Optimal Design of Experiments in the Presence ofInterference∗
Sarah Baird†, J. Aislinn Bohren‡, Craig McIntosh§, Berk Özler¶
July 2017

Abstract
This paper formalizes the optimal design of randomized controlled trials (RCTs) inthe presence of interference between units, where an individual’s outcome depends on
the behavior and outcomes of others in her group. We focus on randomized saturation(RS) designs, which are two-stage RCTs that first randomize the treatment saturationof a group, then randomize individual treatment assignment. Our main contributions
are to map the potential outcomes framework with partial interference to a regression
model with clustered errors, calculate the statistical power of different RS designs, andderive analytical insights for how to optimally design an RS experiment. We showthat the power to detect average treatment effects declines precisely with the ability
to identify novel treatment and spillover estimands, such as how effects vary with theintensity of treatment. We provide software that assists researchers in designing RS
experiments.

∗

KEYWORDS:

Experimental Design, Causal Inference

JEL:

C93, O22, I25

We are grateful for the useful comments received from Frank DiTraglia, Elizabeth Halloran, Cyrus
Samii, Patrick Staples, and especially Peter Aronow. We also thank seminar participants at Caltech, Cowles
Econometrics Workshop, Econometric Society Australiasian Meeting, Fred Hutch workshop, Harvard T.H.
Chan School of Public Health, Monash, Namur, Paris School of Economics, Stanford, University of British
Columbia, UC Berkeley, University of Colorado, University of Melbourne, the World Bank, Yale Political
Science and Yale School of Public Health. We thank the Global Development Network, Bill & Melinda
Gates Foundation, National Bureau of Economic Research Africa Project, World Bank’s Research Support
Budget, and several World Bank trust funds (Gender Action Plan, Knowledge for Change Program, andSpanish Impact Evaluation fund) for funding.
†
George Washington University, sbaird@gwu.edu‡
University of Pennsylvania, abohren@sas.upenn.edu§
University of California, San Diego, ctmcintosh@ucsd.edu¶
World Bank, bozler@worldbank.org

1

Introduction

The possibility of interference in experiments – settings in which the treatment status of anindividual affects the outcomes of others – gives rise to a plethora of important questions.
How does the benefit of treatment depend on the intensity of treatment within a population?
What if a program benefits some by diverting these benefits from others? Does the study
even have an unpolluted counterfactual? In the presence of interference, a full understandingof the policy environment requires a measure of spillover effects that are not captured by (orworse, are sources of bias in) standard experimental designs. This is critical to determine
the overall program impact.
Empirical researchers across multiple academic disciplines have become increasingly interested in bringing spillover effects under the lens of experimental investigation. Over the
past decade, a new wave of experimental studies relax the assumptions around interference
between units. Researchers have used a variety of methods, including (i) using experimental variation across treatment groups, (ii) leaving some members of a group untreated, (iii)
exploiting exogenous variation in within-network treatments, and (iv) intersecting an experiment with pre-existing networks.1
The recent interest in interference between individuals has also spawned a rich econometrics literature. Aronow and Samii (forthcoming) and Manski (2013) consider the most general
settings, in which there are arbitrary forms of independence and treatment assignment dependencies. In this paper, we study settings with partial interference, in which individuals
are split into mutually exclusive clusters, such as villages or schools, and interference occurs
between individuals within a cluster but not across clusters. Partial population experiments(Moffitt 2001), in which clusters are assigned to treatment or control, and a subset of individuals are offered treatment within treatment clusters, partially overcome the challengeof allowing for partial interference. But they provide no exogenous variation in treatment
saturation to estimate the extent to which program effects are driven by the intensity oftreatment.2 To identify whether and how treatment and spillover effects vary with the in1(i) Bobba and Gignoux (2016); Miguel and Kremer (2004), (ii) Barrera-Osorio, Bertrand, Linden, andPerez-Calle (2011); Lalive and Cattaneo (2009), (iii) Babcock and Hartman (2010); Beaman (2012); Conley
and Udry (2010); Duflo and Saez (2002); Munshi (2003), (iv) Banerjee, Chandrasekhar, Duflo, and Jackson(2013); Chen, Humphries, and Modi (2010); Macours and Vakis (2008); Oster and Thornton (2012).
2
Most extant partial population experiments feature cluster-level saturations that are either endogenous

1

tensity of treatment in a cluster, we use randomized saturation (RS) experiments, a two-stage
randomization procedure in which first, the share of individuals assigned to treatment withina cluster is randomized and second, individuals within each cluster are randomly assigned totreatment according to the realized cluster-level saturation from the first stage.3 Hudgens
and Halloran (2008), Tchetgen Tchetgen and VanderWeele (2010) and Liu and Hudgens(2014) also study settings with partial interference using a two-stage design.
Our first contribution is to provide a foundation for the regression models commonlyused to analyze RS designs by setting up a potential outcomes model with partial interference and mapping it into a regression model. We place two restrictions on the population
distribution of potential outcomes – the population average potential outcome only depends
on an individual’s treatment status and the share of treated individuals in the cluster, andthe variance-covariance matrix of the population distribution of potential outcomes is blockdiagonal.4 These assumptions allow us to map the potential outcomes model to a regression
model with clustered standard errors, which provides a bridge between the causal inference
literature and the methods used to analyze randomized saturation (RS) designs in practice.
Athey and Imbens (2017) perform a similar derivation for a model with uncorrelated observations and no interference – our derivation is an extension of their approach that allows for
intra-cluster correlation and partial interference.
We show that RS designs identify a set of novel estimands: not only can the researcher
consistently identify the usual intention-to-treat effect, but she can also observe spillover
effects on treated and untreated units, and understand how the intensity of treatment drives
spillover effects for the treated and the untreated alike. These are similar to the estimands
that Hudgens and Halloran (2008) show can be consistently estimated in a finite population(Mexico’s conditional cash transfer program, PROGRESA/Oportunidades) or fixed (Duflo and Saez 2003)
and typically set at 50%. PROGRESA is perhaps the most-studied example – it features a treatment decisionat the cluster (village) level and an objective poverty eligibility threshold at the household level, so both
eligible and ineligible individuals in treatment villages can be compared to their counterparts in the pure
control group. PROGRESA has been used to examine spillover effects in several contexts (Alix-Garcia,
McIntosh, Sims, and Welch 2013; Angelucci and De Giorgi 2009; Bobonis and Finan 2009).
3
Banerjee, Chattopadhyay, Duflo, Keniston, and Singh (2012); Busso and Galiani (2014); Crepon, Duflo,
Gurgand, Rathelot, and Zamora (2013); Gine and Mansuri (forthcoming); Sinclair, McConnell, and Green(2012).
4
Hudgens and Halloran (2008) make the stronger assumption of stratified interference to estimate variances in a setting with partial interference. Graham, Imbens, and Ridder (2010) relax this assumption with
one of observational symmetry, i.e. exchangeability.

2

model. The experimental estimate of the average effect on all individuals in treated clusters,
which we refer to as the Total Causal Effect, provides the policy maker with a very simple
tool to understand how altering the intensity of implementation will drive outcomes for arepresentative individual.
Our second main contribution is to illustrate the power tradeoffs that exist in designing
RS experiments – that is, choosing the set of saturations and the share of clusters to assign toeach saturation. We derive closed-form expressions for the standard errors (SEs) of various
treatment and spillover estimands. Using these expressions, we derive properties of the
optimal designs to measure different sets of estimands. The ability to identify novel estimands
such as slope effects comes at a cost, namely, decreased statistical power to measure intentionto-treat effects pooled across all saturations. The same variation in treatment saturationthat permits measurement of how treatment and spillover effects vary with the intensity oftreatment is detrimental to the power of the simple experimental comparison of treatment topure control. By placing RS designs in the clustered error framework, we provide the closest
possible analog to the familiar power calculations in cluster randomized trials. This makes
the design tradeoffs present in RS experiments as transparent as possible. In related work,
Hirano and Hahn (2010) study the power of a partial population experiment to analyze alinear-in-means model with no intra-cluster correlation.
We conclude with an application that uses numerical simulations to illustrate the theoretical tools we develop using hypothetical and published study designs. First, we explicitly
define and estimate optimal designs for objective functions that include different individual saturation, slope and pooled estimands. We use the SE calculations to demonstrate
the power trade-offs that arise based on which estimands the researcher would like to identify and estimate. We also calculate standard errors for randomized saturation designs inpublished papers and show how these designs affect the power trade-off between different estimands. These power calculations and numerical optimizations are conducted using software
we developed specifically for designing RS experiments, which is available for researchers at
http://pdel.ucsd.edu/solutions/index.html.
The remainder of the paper is structured as follows. Section 2 sets up the potential outcomes framework, defines a RS design and defines estimands related to spillovers. Section

33 connects the potential outcomes framework to a regression model with clustered errors,presents closed-form expressions for the standard errors and derives properties of the optimal RS design to measure different sets of estimands. Section 4 presents an application
illustrating the optimal design results. All proofs are in Appendix A.

