—for example, some clusters are assigned to have 80% of units treated, others 50%, others 20%. Second, within each cluster, units are randomly assigned to treatment or control according to the cluster's assigned intensity. This creates variation in both individual treatment status and the proportion of treated neighbors, which is the key to separating direct and spillover effects.

Step 3: Construct unbiased estimators. The paper proposes difference-in-means estimators that exploit the two-stage randomization. Let (Y_{ij}) be the outcome for unit (j) in cluster (i), and let (Z_{ij}) be its treatment indicator. Let (p_i) be the proportion of treated units in cluster (i) (the cluster-level treatment intensity). The estimator for the average direct effect is:

[ \hat{\tau}{direct} = \frac{1}{N} \sum{i,j} \frac{Z_{ij} Y_{ij}}{p_i} - \frac{(1-Z_{ij}) Y_{ij}}{1-p_i} ]

This is a Horvitz-Thompson-type estimator that weights each unit by the inverse of its assignment probability, which varies by cluster. The estimator for the spillover effect compares outcomes across clusters with different treatment intensities, controlling for individual treatment status:

[ \hat{\tau}{spillover} = \frac{1}{N} \sum{i,j} \left[ \frac{Y_{ij}(1-p_i)}{1-p_i} - \frac{Y_{ij}(1-p_{i'})}{1-p_{i'}} \right] ]

where the comparison is between clusters with different (p) values. The paper proves these estimators are unbiased under the partial interference and randomization assumptions, and derives their asymptotic variance, which can be estimated using cluster-robust standard errors.

Step 4: Inference. The estimators are asymptotically normal as the number of clusters grows large (with cluster sizes bounded). The variance depends on both within-cluster and between-cluster variation. The paper provides a variance estimator that accounts for the two-stage randomization, which is essential for valid inference—naive standard errors that ignore the clustering will be severely anti-conservative.

• Prefer this over standard SUTVA-based methods (e.g., difference-in-means, regression adjustment) when: You have strong evidence that interference exists (e.g., from prior studies or domain knowledge) and you can plausibly partition units into non-interfering clusters. This includes vaccine trials where clusters are geographic regions, educational interventions where clusters are classrooms, and agricultural experiments where clusters are plots.

• Prefer this over network-based interference methods (e.g., Aronow & Samii 2017, Ugander et al. 2013) when: You do not have complete network data or the network is too large/dense to model. Partial interference requires only cluster membership, not full adjacency matrices. It is also computationally simpler—no need to estimate exposure models or compute complicated variance estimators.

• Prefer this over cluster-randomized trials (CRTs) when: You need to separate direct and spillover effects. CRTs estimate the total effect of treatment (which conflates direct and spillover effects), while this design disentangles them. If you only need the total effect, a CRT is simpler and requires fewer assumptions.

• Prefer this over difference-in-differences or instrumental variables when: You have experimental control over treatment assignment. This is a design-based approach that requires randomization; it is not suitable for observational studies where treatment is confounded.

• Prefer this over the "linear-in-means" social interaction models (Manski 1993) when: You want to avoid parametric assumptions about how interference operates. The partial interference approach is nonparametric within clusters—it does not assume a specific functional form for spillovers.

• Avoid this when: Clusters are poorly defined or interference crosses cluster boundaries. If there are strong connections between clusters (e.g., students in different classrooms who interact after school), the partial interference assumption is violated and estimates will be biased. Also avoid when the number of clusters is small (e.g., fewer than 20), as asymptotic approximations will be poor.

What breaks this method:

1. Violations of partial interference: This is the most critical failure mode. If interference crosses cluster boundaries (e.g., students in different classrooms who share a tutor, or households in different villages who trade goods), the estimators become biased. The direction of bias depends on the sign of the cross-cluster interference—positive spillovers across clusters inflate the estimated direct effect, while negative spillovers deflate it.

2. Non-random cluster assignment: The method requires that clusters are randomly assigned to treatment intensity conditions. If clusters self-select into intensities (e.g., more motivated schools choose higher treatment intensity), the estimates are confounded by cluster-level characteristics. This is a design requirement, not something that can be fixed in analysis.

3. Small number of clusters: With fewer than 20 clusters, the asymptotic approximations break down. The variance estimator becomes unreliable, and confidence intervals under-cover substantially. Permutation tests help but have low power with few clusters.

4. Extreme treatment intensities: If some clusters have treatment intensity near 0% or 100%, the inverse probability weights become very large, inflating variance and potentially introducing bias if the weights are correlated with outcomes.

5. Nonlinear interference: The method estimates average spillover effects, but if spillovers are highly nonlinear (e.g., threshold effects where