Two-Stage Randomized Saturation Design

• Two-Stage Randomized Saturation Design is a two-stage experimental setup that assigns clusters to saturation levels and then individual units to treatment, enabling clear separation of direct and spillover effects.
• The design leverages partial and stratified interference assumptions while employing inverse-probability weighting to achieve unbiased causal estimates.
• It involves trade-offs between efficiency for estimating direct effects and the variation needed for detecting spillovers, with practical applications in education, health, and economic experiments.

Searching arXiv for papers on two-stage randomized saturation designs and interference. Two-stage randomized saturation designs are two-stage experiments: they first randomly assign treatment probabilities over the clusters and then randomly assign the treatment to the units within the clusters. In this design, stage 1 randomizes clusters to a saturation regime or treatment status, and stage 2 randomizes units within clusters so that the treated fraction matches the assigned mechanism. The design is used for causal inference when one individual's treatment assignment affects another individual's outcomes, and it is especially valuable when spillovers are scientifically important (Jiang et al., 2020).

1. Assignment structure and saturation mechanisms

In the general formulation, there are $J$ clusters indexed by $j=1,\dots,J$, cluster $j$ contains $n_j$ units indexed by $i=1,\dots,n_j$, and the total sample size is $N=\sum_{j=1}^J n_j$. Stage 1 assigns each cluster to one of $m$ treatment assignment mechanisms, $A_j\in M=\{1,2,\dots,m\}$, using complete randomization across clusters, so exactly $J_a$ clusters receive mechanism $a$, with $j=1,\dots,J$0. Stage 2 then randomizes units within each cluster conditional on the cluster’s assigned mechanism; under mechanism $j=1,\dots,J$1, exactly $j=1,\dots,J$2 units are treated and $j=1,\dots,J$3 are controls. A saturation level is the proportion of treated units inside a cluster, determined by the assigned mechanism $j=1,\dots,J$4 (Jiang et al., 2020).

This structure appears in several special cases. In the household design used to study absenteeism in the School District of Philadelphia, stage 1 randomly assigned exactly $j=1,\dots,J$5 of the $j=1,\dots,J$6 households to treatment or control, and stage 2 selected exactly one individual for treatment in each treated household. In that design, treated individuals are always nested inside treated households, so the second stage is a special case in which the “saturation” is one treated person per treated household (Basse et al., 2016).

A further extension allows covariate-adaptive randomization at both stages. Clusters may be stratified using baseline cluster covariates $j=1,\dots,J$7 and possibly cluster size $j=1,\dots,J$8, and units within treated clusters may be stratified using baseline unit covariates $j=1,\dots,J$9. The paper on covariate-adaptive randomization often specializes to finite-group, finely stratified randomization, in which clusters are partitioned into strata of size $j$0 and exactly $j$1 clusters are assigned to treatment within each stratum, so $j$2 (Liu, 2023).

The central design implication is that stage 1 determines the cluster-level treatment environment, while stage 2 creates within-cluster exposure variation. This suggests why the design can separate own-treatment effects from exposure to treated neighbors.

2. Interference assumptions and exposure mappings

The standard analysis assumes partial interference: outcomes can be affected by treatment within a cluster, but not by treatment in other clusters. In the cluster-level notation of the general randomization-based framework,

$j$3

A stronger within-cluster restriction is stratified interference,

$j$4

so the potential outcome depends on own treatment and the number treated in the cluster, not on the exact identities of treated peers (Jiang et al., 2020).

In the household-based design, the same logic appears as partial interference across households and stratified interference within households. Under the treatment rule with exactly one treated individual in each treated household, each unit has only three relevant potential outcomes,

$j$5

and the observed outcome is a corresponding mixture determined by household treatment and individual treatment status (Basse et al., 2016).

Recent work extends the standard randomized saturation design to allow for two distinct interference channels: spillovers within clusters and spillovers across clusters driven by geographic proximity. In that formulation, the full assignment vector is reduced to an exposure mapping

$j$6

where $j$7 is own treatment, $j$8 captures within-sublocation exposure, and $j$9 captures between-sublocation geographic exposure. The maintained exclusion restriction is that $n_j$0 whenever $n_j$1, so the relevant potential outcomes can be written as $n_j$2 (Lu et al., 20 Mar 2026).

The shift from $n_j$3 to $n_j$4 is substantively important. A leading example is that some units are geographically close to each other, so spillover effects arise across clusters. This suggests that the classical “isolated clusters” interpretation is not always appropriate even when the experimental assignment is clustered.

3. Causal estimands

Under the standard clustered-interference formulation, the average direct effect at saturation mechanism $n_j$5 is

$n_j$6

where $n_j$7 is the average potential outcome under own treatment $n_j$8 and mechanism $n_j$9. Because there are $i=1,\dots,n_j$0 direct effects, the framework also defines a marginal direct effect,

$i=1,\dots,n_j$1

with $i=1,\dots,n_j$2, and a spillover effect,

$i=1,\dots,n_j$3

which compares saturation mechanisms while holding own treatment fixed (Jiang et al., 2020).