2

Causal Inference with Partial Interference

2.1

Potential Outcomes

A researcher seeks to draw inference on the outcome distribution of a population under
different treatment allocations. The target population I is partitioned into equal-sized, nonoverlapping groups, or clusters, of size n.5 Individual i in cluster c has response function
Yic : {0, 1}n → Y that maps each potential cluster treatment vector t = (t1 , ..., tn ) ∈ {0, 1}ninto potential outcome Yic (t) ∈ Y, where t ∈ {0, 1} is a binary treatment status in whicht = 1 corresponds to being offered treatment and t = 0 corresponds to not being offeredtreatment, and Y is a set of potential outcomes. The response function is independentof the treatment vectors for all clusters d ̸= c; spillovers may flow within a cluster, but
do not flow between clusters. Thus, we relax the stable unit treatment value assumption(SUTVA) within clusters, but maintain it across clusters. This set-up is referred to as partial
interference (Sobel 2006).6
A random sample is taken from this infinite population and randomly assigned treatment
according to a prespecified experimental design. Our goal is to study the power of different
experimental designs to detect treatment and spillover effects by comparing the standard
errors of the estimands in different designs. In order to characterize these standard errors,
we make two assumptions on the distribution of potential outcomes. First, we assume thatthe population average potential outcome E[Yic (t)] at potential treatment vector t ∈ {0, 1}ndepends only on individual treatment status ti and cluster treatment saturation p(t) ≡∑n1i=1 ti , where the expectation is with respect to the population distribution of potential
noutcomes.
Assumption 1. There exists a function Y : {0, 1}×[0, 1] → co(Y), where co(Y) is the convex
5

We assume clusters are equal in size to simplify the analysis. In practice, datasets may have significant
variation in the size of the cluster and the researcher may want to group clusters into different sized bins –for example, rural and urban clusters.
6
The assumption of no interference across groups is testable. For example, see Miguel and Kremer (2004).

4

hull of the set of potential outcomes, such that the population average potential outcome for
an individual with treatment status t is E[Yic (t)] = Y (t, p) at all treatment vectors t ∈ {0, 1}nwith treatment saturation p(t) = p.
Assumption 1 says that in expectation, the impact an individual receiving treatment has on
the outcomes of others in the same cluster is independent of the treated individual’s identity.
This allows for a characterization of the variance of estimands without possessing information
about the underlying network structure within a cluster.7 Assumption 1 is weaker than thestratified interference assumption proposed by Hudgens and Halloran (2008), which assumes
that the realized potential outcomes of an individual is independent of the identity of theother individuals assigned to treatment.
Clustering of outcomes can be due to either (i) the extent to which outcomes are endogenously driven by the treatment of others in the same cluster, which is a type of interference
between units, or (ii) a statistical random effect in outcomes that is correlated between
individuals – correlated effects (Manski 1993) – which does not stem from interference between units. In order to also allow for (ii), we assume a variance-covariance structure forthe distribution of potential outcomes that allows potential outcomes to be correlated acrossindividuals within the same cluster. We assume there is no correlation across clusters.
Assumption 2. Given σ 2 > 0 and τ 2 ≥ 0, the variance-covariance structure for the population distribution of potential outcomes is:
1. Var(Yic (t)) = σ 2 + τ 2 ,2. Cov(Yic (t), Yjc (t)) = τ 2 for i ̸= j,
3. Cov(Yic (t), Yjd (t′ )) = 0 for c ̸= d
for all t, t′ ∈ {0, 1}n .
Assumption 2 imposes homoskedasticity across all potential outcomes for a given individual
and across potential outcomes between two individuals in the same cluster. In other words,

7

In the absence of this assumption, a researcher would need to observe the complete network structure
in each cluster, understand the heterogeneity in networks across clusters, and use a model of network-driven
spillovers to simulate the variance in outcomes that could be generated by these networks. This is not an
issue when there is no interference within clusters, as each unit has only two potential outcomes.

5the variance and covariance of the distribution of potential outcomes do not depend on thetreatment status of an individual or the share treated in a cluster.8
Assumption 2 allows us to connect the potential outcomes framework to a regression
model with a block-diagonal error structure. Our goal is to provide a bridge between thetheoretical literature and the use of field experiments in economics to measure spillover
effects. To this end, it is natural to impose a variance structure on potential outcomesthat maps to the regression model typically used for power calculations when there is nointerference.9 It enables a direct comparison of the power of RS designs to the power ofthe canonical individually-randomized (blocked) and cluster-randomized (clustered) designs,
making explicit the impact that randomizing saturation has on power. A regression modelwith a block-diagonal structure is also the model underlying the use of OLS with clustered
standard errors to analyze resulting data, the method commonly used for analysis. We willoften use ρ ≡ τ 2 /(τ 2 + σ 2 ) to denote the intra-cluster correlation (ICC).
2.2

A Randomized Saturation Design

Suppose a researcher draws a sample of C clusters of size n.10 A randomized saturation (RS)design is a two-stage treatment assignment mechanism that specifies how to assign treatment
to these N ≡ nC individuals. The first stage randomizes the treatment saturation of eachcluster. Let Π ⊂ [0, 1] be a finite set of treatment saturations. Each cluster c is randomly
assigned a treatment saturation Pc ∈ Π according to the distribution f : Π → [0, 1], which
specifies the share of clusters assigned to each saturation. The second stage randomizes thetreatment status of each individual in the cluster, according to the realized saturation of thecluster. Each individual i in cluster c is randomly assigned treatment Tic ∈ {0, 1}, where
the realized cluster treatment saturation Pc specifies the share of individuals assigned to8
The analysis could be extended to allow for heteroskedasticity. In this case, the standard errors would
be less tractable to characterize analytically, and hence, optimal design results would also be less tractable.
We view the homoskedastic case as a natural benchmark to establish general insights about how RS designs
impact power.
9
See Duflo, Glennerster, and Kremer (2007) for these power expressions when there is no interference.
10
The RS design and studies discussed here use a simple, spatially defined definition of a cluster that ismutually exclusive and exhaustive. This is distinct from determining how to assign treatment in overlappingsocial networks (Aronow 2012), which requires a more complex sequential randomization routine (Toulis and
Kao 2013). An additional benefit of an RS design is that it also creates exogenous variation in the saturationof any overlapping network in which two individuals in the same cluster have a higher probability of being
linked than two individuals in different clusters.

6treatment (i.e.

∑ni=1 Tic = nPc for all c). Let Tc denote the realized treatment vector. An RS

design is completely characterized by the pair {Π, f }. The RS design nests several common
experimental designs, including the clustered, blocked, and partial population designs.11
We refer to individuals assigned to treatment as treated individuals, individuals in clusters
assigned saturation zero as pure controls and individuals who are not assigned to treatment
but are in clusters with treated individuals as within-cluster controls. Let Sic = 1{Tic =0, Pc > 0} be the random variable that denotes whether individual ic is a within-cluster
control and Cic = 1{Tic = 0, Pc = 0} be the random variable that denotes whether individual∑
ic is a pure control. An RS design has share of treated individuals µ ≡ p∈Π pf (p), share ofwithin-cluster control individuals µS ≡ 1 − µ − ψ, and share of control individuals ψ ≡ f (0).
A RS design has a pure control if ψ > 0.
In order to identify treatment and spillover effects, we must place a restriction on the
support of the RS design. We say a RS design is non-trivial if it has at least two saturations,at least one of which is strictly interior. Multiple saturations guarantee a comparison group
to determine whether effects vary with treatment saturation, and an interior saturation
guarantees the existence of within-cluster controls to identify spillovers on the untreated.
The blocked and clustered designs are trivial, and it is not possible to identify any spillover
effects in these designs, while the partial population design is non-trivial and it is possible
to identify spillover effects on the untreated.
An RS design introduces correlation between the treatment statuses of two individuals
in the same cluster,(Cor(Tic , Tjc ) =where η 2 ≡

∑

1
n−1

)(

)
nη 2
−1 ,
µ(1 − µ)22p∈Π p f (p) − µ denotes the variance of the cluster-level treatment saturation.

This variance in treatment saturation will play a key role in determining the power of an
RS design when there is correlation between the potential outcomes of individuals in thesame cluster, ρ > 0. At one extreme, a clustered design has perfect correlation between thetreatment statuses of individuals in the same cluster, r = 1, while at the other extreme, aFixing the share of treated individuals at µ, the clustered design corresponds to Π = {0, 1} and f (1) = µ,the blocked design corresponds to Π = {µ} and f (µ) = 1 and the partial population design corresponds toΠ = {0, P } and f (P ) = µ/P .
11

7

blocked design has slightly negative correlation, r = −1/(n−1).12 These two designs bracket
the continuum of RS designs, so it is natural that RS designs have an intermediate level ofcorrelation.
Discussion.

We implicitly assume that all individuals who are part of the spillover network

in a cluster are included in the sample. If this is not the case and spillovers occur on
individuals outside of the sampling frame, either because there is a ‘gateway to treatment’
within the cluster and not all eligible individuals are sampled, or because not all individuals
in a cluster’s spillover network are eligible for treatment, then it is necessary to distinguishbetween the true treatment saturation (the share of treated individuals in the cluster) and theassigned treatment saturation (the share of treated individuals out of sampled individuals
in the cluster).13 If the sampling rate and share of the cluster eligible for treatment are
constant across clusters, the true saturation is proportional to the assigned saturation. If
sampling rates are driven by cluster characteristics or the share of the cluster that is eligible
for treatment varies across clusters, then the true saturation is endogenous. In this case, theresearcher can instrument for the true saturation with the assigned saturation. To streamline
the analysis, we assume that the assigned and true saturations coincide.
Our framework can be applied to settings with perfect compliance or to identify intention
to treat effects in settings with imperfect compliance. While non-compliance does not bias
intention to treat estimands, it presents a second channel for interference – treatment andspillover effects may vary with saturation due to compliance effects or the direct impact of anindividual’s treatment on others. Exploring extensions considering compliance as a function
12
There are two sources of correlation in treatment status between individuals in the same cluster: (i)the correlation introduced by the variation in treatment saturation across clusters; (ii) when the share oftreated individuals in a cluster is fixed, then when an individual is selected for treatment, this reduces theprobability that another individual is selected for treatment i.e. conditional on realized treatment share
Pc , Cor(Tic , Tjc |Pc ) = −1/(n − 1). In a blocked design, the negative correlation stems from the fact that(ii) is the only source of correlation. If instead each individual in a cluster was independently treated withprobability Pc (sampling with replacement), then (ii) would not exist.
13
For example, Gine and Mansuri (forthcoming) sample every fourth household in a neighborhood, andrandomly offer treatment to 80 percent of these households. This causes the true treatment saturation
to be 20 percent rather than the assigned 80 percent. Other examples include unemployed individuals
on official unemployment registries form a small portion all unemployed individuals in an administrative
region (Crepon et al. 2013); neighborhoods eligible for infrastructure investments comprise only 3 percent
of all neighborhoods (McIntosh, Alegria, Ordonez, and Zenteno 2013); and malaria prevention efforts target
vulnerable individuals, who account for a small share of total cluster population (Killeen, Smith, Ferguson,
Mshinda, Abdulla et al. 2007).

8

of the assigned treatment saturation – and thereby defining a response function that depends
on whether individuals comply with assigned treatment – is an important avenue for future
research.
2.3

Treatment and Spillover Estimands

Next we define a set of estimands for treatment and spillover effects. We focus on average
effects across all individuals in the population. Recall that the population average potential
outcome at individual treatment assignment t ∈ {0, 1} and saturation p ∈ [0, 1] is Y (t, p).
Individuals offered treatment will experience a direct treatment effect from the program aswell as a spillover effect from the treatment of other individuals in their cluster. Let p ≡ 1/n
corresponds to a cluster with a single treated individual. The Treatment on the Uniquely
Treated (TUT) measures the intention to treat an individual, absent any spillover effects,
T U T ≡ Y (1, p) − Y (0, 0), and the Spillover on the Treated (ST) measures the spillover
effect at saturation p on individuals offered treatment, ST (p) ≡ Y (1, p) − Y (1, p). The
familiar Intention to Treat (ITT) is the sum of these two effects, IT T (p) = T U T + ST (p).
Individuals not offered treatment experience only a spillover effect. The Spillover on the NonTreated (SNT) is the analogue of the ST for individuals not offered treatment, SN T (p) ≡Y (0, p) − Y (0, 0). Given these definitions, there are spillover effects on the treated (nontreated) if there exists a p such that ST (p) ̸= 0 (SN T (p) ̸= 0).
We can also measure the rate of change in spillovers. The Slope of Spillovers on theTreated measures the rate of change of the spillover effect on treated individuals between
saturations pj and pk , DT (pj , pk ) ≡ (ST (pk ) − ST (pj ))/ (pk − pj ) . If spillover effects areaffine, then this is a measure of dST (p)/dp; otherwise, it is a first order approximationof the slope. The analogue slope effect for individuals not offered treatment is denoted
DN T (pj , pk ).
In the presence of spillovers, the true effectiveness of a program is measured by the total
effect of treatment on both treated and untreated individuals. The Total Causal Effect(TCE) measures this overall cluster-level effect on clusters treated at saturation p, comparedto pure control clusters, T CE(p) ≡ pIT T (p) + (1 − p)SN T (p). We say that treatment
effects are diversionary at saturation p if the benefits to treated individuals are offset by
negative externalities imposed on untreated individuals in the same cluster, IT T (p) > 0
9and T CE(p) < pIT T (p). Diversionary treatment effects redistribute value within a cluster
to treated individuals, and the true effectiveness of the program is muted compared to thedirect treatment effect captured in the ITT.14 If the TCE is negative, the program causes
an aggregate reduction in the average potential outcome, even though treatment effects may
be positive. In the presence of spillovers, it is imperative to use the TCE, rather than the
ITT, to inform policy, as the ITT may misrepresent the true effectiveness of the program.
We can also measure the direct impact of being assigned to treatment at a given saturation. The Value of Treatment (VT) measures the individual value of receiving treatment atsaturation p, V T (p) ≡ Y (1, p) − Y (0, p). If V T (p) is decreasing in p, then the value of treatment is decreasing in the share of other individuals treated and spillover effects substitute fortreatment, while if the VT is increasing in p, then the value of treatment is increasing in theshare of other individuals treated and treatment is complementary with spillover effects.15
Hudgens and Halloran (2008) also study causal inference in the presence of partial interference, and define a set of estimands for a finite population. The ST and SNT defined above
are the infinite population analogues of the indirect causal effects defined in their paper, the
ITT is the analogue of the total causal effect, the TCE is the analogue of their overall causal
effect and the VT is the analogue of their direct causal effect.
2.4

Examples of Spillovers

We illustrate the subtlety and importance of measuring spillover effects with three stylized
examples: measles vaccinations, deworming interventions and job training programs. Consider an intervention that vaccinates a share p of a cluster. The TUT measures the efficacyof the vaccination in isolation. The vaccination almost fully protects vaccinated individuals
independent of the treatment saturation, which means the IT T (p) is flat with respect top and spillovers on treated individuals, ST (p), are small. However, the protection to the
non-treated only becomes sizeable when the saturation is high enough to provide herd immunity, which means the SN T (p) varies from zero to one. Thus, the value of receiving the14

Of course, to say anything about the welfare implications of diversionary effects requires a welfare
criterion specifying the social value of different distributions of the outcome variable within a cluster.
15
If a RS design does not include a pure control, one could define analogous estimands for the ITT, SNT,TCE and VT relative to the lowest saturation in the study. For example, if clusters have a base saturationof share p0 individuals receiving a treatment before an intervention, a researcher could use estimands thatare defined relative to p0 .

10Figure 1. Examples
vaccination, V T (p), is very large when vaccination rates are low and approaches zero at highvaccination rates since the unvaccinated are protected by herd immunity. Positive spillovers
from treatment create a free-rider problem that may diminish the salience of vaccinations in
populations that have very high overall treatment levels. This is illustrated in the left panelof Figure 1.
Deworming provides a more challenging case. Reinfection rates are proportional to the
population prevalence of worm infections, which means that individuals who have received
deworming treatment will quickly become reinfected in environments with high prevalence.
The population saturation of deworming treatment drives long-term outcomes for both
treated and non-treated individuals, and effective deworming requires near universal treatment. The poignant irony of such a program is that the V T (p) is close to zero at all
saturations even though deworming can be effective if applied universally. The key featureof this setting is the positive externality of treatment on both non-treated and other treatedindividuals. This is illustrated in the center panel of Figure 1.
Another example is a job training program in which the training has no effect on theoverall supply of jobs – treatment simply diverts benefits from non-treated to treated individuals but provides little net benefit (Crepon et al. 2013). Similar examples are tutoring
programs for admissions to college or grant-writing workshops that improve specific proposals for a fixed funding pool. This type of diversionary treatment effect will have a T CE(p)that is zero for all p, even though the IT T (p) and especially the V T (p) are strictly positive.

11

In the face of diversionary effects, an RS design is imperative to identify the total policy
effect, which is zero. Using within-cluster controls as counterfactuals will yield mistaken
conclusions that the overall impact of a program is positive. This is illustrated in the rightpanel of Figure 1.

3Standard Errors and Optimal Design

This section maps the potential outcomes framework developed in Section 2.1 into a regression model that identifies the estimands defined in Section 2.3, derives analytical expressions
for the standard errors of the OLS estimates, and characterizes properties of the optimal RS
design to detect different sets of effects. We begin with the individual saturation and slope
estimands, and follow with complementary results for a model that pools multiple saturations. The section concludes with an illustration of the power trade-off between measuringslope and pooled effects.
3.1

Individual Saturation and Slope Effects

A Regression Framework.

A regression model to estimate treatment and spillover ef-

fects at each saturation in the support of an RS design (Π, f ) is∑

Yicobs = β0 +β1p Tic ∗ 1{Pc = p} +∑β2p Sic ∗ 1{Pc = p} + εic ,(1)p∈Π\{0}p∈Π\{0}where Yicobs ≡ Yic (Tc ) denotes the observed outcome for individual ic. To map the potential
outcomes framework into this model, we define the regression coefficients and error in termsof potential outcomes, population average potential outcomes and realized treatment status.
Let β0 ≡ Y (0, 0), β1p ≡ Y (1, p) − Y (0, 0) and β2p ≡ Y (0, p) − Y (0, 0).16 Define the error as
εic ≡

∑

(

1Tc =t Tic {Yic (t) − Y (1, p(t))} + Sic {Yic (t) − Y (0, p(t))})(2)

t∈{0,1}n \0n+ Cic {Yic (0n ) − Y (0, 0)},where p(t) is the share of treated individuals in treatment vector t. Athey and Imbens(2017) build a similar connection for a potential outcomes model with no interference andno intra-cluster correlation. The following lemma characterizes the distribution of the error
16

Note that we are not assuming a constant treatment effect when estimating (1) – β̂ is the averagetreatment or spillover effect.