In the household-based literature, the same conceptual distinction is expressed as a primary effect and a spillover effect. When household sizes vary, the analysis distinguishes household-weighted estimands, in which each household gets equal weight, from individual-weighted estimands, in which each individual gets equal weight. The practical reason is that under the two-stage design the within-household treatment probability depends on household size, $i=1,\dots,n_j$4, so the choice between household-weighted and individual-weighted targets is not innocuous (Basse et al., 2016).

With cross-cluster spillovers made explicit through the exposure mapping $i=1,\dots,n_j$5, the relevant causal estimands separate direct, within-cluster indirect, and between-cluster indirect effects. The direct effect at exposure $i=1,\dots,n_j$6 is

$i=1,\dots,n_j$7

The within-cluster spillover effect holding own treatment fixed at zero is

$i=1,\dots,n_j$8

and the between-cluster spillover effect is

$i=1,\dots,n_j$9

These are conditional because they compare exposure levels at fixed values of the other exposure variables. The same framework also defines in-policy marginal effects and policy-specific estimands under an arbitrary policy $N=\sum_{j=1}^J n_j$0; the paper emphasizes that these marginal estimands depend on the treatment assignment mechanism and are not purely structural objects independent of the design (Lu et al., 20 Mar 2026).

A common source of confusion is the relation between conditional and marginal effects. The marginal direct effect averages over the design’s distribution of exposures, whereas the conditional direct effect fixes the exposure environment. This suggests that heterogeneity across exposure environments can be diluted by in-policy averaging.

4. Estimation, variance, and inference

In the general randomization-based framework, unbiased estimation begins with cluster-level observed means,

$N=\sum_{j=1}^J n_j$1

and mechanism-level means,

$N=\sum_{j=1}^J n_j$2

Under two-stage randomization, no cross-cluster interference, and stratified interference, $N=\sum_{j=1}^J n_j$3, so the plug-in estimators of $N=\sum_{j=1}^J n_j$4, $N=\sum_{j=1}^J n_j$5, and $N=\sum_{j=1}^J n_j$6 are exactly unbiased in the finite-population randomization framework. The same paper derives conservative variance estimators, establishes asymptotic normality, constructs Wald tests, and gives sample-size formulas for direct, marginal direct, and spillover effects (Jiang et al., 2020).

For the exposure-cell formulation with within-cluster and between-cluster spillovers, estimation is based on inverse-probability weighting. For each exposure cell $N=\sum_{j=1}^J n_j$7,

$N=\sum_{j=1}^J n_j$8

The Horvitz–Thompson estimator of the average potential outcome is

$N=\sum_{j=1}^J n_j$9

and the Hájek estimator is the normalized version

$m$0

Estimators of $m$1, $m$2, and $m$3 are then formed by differences of these cell means. Identification and inference rest on bounded potential outcomes, positivity of exposure probabilities, bounded network degree $m$4, and bounded order of dependence $m$5. Under these conditions, both HT and Hájek estimators are consistent and jointly asymptotically normal, and the paper derives conservative, asymptotically valid confidence intervals using a Cauchy–Schwarz upper bound because the covariance between different potential-outcome estimators is not identified (Lu et al., 20 Mar 2026).

When household sizes vary, inverse-probability weights are also central in the simpler two-stage design. The household-weighted estimators reduce to simple differences in household-level means, whereas the individual-weighted estimators are Horvitz–Thompson-style estimators that upweight treated individuals in large households because their treatment probability is $m$6. The same paper shows that the naive simple difference-in-means estimator can be biased for individual-weighted targets when household size is correlated with outcomes or treatment effects (Basse et al., 2016).

Two further implementation results are notable. First, in the household design, ordinary least squares estimates from

$m$7

match the randomization-based estimators, and with cluster-robust HC2 standard errors the variance estimates match exactly. Second, in the more general saturation design, the randomization-based estimators are equivalent to weighted least squares with inverse-probability weights, and the cluster-robust HC2 covariance matrix is exactly equal to the conservative randomization-based covariance estimator (Basse et al., 2016).

5. Design tradeoffs, covariate adaptation, and ranking saturation regimes

The two-stage randomized saturation design involves an explicit tradeoff between learning about spillovers and preserving efficiency for direct effects. Under the power-analysis framework, more variation in saturation levels is better for spillover identification, while less variation in saturation levels is better for direct-effect precision. In simulations, the required number of clusters is much larger for spillover effects than for direct or marginal direct effects, and unequal cluster sizes do not materially harm performance because the formulas depend on cluster sizes mainly through the harmonic mean $m$8 (Jiang et al., 2020).

Relative efficiency also depends on the assignment rule. The comparison with completely randomized and cluster randomized designs is framed as follows: if all saturation levels $m$9 are equal, the two-stage design becomes a stratified randomized design and can be more efficient than complete randomization; greater heterogeneity in $A_j\in M=\{1,2,\dots,m\}$0 helps detect spillovers but hurts efficiency for estimating average treatment effects when spillovers are absent; and compared with cluster randomization, the two-stage design becomes relatively more efficient as cluster size grows (Jiang et al., 2020).