12

in terms of the distribution of potential outcomes.
Lemma 1. Assume Assumptions 1 and 2. Then the error defined in (2) is strictly exogenous,
E[εic |Tc ] = 0, and has a block-diagonal variance-covariance matrix with E[ε2ic |Tc ] = σ 2 + τ 2 ,E[εic εjc |Tc ] = τ 2 for i ̸= j and E[εic εjd |Tc ] = 0 for c ̸= d.
Given Lemma 1, the OLS estimate of (1) will yield an unbiased estimate of β. For any RS
design with an interior saturation and a pure control, this estimate identifies ITˆT (p) = β̂1p ,ˆ T (p) = β̂2p , T CE(p)ˆSN= pβ̂1p + (1 − p)β̂2p and VˆT (p) = β̂1p − β̂2p for each p ∈ Π \ {0}.
Hudgens and Halloran (2008) present similar estimators for finite population estimands andshow these estimators are unbiased (Theorems 1 and 2).17 Tests for the presence of treatment
and spillover effects at saturation p are β̂1p ̸= 0 and β̂2p ̸= 0. A one-tailed test of the signof β̂2p determines whether treatment creates a negative or positive externality on untreatedindividuals, β̂1p ̸= β̂2p determines whether the value to treatment is non-zero and {β̂1p ≥0, β̂2p ≤ 0} tests for diversionary effects at saturation p.
We can also use (1) to estimate the slope effects. Given saturations pj and pk , the slope()
Teffect on individuals offered treatment is δjk≡ β1pk − β1pj / (pk − pj ) , with an analogous
S
expression for the slope effect on within-cluster controls, δjk. A pure control is not required– any RS design with two interior saturations identifies the slope effect for both treatment
and within-cluster control individuals. To estimate the slope effect in a design with no pure
control, replace the control group with the within-cluster controls in the lowest saturationin the RS design, and redefine the coefficients in (1) to be relative to the population meanof untreated individuals at the lowest saturation.18
Standard Errors.

Our first result characterizes the standard errors (SEs) for the esti-mates of the individual saturation effects and slope effects from (1). This illustrates how thestandard errors depend on the RS design.19

17

In Hudgens and Halloran (2008), the sample is equal to the population and uncertainty stems fromunobserved potential outcomes. Our model is defined for an infinite population, and uncertainty stems fromboth unobserved potential outcomes and sampling uncertainty. Minor technical modifications to their proofs
establish the analogous results in our setting.
18
This model also allows for tests on the shape of the IT T (p) and SN T (p). For example, three interior
saturations allows one to test for concavity or convexity.
19
Using these expressions to inform experimental design requires estimates of τ 2 and σ 2 . One could use
existing observational data or conduct a small pilot experiment (Hahn, Hirano, and Karlan 2011).

13

Theorem 1 (Individual Saturation and Slope SEs). Assume Assumptions 1 and 2. For any
RS design (Π, f ) with a pure control, the SE of the treatment effect at saturation p is
√
{ (
)
(
)}
τ 2 + σ2
1
1
1
1
SEIT T (p) =∗ nρ++ (1 − ρ)+nC
f (p) ψpf (p) ψfor each p ∈ Π. For any RS design (Π, f ) with κ ≥ 2 interior saturations, the SE for theslope effect on treated individuals between saturations pj > 0 and pk > 0 is
√
( (
)
(
))
1
1
1
τ 2 + σ211∗ nρ++ (1 − ρ)+
SEDT (pj , pk ) =pk − pjnC
f (pj ) f (pk )pj f (pj ) pk f (pk )Substituting (1 − p)f (p) for pf (p) yields analogous expressions for untreated individuals,
denoted SESN T (p) (for p ∈ (0, 1)) and SEDN T (pj , pk ).
Theorem 1 illustrates the relationship between the correlation structure of outcomes and theprecision of estimates in an RS design. At one extreme, if there is no correlation (ρ = 0),
the variation in ITˆT (p) depends on the share of treated individuals at saturation p, pf (p),and the share of control individuals, ψ. There is no correlation between potential outcomes
within a cluster, so observing Yic (1, p) for treated individual i provides no information about
the potential outcome Yjc (1, p) for untreated individual j and the share of within-cluster
control individuals at saturation p is irrelevant for SEIT T . At the other extreme, if there isperfect correlation (ρ = 1), the variation in ITˆT (p) depends on the total share of individuals
at saturation p, f (p), and the share of control individuals. Within a cluster, there is perfect correlation between individuals’ potential outcomes and observing Yic (1, p) for treatedindividual i provides perfect information about the potential outcome Yjc (1, p) for untreatedindividual j. At intermediate levels of correlation, SEIT T depends on a weighted average ofthe share of treated individuals and the total share of individuals at saturation p.
Next consider the standard error of the slope effect. As the distance between two saturations increases, 1/(pk − pj ) decreases, making it possible to detect smaller slope effects. At
the same time, increasing the spread of saturations makes the number of treatment (withincluster control) individuals very small at low (high) saturations. The former effect dominates
at saturations close to 1/2, and spreading the saturations apart decreases the SE, while thelatter effect dominates at saturations close to zero or one, and spreading the saturations
apart increases the SE. When ρ is large, the share of clusters assigned to each saturation,14

f (pj ) and f (pk ), play a larger role in determining the SE; a more equal distribution leads
to a smaller SE. When ρ is small, the share of treatment (within-cluster control) individuals
assigned to each saturation, pj f (pj ) and pk f (pk ) ((1 − pj )f (pj ) and (1 − pk )f (pk )), are more
important; a more equal share leads to a smaller SE.
Theorem 1 can be used to characterize the power of an RS design. The minimum detectable effect (MDE) is the smallest value of an estimand that it is possible to distinguishfrom zero (Bloom 1995). Given statistical significance level α, the null hypothesis of notreatment effect at saturation p is rejected with probability γ (the power) for values of β1pthat exceed MDE = (t1−γ + tα ) × SE(β̂1p ). The expressions for the MDEs of the spillover
effect on untreated individuals and the slope effects are analogous.
In general, the OLS estimator is inefficient when errors are correlated. The variance of
the OLS estimate characterized in Theorem 1 will be conservative if GLS or another more
efficient estimator is used to analyze the resulting data.
Optimal Design: Individual Saturation Effects.

Given a set of saturations Π, thedesign choice for measuring individual saturation effects involves choosing the share of clusters to allocate to each saturation. If the researcher places equal weight on the treatment andspillover effect at each saturation, she chooses f to minimize the sum of standard errors,20
min
f

∑

(SEIT T (p) + SESN T (p)) .

(3)p∈Π\{0}First consider the choice of how many clusters to allocate to each positive saturation. By
design, extreme saturations have more uneven shares of treatment and within-cluster control
individuals, relative to saturations closer to 1/2. A researcher who places equal weight onmeasuring effects at each saturation in Π will want to allocate a larger share of clusters tothese more extreme saturations. This stems directly from the concavity of the SE. As ρ
increases, this asymmetry in the optimal f is muted since within-cluster control individuals
provide information about treated individuals, and vice versa, and the uneven shares oftreatment and within-cluster control individuals has a smaller impact on the precision of
estimates
20

This is equivalent to maximizing the probability of rejection for a test of the null of no effect i.e.
minimizing the minimum detectable effect.

15

Next, consider the optimal control group size. The marginal impact of adding anothercluster to the control reduces all terms in (3), while the marginal impact of adding anothercluster to an interior saturation only reduces the SEs at that saturation. Therefore, theoptimal share of individuals allocated to the control group is always larger than the smallest
share of individuals at any treatment saturation. The optimal control size increases with ρ– when the outcomes of treated and within-cluster control individuals are more correlated,the optimal f allocates a smaller share of clusters to each positive treatment saturation.
Corollary 1 formalizes these insights.
Corollary 1. Fix a set of saturations Π. Let f ∗ minimize (3), with ψ ∗ ≡ f ∗ (0).
1. A larger share of clusters are allocated to more extreme saturations: given p1 , p2 ∈
Π \ {0} such that |0.5 − p1 | > |0.5 − p2 |, f ∗ (p1 ) > f ∗ (p2 ). The difference in the shareof clusters at each saturation, f ∗ (p1 ) − f ∗ (p2 ), is decreasing in ρ.
2. The share of individuals assigned to pure control is larger than the share of treated orwithin-cluster control individuals at any positive treatment saturation, ψ ∗ > min{p, 1 −p}f ∗ (p) for all interior saturations p ∈ Π.
3. For each interior saturation p ∈ Π, f ∗ (p) is decreasing in ρ, and ψ ∗ is increasing in ρ.
For a given intra-cluster correlation ρ and cluster size n, it is straightforward to numericallysolve for the optimal share of clusters to assign to each saturation.
Optimal Design: Slope Effects.

There are two steps to the design choice to measureslope effects: selecting the set of saturations Π and choosing the share of clusters to allocate
to each saturation. Suppose a researcher is interested in measuring the slope effect, sheplaces equal weight on estimating the slope effect for treated and untreated individuals, andshe believes that the slope effects are monotonic. Then she chooses an RS design to solvemin
p1 ,p2 ,f (p1 )SEDT (p1 , p2 ) + SEDN T (p1 , p2 ).

(4)

The optimal saturations are symmetric about one half, an equal share of clusters are allocatedto each saturation, and the optimal distance between saturations is increasing in ρ.
Corollary 2 (Optimal Saturations). The RS design that minimizes (4) equally divides clusters between two saturations symmetric about 1/2, p∗1 = (1 − ∆)/2 and p∗2 = (1 + ∆)/2, where
16the optimal distance between saturations ∆ ∈(√)
2/2, 1 satisfies

2∆2 − 1nρ=.
2(1 − ρ)∆(1 − ∆2 )2
If ρ = 0, then ∆ =√2/2 for all n, ∆ is increasing in ρ and n, and if ρ = 1, then ∆ = 1−2/n.

Note that this optimal design equalizes the standard errors, SEDT (p∗j , p∗k ) = SEDN T (p∗j , p∗k ).
More generally, if a researcher is interested in identifying individual saturation or slope
effects at or between more than two saturations, Theorem 1 can be used to answer questions
like what is the optimal spacing of saturations and what share of clusters should be assigned
to each saturation. For example, suppose a researcher would like to test for linearity byincluding three saturations. To minimize the analogue of (4), one saturation should be 1/2
and the other two should be spaced symmetrically about one half. A larger share of clusters
should be allocated to the extreme saturations relative to saturation 1/2.
3.2

Pooled Effects

Suppose the researcher would like to combine observations from clusters with different saturations to measure an average of different estimands across all saturations in the RS design.
What we refer to as a pooled estimand is a weighted sum of the estimand at each individual
saturation. Given design (Π, f ) and vector of weights w : Π → [0, 1], a pooled ITT that∑assigns weight w(p) to IT T (p) is IT T ≡ Π\{0} w(p)IT T (p). The definitions for ST , SN T ,T CE and V T are analogous.
A Regression Framework.

A regression model to estimate pooled effects isYicobs = β0 + β1 Tic + β2 Sic + εic .

(5)

As in Section 3.1, we map the potential outcomes framework into this model by defining theregression coefficients and error in terms of potential outcomes and treatment status. Let∑∑
Y (1) ≡ µ1 p∈Π\{0} pf (p)Y (1, p) and Y (0) ≡ µ1S p∈Π\{0} (1−p)f (p)Y (0, p) be the population
average potential outcome averaged across all non-zero saturations in the RS design, whent = 1 and t = 0, respectively. Let β0 ≡ Y (0, 0), β1 ≡ Y (1) − Y (0, 0) and β2 ≡ Y (0) − Y (0, 0).

17

Define the error asεic ≡ Tic {Yic (1, T−i,c ) − Y (1)} + Sic {Yic (0, T−i,c ) − Y (0)} + Cic {Yic (0n ) − Y (0, 0)},(6)

where T−i,c is the treatment vector for individuals j ̸= i in cluster c. The following Lemma
characterizes the distribution of the error in terms of the distribution of potential outcomes
and the structure of the RS design.
Lemma 2. Under Assumptions 1 and 2, the error defined in (6) is strictly exogenous,
E[εic |Tc ] = 0, uncorrelated across clusters, and has within-cluster variance-covariance matrix
specified as follows:
1. Treated clusters: the variance for treated individuals is Var(ε2ic ) = σ 2 + τ 2 + ϕT and for
untreated individuals is Var(ε2ic ) = σ 2 + τ 2 + ϕS . The covariance is Cov(εic , εjc ) = τ 2 +ϕT T between treated individuals, Cov(εic , εjc ) = τ 2 + ϕSS between untreated individuals,
and Cov(εic , εjc ) = τ 2 + ϕT S between a treated and untreated individual.
2. Control clusters: the variance is Var(εic ) = σ 2 and the covariance is Cov(εic , εjc ) = τ 2 .
∑where ϕT ≡ µ1 p∈Π\{0} pf (p)Y (1, p)2 − Y (1)2 captures the variation in Y (1, ·) across saturations in the RS design, with analogous definitions for ϕS , ϕT T , ϕT S and ϕSS .
By Lemma 2, the OLS estimate of (5) will yield an unbiased estimate of β for any RS design
with an interior saturation and a pure control.
The interpretation of β is somewhat subtle and depends on the RS design. When observations are pooled across saturations, βˆ1 places a disproportionate weight on treatedindividuals in high saturation clusters relative to low saturation clusters – it is an estimateof the pooled ITT with weight w(p) = pf (p). Similarly, βˆ2 places a disproportionate weighton untreated individuals in low saturation clusters relative to high saturation clusters – itis an estimate of the pooled SNT with weight w(p) = (1 − p)f (p). Due to these different
weights, a comparison of the two pooled measures does not have a natural interpretation.
Additionally, one must be careful when combining these estimates to identify other effects.
For example, βˆ1 + β̂2 is a pooled measure of the TCE with weight w(p) = f (p), but βˆ1 − β̂2
is not a pooled measure of the VT.21
21

What we call saturation weights, which have a similar interpretation to sampling weights, can be used
to adjust for the different probability of being assigned to treatment at each saturation. To estimate a18

Pooling observations across multiple saturations introduces the possibility of heteroskedasticity. Lemma 2 characterizes the precise form of this heteroskedasticity, which depends onthe expected potential outcome at each saturation in the RS design. When IT T (p) andSN T (p) are relatively flat, the heteroskedasticity will be small, whereas when these estimands vary with the intensity of treatment, the heteroskedasticity will be more significant.
The error is homoskedastic precisely when the expected potential outcomes do not vary withthe treatment saturations in the RS design.
Definition 1. Treatment and spillover effects are constant on Π if for all pj , pk ∈ Π,
Y (1, pj ) = Y (1, pk ) and Y (0, pj ) = Y (0, pk ).
Corollary 3. Given saturations Π, the error has a block-diagonal variance-covariance matrix
if and only if treatment and spillover effects are constant on Π.
Generally, cluster robust standard errors should be used in two-level experiments due to thedesign effect. This corollary provides an additional argument for doing so when estimating(5) due to the variation in treatment and spillover effects at different saturations.
Standard Errors.

Since an RS design opens the door to a novel set of questions about

how treatment and spillover effects vary with intensity of treatment, and still identifies
pooled treatment and spillover effects, it may be tempting to conclude that there is no
reason not to run an RS design. If there are slope effects, then the heteroskedastic errors
in the pooled regression are not an important issue, as the researcher is more interested
in the individual saturation model (1), while if no slope effects emerge, then the pooledmodel is homoskedastic and there is no need to worry about multiple treatment saturations
introducing heteroskedasticity that reduces the precision of estimates. However, this line ofreasoning misses a crucial piece of the story. Next, we show that including multiple treatment
saturations increases the standard errors of pooled estimates, even when the treatment andspillover effects are constant, so that the error in (5) is homoskedastic.
pooled IT T and SN T that places equal weight w(p) = 1/|Π| on the treatment or spillover estimand at eachsaturation, estimate (5) with weights sic = 1/Pc f (Pc ) for treated individuals and weight sic = 1/(1−Pc )f (Pc )for within-cluster controls. Using these weights, βˆ1 − β̂2 is now a pooled measure of the VT that places equal
weight on each saturation, but βˆ1 + β̂2 is no longer a pooled measure of the TCE. For example, consider adesign with three saturations, Π = {0, 1/3, 2/3} and an equal share of clusters assigned to each saturation,f (p) = 1/3 for each p ∈ Π. An individual in a cluster assigned p = 2/3 is twice as likely to be assigned totreatment as a cluster assigned p = 1/3. Weighting the treated individuals in clusters assigned p = 1/3 andp = 2/3 by sic = 3 and sic = 3/2, respectively, allows one to calculate the pooled estimate that places equal
weight on both clusters, rather than twice as much weight on the p = 2/3 clusters.

19

Let ηT2 be the component of the variance in treatment saturation across clusters thatarises from multiple non-zero saturations,()∑ p2 f (p) ( µ )2 ( 1 )
ψ
2
2
ηT ≡
−
=
η −
µ2
1−ψ
1−ψ
1−ψ
(1 − ψ)2(7)

p∈Π\{0}where f (p)/(1 − ψ) is the distribution of treatment saturation conditional on p > 0, withsupport Π\{0}, and η 2 is the total variance in treatment saturation. Trivially, ηT2 = 0 when
there is a single non-zero saturation.
In order to isolate the impact that variance in treatment saturation has on the SE for
the pooled ITT and SNT, we focus on the case where spillover and treatment effects areconstant across all saturations in the RS design.
Theorem 2 (Pooled SE). Let (Π, f ) be an RS design with an interior saturation and a pure
control. Assume Assumptions 1, 2 and treatment and spillover effects are constant on Π.
The SE of IT T is:
√
( (
(
) )
(
))
1
1−ψ
1
τ 2 + σ2
1
SEIT T =nρ+ηT2 + (1 − ρ)+.
nC
(1 − ψ) ψµ2µ ψ
Substituting µS for µ yields an analogous expression for the SE of SN T , denoted SESN T .
The SE for the pooled estimands depends on the size of the treatment and control groups andthe within-cluster variation in treatment status. Crucially, when outcomes within clusters
are correlated (ρ > 0), the SE is strictly increasing in the variation in treatment saturation
ηT2 and introducing multiple treatment saturations reduces precision. Standard errors areminimized in a partial population design in which there is a single treatment saturation anda pure control. This design has no variation in treatment saturation, ηT2 = 0.
Corollary 4 (Optimality of Partial Population Design). Suppose ρ > 0. For any (µ, ψ),the partial population design with treatment saturation p = µ/(1 − ψ) and a pure control
simultaneously minimizes SEIT T and SESN T .
Moving away from the partial population design to a design with variation in the treatment
saturation, the power loss is more severe for settings with higher intra-cluster correlation.
The variance of β̂ increases linearly with respect to ηT2 and the rate at which this varianceincreases is proportional to ρ. Therefore, if the researcher a priori believes that slope effects
20

Figure 2. Partial Population Design
are small and intra-cluster correlation is high, she is best off selecting a partial population
design. The next subsection explores which partial population design to choose.
Optimal Partial Population Design.