Covariate-adaptive randomization changes both design optimality and valid inference. Under the homogeneous partial interference assumption, the difference-in-“average of averages” estimators are consistent and asymptotically normal for the corresponding average primary and spillover effects, and the paper develops consistent estimators of their asymptotic variances. Its practical message is that ignoring covariate information in the design stage can result in efficiency loss, and commonly used inference methods that ignore or improperly use covariate information can lead to either conservative or invalid inference. In large samples, a specific generalized matched-pair design achieves minimum asymptotic variance for each proposed estimator (Liu, 2023).

A separate recent development treats the two-stage randomized saturation design as a platform for ranking saturation levels rather than only estimating causal contrasts. In that setting, clusters are assigned to one of $A_j\in M=\{1,2,\dots,m\}$1 saturation regimes at stage 1 and units are assigned treatment according to the assigned saturation at stage 2. The proposed empirical success ranking rule compares estimated welfare across pairs of saturations, finite-sample regret is bounded using the fractional chromatic number $A_j\in M=\{1,2,\dots,m\}$2, and the balanced design

$A_j\in M=\{1,2,\dots,m\}$3

is quasi-optimal because it minimizes an upper bound on the worst-case risk. Under a rank-one structural condition, the empirical success rule is asymptotically optimal among threshold ranking rules (Han et al., 17 Jun 2026).

These results broaden the role of saturation experiments. They are not restricted to testing whether spillovers exist; they can also support design-based policy comparisons across a finite menu of saturation regimes.

6. Empirical applications and interpretive issues

Empirical applications illustrate both the flexibility of the design and the importance of specifying the exposure environment correctly. In the attendance study from the School District of Philadelphia, the primary effect on chronic absenteeism was about $A_j\in M=\{1,2,\dots,m\}$4 percentage points for both household-weighted and individual-weighted estimands, and the spillover effect was about $A_j\in M=\{1,2,\dots,m\}$5 percentage points. For log absences, the primary effect was about $A_j\in M=\{1,2,\dots,m\}$6 log-days for household-weighted estimands and $A_j\in M=\{1,2,\dots,m\}$7 log-days for individual-weighted estimands, corresponding to roughly 1.2 fewer days absent; the spillover effect was about $A_j\in M=\{1,2,\dots,m\}$8 to $A_j\in M=\{1,2,\dots,m\}$9 log-days, or roughly 0.7 fewer days absent. The spillover was summarized as 60% to 80% as large as the primary effect, and accounting for spillovers changed estimated cost effectiveness from about $J_a$0 per additional student day (Basse et al., 2016).

In the randomized evaluation of the Indian national health insurance program, villages were assigned to one of three saturation levels—90%, 70%, and 50%—and households within villages were then randomized according to the assigned saturation. For midline hospitalization, estimated direct effects were positive under all saturation levels but not statistically significant, and spillovers were also insignificant. For endline hospitalization, the direct effect varied more across saturation levels: under the highest treatment saturation, the estimated direct effect was positive, while under the lowest saturation it was negative, with a difference of about 6.6 percentage points (Jiang et al., 2020).

The Kenya cash transfer re-analysis extends the design to cross-cluster interference. The experiment involved 653 villages in 155 sublocations across two counties. Stage one assigned sublocations to high saturation or low saturation, and stage two assigned villages to treatment at rates of about $J_a$1 or $J_a$2. The analysis considered profits, revenues, total cost, and wage bill, defined within-sublocation exposure $J_a$3 from the fraction of treated villages in the same sublocation, and defined geographic exposure $J_a$4 from treated nearby villages outside the sublocation using villages within 4 km and the three nearest outside villages in the baseline specification. Because propensity scores and joint inclusion probabilities were not available in closed form, they were approximated with 100,000 Monte Carlo draws from the randomization scheme. The re-analysis found that between-sublocation spillovers are economically meaningful: control villages in low-saturation sublocations benefit from proximity to treated villages outside their sublocation, while treated villages in high-saturation sublocations suffer negative geographic spillovers, consistent with competition for labor and inputs. The in-policy marginal effects were much less often significant because averaging over heterogeneous exposure environments dilutes the signal (Lu et al., 20 Mar 2026).

These applications clarify several recurring interpretive issues. A simple difference in means can target the wrong estimand when treatment probabilities vary with cluster size. Regression is not “different” from randomization inference here if done properly, because with suitably chosen standard errors the two approaches can yield identical point and variance estimates. Most importantly, analyses that ignore between-cluster spillovers by assuming clusters are isolated can be misleading: the marginalization over unmodeled geographic spillovers can mask substantively important heterogeneity and bias interpretation. The reduced $J_a$5 model can still capture broad within-sublocation patterns, but it loses the ability to detect the geographic spillover channel and yields averaged effects that resemble the full model’s marginal effects (Lu et al., 20 Mar 2026).