Consider the optimal treatment saturation p andcontrol size ψ for a partial population design. The SE of the ITT decreases with p, while
the SE of the SNT increases with p. The relative importance of detecting these two effects,
as well as their expected magnitudes, will determine the optimal choice of p. If a researcher
places equal weight on each effect,
min SEIT T (p, ψ) + SESN T (p, ψ),

(8)

(p,ψ)

then the optimal saturation creates equally sized treatment and within-cluster control groups
by choosing p∗ = 0.5. The left panel of Figure 2 illustrates the SEs in a partial population
design, as a function of p. Note SEIT T (0.5, ψ) = SESN T (0.5, ψ).
The optimal share of control clusters depends on ρ and n. As ρ increases, the optimal
share of control clusters also increases – within-cluster controls and treated individuals provide more information about each other, and the total number of clusters in each treatmentgroup becomes more important for statistical power than the total number of individuals ineach treatment group. In a partial population design with saturation 0.5, it is always optimal to allocate more than a third of clusters to the pure control as the control serves as thecounterfactual for both treatment and spillover groups; designating about 41% of clusters as
pure controls yields the smallest SE when ρ = 0, while designating 50% is preferable when21

Figure 3. Trade-off between SEs of Pooled and Slope Estimands
ρ = 1. Corollary 5 summarizes these results.
Corollary 5. The partial population design that minimizes (8) has saturation p∗ = 0.5 andallocates share
√
√
−(1
+
(n
−
1)ρ)
+
(1 + (n − 1)ρ)2 + (1 − ρ)(1 + (n − 1)ρ)ψ∗ =∈ [ 2 − 1, 1/2)
1−ρof clusters to pure control for ρ ∈ [0, 1) and ψ ∗ = 1/2 for ρ = 1. The optimal share of control
clusters ψ ∗ is increasing in ρ and n.
The right panel of Figure 2 illustrates how the SEs in a partial population design withsaturation 0.5 (note they are equal) depend on the control group size when ρ = 0 and ρ = 1.
The minimum in each case is marked with an asterisk. Corollary 5 is similar in spirit to
Hirano and Hahn (2010). They show that a partial population design identifies the IT T
and SN T in a linear-in-means model when ρ = 0, and establish that the optimal treatment√
saturation is p∗ = 0.5 and the optimal control group size is ψ ∗ = 2 − 1.
3.3

The Design Trade-off.

Taken together, the results in Sections 3 provide important insights on experimental design.
Clustering of outcomes can be due to either correlated effects or interference between units.
Theorems 1 and 2 show that the source of clustering plays an important role in determining
the power of different designs. The optimal design depends crucially on the degree of intracluster correlation and the degree to which individual effects vary with intensity of treatment– precisely the two underlying factors that drive clustering of outcomes.
22

If the researcher has a strong prior belief that spillover effects are relatively flat withrespect to treatment intensity but ρ is high, then choosing an RS design with multiple
treatment saturations will reduce statistical power without yielding novel insights and theresearcher is better off running a partial population design. However, partial population
designs have the drawback that they only measure effects at a single saturation. When aresearcher seeks to identify or rule out slope effects, she will need to introduce variation in
the treatment saturation. A graphical representation of the tradeoff in precision between
measuring pooled and slope effects is presented in Figure 3.
Moreover, if the researcher is primarily interested in identifying slope effects, a design
with no pure control is optimal. But such a design cannot identify treatment and spillover
effects at any individual saturation. Thus, the optimal RS design for a slope analysis stands
in sharp contrast to that for an analysis at individual saturations or a pooled analysis. If theresearcher seeks to identify both slope and individual effects, the optimal design will dependon the relative importance that the researcher places on each effect.

4

Application

This section illustrates our results by characterizing the optimal design for different hypothetical objective functions and calculating the power of RS designs from published studies
in economics and political science. These examples quantify the power trade-offs that arise
between measuring individual, slope and pooled effects. The calculations are conductedusing code we developed as a tool for researchers.22
First, suppose a researcher uses a clustered design to identify the average treatment effect.
She selects C = 100 clusters, each of which contain n = 10 individuals, and is interested
in the precision of her estimate of the ITT. She implements the optimal clustered design,
which assigns 50% of the clusters to the control group and 50% to the treatment groupand identifies IT T (1). The SE of IT T (1) depends on the intra-cluster correlation, ρ, andis measured in standard deviations.

When ρ = 0, SEIT T (1) = 0.063. It increases with ρ,

rising to 0.087 when ρ = 0.1 and 0.200 when ρ = 1 (Table 1, Columns 1-3). The researcher
cannot identify any spillover effects on treated or untreated individuals.
22

We created a Graphical User Interface (GUI) to answer many optimal design questions and calculate
power for a given RS design. Code in R and Python is also available to conduct numerical optimization for
more complex design questions. All code is available at http://pdel.ucsd.edu/solutions/index.html.

23

Table 1. Optimal Design to Detect Pooled Effects
BENCHMARK: CLUSTERED DESIGN
min SE_ITTPARTIAL POPULATION DESIGN
min SE_ITT + SE_SNTmin SE_ITT+ 2*SE_SNTmin SE_SNT
s.t.
SE_ITT≤0.09

0.1
0.00
0.41
0.45
0.55
0.100
0.094

0.1
0.00
0.78
0.47
0.53
0.090
0.117

Objective Function
ICC: ρ
Optimal saturation 1: pure control
Optimal saturation 2: p2
Optimal share in pure control: ψ
Optimal share in p2
SE of pooled ITT
SE of pooled SNT

0
0.00
1.00
0.50
0.50
0.063
.

0.1
0.00
1.00
0.50
0.50
0.087
.

1
0.00
1.00
0.50
0.50
0.200
.

0
0.00
0.50
0.41
0.59
0.076
0.076

0.1
0.00
0.50
0.45
0.55
0.097
0.097

1
0.00
0.50
0.50
0.50
0.200
0.200

Other parameters: C=100, n=10

Next, suppose that the researcher also would like to measure spillover effects on untreatedindividuals and cares equally about the precision of the estimates of the pooled ITT andpooled SNT. Applying Corollary 4, the optimal design is a partial population experiment(PPE), Π = {0, p} and f = {ψ, 1 − ψ}. This design identifies IT T (p) and SN T (p). From
Corollary 5, we know that when the researcher places equal weight on minimizing the SEIT T
and SESN T , the optimal treatment saturation is p∗ = 0.5, meaning that half of the individuals
in each treatment cluster are assigned to treatment, and the optimal share of control clusters
ranges from ψ ∗ = 41% to 50% as ρ increases from 0 to 1 (Table 1, Columns 4-6). The SE
for the ITT and SNT are equal, SEIT T (0.5) = SESN T (0.5), and range from 0.076 to 0.200 as
ρ increases from 0 to 1. Hence, when the researcher wants to detect spillovers on untreatedindividuals, the SE for the ITT rises. The source of this power loss is obvious: it stems fromreassigning some treatment and control individuals to serve as within-cluster controls. The
power loss is decreasing in ρ, as within-cluster control individuals provide more information
about treated individuals for high ρ.
Now suppose the researcher wants to detect a pooled SNT that is smaller or larger thanthe pooled ITT. A partial population experiment remains optimal, but now the optimaltreatment saturation and control group size minimizes
min θSEIT T (p) + (1 − θ)SESN T (p),p,ψwhere θ ∈ [0, 1] is the relative weight that the researcher places on detecting treatment versus
spillover effects. When ρ = 0.1 and θ = 1/3, the optimal treatment saturation is p∗ = 0.41,

24

Table 2. Optimal Design to Detect Slope Effects and SE in Existing Studies
OPTIMAL RS DESIGNSmin SE_ITTBanerjee et+ SE_SNT
al. & Crepon Sinclair et al.
+ SE_DTet al.
+ SE_DNT

min SE_DT + SE_DNTObjective Function
ICC: ρ
Saturation 1: p1
Saturation 2: p2
Saturation 2: p3
Saturation 2: p4
Saturation 2: p5
Share in p1
Share in p2
Share in p3
Share in p4
Share in p5
SE of pooled ITT
SE of pooled SNT
SE of Treated slope
SE of Untreated slope

0
0.15
0.85
.
.
.
0.50
0.50
.
.
.
.
.
0.179
0.179

0.1
0.13
0.87

.
.
.
0.50
0.50

.
.
.
.
.
0.191
0.191

EXISTING STUDIES11/n(n-1)/n
.
.
.
0.50
0.50
.
.
.
.
.
0.204
0.204

0.1
0.00
0.21
0.88
.
.
0.28
0.33
0.39
.
.
0.104
0.109
0.217
0.192

0.1
0.00
0.25
0.50
0.75
1.00
0.20
0.20
0.20
0.20
0.20
0.113
0.120
0.240
0.240

0.1
0.00
0.10
0.50
1.00
.
0.25
0.25
0.25
0.25
.
0.109
0.111
0.242
0.274

Baird et al.

Baird et al. sat;shares solve
min SE_SNT
s.t.
SE_ITT≤.095

0.1
0.00
0.33
0.67
1.00
.
0.55
0.15
0.15
0.15
.
0.095
0.115
0.289
0.251

0.1
0.00
0.33
0.67
1.00
.
0.45
0.21
0.21
0.13
.
0.095
0.106
0.269
0.221

Other parameters: C=100, n=10

meaning 41% of individuals in a treatment cluster are assigned to treatment (Table 1, Column
7). The optimal share of clusters allocated to the control group is ψ ∗ = .45, as was the casefor θ = 1/2 and ρ = 0.1. This produces SEIT T (.41) = 0.100 and SESN T (.41) = 0.094.23
Alternatively, if the researcher wants to minimize the SE of the SNT, while maintaining a
SE for the pooled ITT of 0.09 or lower (approximately the SE in the clustered design), thenshe would use treatment saturation p∗ = 0.78 and share of control clusters ψ ∗ = .47. This
would yield a higher standard error for the spillover effect on the non-treated, 0.117 (Table
1, Column 8).
Next, suppose the researcher wishes to estimate the slope effect for treated and untreatedindividuals, and does not care about identifying the individual or pooled ITT and SNT. Thenthe optimal design will have two interior saturations and no pure control group. She chooses
a design to solve
min SEDT (p1 , p2 , f ) + SEDN T (p1 , p2 , f ).

p1 ,p2 ,f

By Corollary 2, the optimal saturations are symmetric about 0.5 and clusters equally divided
between these two saturations. When ρ = 0, the optimal saturations are p∗1 = 0.15 andp∗2 = 0.85. This produces a SE of 0.179 for both the treated and non-treated individuals(Table 2, Column 1). Increasing ρ moves the optimal saturations further apart and increases
23

Moving to a more extreme θ = 1/10 does not alter the share of clusters allocated to pure control
substantively (ψ ∗ = 47%), but significantly reduces the optimal treatment saturation (p∗ = 0.23).

25

the SEs for the slope effects (Table 2, Columns 2 - 3). At the extreme, when outcomes withina cluster are perfectly correlated (ρ = 1), the optimal saturations are as far apart as possible
while still maintaining at least one treated and one within-cluster control individual in eachcluster. This corresponds to saturations p∗1 = 1/n and p∗2 = (n − 1)/n.
However, not many researchers are interested in designing an experiment to maximize theprecision of slope estimands, at the expense of not being able to identify standard estimands,
such as the ITT. To give a sense of the optimal design when the researcher would like to havea pure control group along with two interior saturations, we consider an objective functionthat puts equal weights on both the pooled and slope effects,
min SEIT T + SESN T + SEDT (p1 , p2 , f ) + SEDN T (0, p2 , f ).

p1 ,p2 ,fWhen ρ = 0.1, it is optimal to allocate 33% of the clusters to saturation p∗1 = 0.21, 39%
to saturation p∗2 = 0.88, and the remaining ψ ∗ = 28% to the pure control group, i.e. Π∗ ={0, 0.21, 0.88} and f ∗ = {0.28, 0.33, 0.39} (Table 2, Column 4).24 The calculated SEs of
0.104 and 0.109 for the pooled ITT and SNT, respectively, indicate an 7-13% increase in theSEs compared to the optimal partial population design using the same parameters (Table
1, Column 5).25 Unlike the precision loss that arises when moving from a clustered to apartial population design, the precision loss in moving from a partial population design toa RS design with two interior saturations arises from the increased variance of treatment
saturations, rather than a reduction in sample size. It is precisely this variance in treatment
saturation that enables identification of slope effects.
Finally, we calculate the standard errors in RS designs used by three published studies.
To facilitate comparability with the optimal designs discussed above, we use the same numberof clusters (C = 100), individuals per cluster (n = 10) and intra-cluster correlation (ρ = 0.1)
24

The careful reader might note that the optimal interior saturations are not symmetric about 0.5, as
would be the case if we were solely interested in minimizing detectable slope effects. In this example, a pure
control group is included to identify the ITT and SNT. Furthermore, at 27%, the size of the optimal control
group is smaller than the control group size that minimizes the sum of the individual SEs for the ITT and
SNT (Corollary 1).
25
The SEDT is larger than in the optimal slope design in Column 2 because the distance between saturations for treated individuals is smaller in this design, and fewer clusters are allocated to the saturations that
identify the DT i.e. 0.21 and 0.88. The SEDN T is approximately the same as in the optimal slope design inColumn 2 – the distance between the saturations for untreated individuals is larger, but fewer clusters areallocated to the highest saturation, 0.88.

26

as in our examples, rather than the actual values from each study.26
We begin with the RS design used in Banerjee et al. (2012) and Crepon et al. (2013).
Clusters were assigned to a pure control group and four equally spaced treatment saturations
in equal shares, Π = {0, 0.25, 0.50, 0.75, 1} and f = {0.2, 0.2, 0.2, 0.2, 0.2}. By virtue of
having a pure control group and more than two interior saturations, this study design canidentify the ITT and SNT (pooled and saturation-specific) effects, slope effects and test
for the shapes of IT T (p) and SN T (p). The cell with 100% treatment saturation allows
for examination of general equilibrium effects when everyone in the target population istreated, compared with the partial equilibrium effects in lower saturation cells. Our power
calculations for this design yield SEIT T = 0.113, SESN T = 0.120, and SEDT = SEDN T =0.240 (Table 2, Column 5). All of these figures are higher than their counterparts under
the optimal design for minimizing the sum of these four variables (Table 2, Column 4),
demonstrating the power loss that arises from having a richer, more granular design thatcan, for example, test for concavity of IT T (p) and SN T (p).
Our next example is the design used by Sinclair et al. (2012). They randomized ninedigit zip codes in a congressional district in Illinois into a pure control and three different
saturations: Π = {0, 1/n, 0.50, 1} and f = {0.25, 0.25, 0.25, 0.25}, where 1/n is the saturationin which only one household is treated.27 In addition to the estimands that can be identified
in Banerjee et al. (2012) and Crepon et al. (2013), this design can also identify the TUT and
the ST (p) for p = 0.5 and p = 1. Our power calculations for this design yield SEIT T = .109,
SESN T = 0.111, SEDT = 0.242 and SEDN T = 0.274, respectively (Table 2, Column 6). The
pooled SEs are quite similar to their counterparts under the optimal design for minimizing thesum of these four quantities (Table 2, Column 4), but the slope effect SEs are substantiallyhigher, particularly for the non-treated (0.274 vs. 0.192), because the largest saturation
26
The pooled SEs in columns 4-8 are calculated for a model with constant treatment and spillover effects,
which implies homoskedastic errors. These are lower bounds for the pooled SEs when treatment and spillover
effects are not constant, and therefore, errors are heteroskedastic. Even if it is not possible to reject the null
hypothesis of a zero slope effect, there may still be a small slope effect that creates heteroskedasticity. For
example, in column 4, the design is powered to detect treatment slope effects larger than 0.62. Suppose thetrue slope is 0.5. It will not be possible to reject the null hypothesis that the slope is zero, but there will
still be heteroskedasticity and the pooled SE for treated individuals will be strictly larger than 0.104 whichis the pooled SE for a ITT effect of zero. To account for this, researchers should build some sample size
cushion into their designs.
27
The saturation of 0.5 is approximate, as one core household plus half of the remaining households wererandomly assigned to treatment in clusters assigned to that saturation.

27

containing within-cluster controls is 0.5.
Our final example is Baird, McIntosh, and Özler (2011), which has a pure control andthree positive saturations, Π = {0, 0.33, 0.67, 1} and f = {0.55, 0.15, 0.15, 0.15}. While thesaturations in this design are also equally spaced, they are not equally sized: the pure control
group, at 55% of clusters, is much larger than the share assigned to any treatment saturation. The combination of having a larger control group and smaller variation in treatment
saturations produces SEs for the pooled ITT that are smaller than those in Banerjee et al.
(2012) and Crepon et al. (2013), but higher SEs for the slope effects, particularly for treatedindividuals (Table 2, Column 7). The SE for the pooled SNT is 2 percentage points (or 21%)higher than that for the ITT, indicating that the pooled spillover effects on the untreatedare underpowered relative to the pooled treatment effects.
Given this large difference between SEs for the pooled ITT and SNT, we can ask whether
there is a way to allocate clusters to this set of saturations that leads to both lower pooled
and slope SEs. Consider the objective function that minimizes the SE of the SNT, subject
to the constraint that the SE of the ITT remains below its value in the original study design,
minf SESN T subject to SEIT T ≤ 0.095. The optimal distribution of treatment saturations forthis objective allocates a lower share of clusters to the pure control group and to saturationp = 1, and a higher share to the two interior saturations, 1/3 and 2/3 (Table 2, Column
8). Such a design dominates the original study design, as it not only lowers the SE for thepooled SNT, but also decreases the SEs of the slope effects. As we kept Π fixed, the improved
precision comes from redistributing clusters more efficiently between different treatment
saturations, particularly by reallocating clusters from the pure control to interior saturations.

5

Conclusion

In recent years, empirical researchers have become increasingly interested in studying interference between subjects. Experiments designed to rigorously estimate spillovers open up afascinating set of research questions and provide policy-relevant information about program
design. For example, if a vaccination or a bed net distribution program with fixed resources
can either treat 50% of all villages or 100% of half of them, which treatment allocation will
maximize the total benefit? Small policy trials conducted on a subset of the population canmiss important scale or congestion effects that will accompany the full-scale implementa28

tion of a program. RCTs that fail to account for spillovers can produce biased estimates ofintention-to-treat effects, while finding meaningful treatment effects but failing to observe
deleterious spillovers can lead to misconstrued policy conclusions. Varying the cluster-level
saturation can lead to differential impacts on prices, norms, and congestion effects. The RS
design presented here provides an experimental framework to inform these policy questions
and bolster both external and internal validity.
In this paper, we attempt to formalize the optimal design and analysis of RS designs.
Building on the previous multidisciplinary literature, we map the potential outcomes framework to a clustered error regression model, which allows us to gain analytical insights forthe optimal design of such experiments and derive ex-ante power calculations. The benefitof randomizing treatment saturations is the ability to generate direct experimental evidence
on the nature of spillover and threshold effects both for treated and non-treated individuals.
The cost of doing so is the precision of these estimates. Having laid out the assumptions
necessary to estimate both the mean and variance of spillover effects, we derive analyticalclosed-form expressions for the standard errors. The SEs for the pooled intention-to-treat
effect and spillover effect on the non-treated are directly related to the variation in treatment
saturation. A design trade-off emerges in that randomizing saturations allows the researcher
to identify novel estimands but comes at the cost of the precision of the estimates of morebasic estimands. This is an inherent feature of RS designs.

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32

A

Proofs from Section 3

A.1

Proof of Theorems 1 and 2

Preliminary Calculations

This section provides background material used in the proofsof Theorems 1 - 4. Consider the OLS estimate of
Yic = Xic′ β + εic ,(9)where Xic is a vector of treatment status covariates and εic is an error term with a blockdiagonal variance-covariance matrix. Given Xc′ = [X1c ... Xnc ] and ε′c = [ε1c ... εnc ], letE[εc ε′c |Xc ] = σ 2 In + τ 2 1n denote the within-cluster variance-covariance matrix, where 1n isthe (n × n) matrix of ones. Between clusters, E[εic εjd |X] = 0 for all c ̸= d. Then the exact
finite sample variance of β̂ is( C∑

Var(β̂|X) = A−1)
Xc′ E[εc ε′c |Xc ]Xc

c=1

( C
∑

= A−1

A−1
)

Xc′ (σ 2 In + τ 2 1n )Xc A−1

c=1
2

= σ A

−1

+ τ 2 A−1 BA−1 ,

(10)

where
A ≡
B ≡

C ∑
n
∑
c=1 i=1( C∑

Xic Xic′

Xc′ 1Xc

(11)

)
.

(12)

c=1

Proof of Theorem 1.

Consider an RS design with two interior saturations, p1 and p2 ,and a pure control. Let Tkic ≡ Tic ∗ 1{Pc = pk } and S1ic ≡ Sic ∗ 1{Pc = pk } for k = 1, 2. We
want to compute Var(β̂|X) for (9) when
Xic′ = [ 1 T1ic S1ic T2ic S2ic ].
By Lemma 1, the error distribution is block-diagonal. Let µk ≡ pk f (pk ), sk ≡ (1 − pk )f (pk ),ηk ≡ p2k f (pk ) and qk ≡ (1 − pk )2 f (pk ) = sk − µk + ηk . From Section A.1, Var(β̂|X) =33

σ 2 A−1 + τ 2 A−1 BA−1 , with




1
T1ic
S1ic
T2ic
S2ic
1 µ1 s1 µ2 s2








2
 T1ic
T1ic
S1ic T1ic T2ic T1ic S2ic T1ic
µ1 µ1 0 0 0 
C
n




∑∑



2
A=
 S1ic T1ic S1ic
S1ic
T2ic S1ic S2ic S1ic  = nC  s1 0 s1 0 0 
c=1 i=1 2 T2ic T1ic T2ic S1ic T2ic
 µ2 0 0 µ2 0 
T2ic
S2ic T2ic 




2
S2ic T1ic S2ic S1ic S2ic T2ic S2ic
S2ic
s2 0 0 0 s2
and


 

′ 





1
µ1
s1
µ2
s2
n
n



  ∑
 ∑



 
 n
 µ1

 i=1 T1ic   ni=1 T1ic  
η
µ
−
η
0
0
1
1
1
C








∑  ∑  ∑n2 nB =, i=1 S1ic  ∗  i=1 S1ic   = n C  s1 µ1 − η1
q1
0
0



 

c=1  ∑n  ∑n µ2
 i=1 T2ic   i=1 T2ic  00η2µ2 − η2 



  ∑
 ∑
n
n
s2
0
0
µ2 − η2q2
i=1 S2ic
i=1 S2ic∑ ∑n∑∑where the second equalities follow from ni=1 Tkic = npk , ni=1 Skic = n(1−pk ), C
c=1
i=1 Tkic =
∑ ∑n
∑C ∑n
2
npk × Cf (pk ) = nCµk , C
c=1
i=1 Skic = n(1 − pk ) × Cf (pk ) = nCsk ,c=1 (i=1 Tkic ) =
∑
∑n
∑n
2
2
n2 p2k ×Cf (pk ) = n2 Cηk , C
c=1 (i=1 Tkic ×
i=1 Skic ) = n pk (1−pk )×Cf (pk ) = n C(µk −ηk ),∑∑( ni=1 T1ic ) ( ni=1 S2ic ) = 0, and other analogous calculations. Taking the diagonal entries ofVar(β̂|X) yields
{
(
)
(
)}
1
1
1
1
1
2
2
Var(β̂1pj ) =
∗ nτ
+
+σ
+
nC
f (pj ) ψ
µj ψ
and
{
(
(
)
)}
1
1
1
1
1
2
2
Var(β̂2pj ) =
∗ nτ
+
+σ
+
nC
f (pj ) ψsj ψ
for each pj ∈ Π. Taking the square root yields the results for Theorem 1. It is straightforward
to extend the result to more than two interior saturations.
T
To compute the SEDT , note Var(δjk) = Var(β1pk − β1pj )/ (pk − pj )2 , Cov(β1pk , β1pj ) =34

(nτ 2 + σ 2 )/ψnC, andVar(β1pk − β1pj ) = Var(β1pj ) + Var(β1pk ) − 2 Cov(β1pk , β1pj )
{
(
)
(
)}
1
1
1
1
1
2
2
=
∗ nτ
+
+σ
+
,
nC
f (pj ) f (pk )µj µkSwhere Var(β1pk ) follows from Theorem 1. Similarly, Var(δjk) = Var(β2pk − β2pj )/ (pk − pj )2 ,where
Var(β2pk − β2pj ) = Var(β2pj ) + Var(β2pk ) − 2 Cov(β2pk , β2pj )
)
(
)}
{
(
1
1
1
1
1
2
2
∗ nτ
+
+σ
+
.
=
nC
f (pj ) f (pk )sj skTaking the square root yields the result for the slope effect.
Proof of Theorem 2.

Consider an RS design with at least one interior saturation and apure control. We want to compute Var(β̂|X) for (9), when
Xic′ = [ 1 Tic Sic ].
By Lemma 2, the error distribution is block-diagonal. From Section A.1, Var(β̂|X) =σ 2 A−1 + τ 2 A−1 BA−1 , with








1
Tic
Sic
1 µ µS
C ∑
n 



∑




2
A=
 Tic Tic Tic Sic  = nC  µ µ 0 
c=1 i=1
2
Sic Tic Sic SicµS 0 µS
and


2

∑n

∑n



n
n i=1 Ticn i=1 Sic
C 

∑
∑n
∑n
∑n
∑n


2
B =
 n i=1 Tic( i=1 Tic )( i=1 Tic ) ( i=1 Sic ) 


c=1
∑
∑
∑
∑
2
( ni=1 Sic )n ( ni=1 Sic ) ( ni=1 Tic ) ( ni=1 Sic )


1
µ
µS




2
2
2
2
2
= n C µ,η +µµ−µ −η
2222µS µ − µ − η µS − µ + η + µ∑n∑nwhere the second equalities follow from
i=1 Sic = n(1 − Pc ) if Pc >i=1 Tic = nPc ,
∑
∑C ∑n
∑C
∑C
C
2
2
2
2 2
2
0,
c=1 n Pc = n C(η + µ ),i=1 Tic ) =c=1 (p∈Π pCf (p) = nCµ,c=1 nPc = n
35

∑C

∑n

c=1 (

i=1 Tic ×∑ni=1 Sic ) =

∑C

2
2
2
2
c=1 n Pc (1 − Pc ) = n C(µ − η − µ ), and other analogous

calculations. Taking the diagonal entries of Var(β̂|X), and plugging in (7) to relate η 2 andηT2 yields the result for Theorem 2.
A.2

Proofs of Lemmas 1 and 2

Proof of Lemma 1.

Suppose the realized treatment vector is Tc = t, with Tic = t,

Tjc = t′ and p(t) = p. Then E[εic |Tc = t] = E[Yic (t) − Y (t, p)] = 0. The variance of theerror is E[ε2ic |Tc = t] = E[(Yic (t) − Y (t, p))2 ] = τ 2 + σ 2 . The covariance of the error between
individuals in the same cluster is E[εic εjc |Tc = t] = E[(Yic (t) − Y (t, p))(Yjc (t) − Y (t′ , p))] =τ 2 . Errors across clusters are not correlated since outcomes across clusters are not correlated.
Proof of Lemma 2.

The expected value of the error for treated individuals is

E[εic |Tic = 1] = E[Yic (1, T−i,c ) − Y (1)|Tic = 1]∑
P r(Pc = p|Tic = 1)Y (1, p) − Y (1)=p∈Π\{0}=1 ∑pf (p)Y (1, p) − Y (1)µp∈Π\{0}= 0,since from the perspective of a treated individual, P r(Pc = p|Tic = 1) = pf (p)/µ. Similarly,E[εic |Sic = 1] = 0 and E[εic |Tic = Sic = 0] = 0. The variance of the error for treatedindividuals is
E[ε2ic |Tic = 1] = E[(Yic (1, T−i,c ) − Y (1))2 |Tic = 1]
1 ∑
2 ∑
=
pf (p)(τ 2 + σ 2 + Y (1, p)2 ) −pf (p)Y (1, p)Y (1) + Y (1)2µµp∈Π\{0}p∈Π\{0}1 ∑= τ 2 + σ2 +pf (p)Y (1, p)2 − Y (1)2 .
µp∈Π\{0}Similarly, the variance of the error for within-cluster controls is
E[ε2ic |Sic = 1] = τ 2 + σ 2 +1µS∑p∈Π\{0}36(1 − p)f (p)Y (0, p)2 − Y (0)2 ,and the variance of the error for pure controls is E[ε2ic |Cic = 1] = τ 2 + σ 2 . The covariance ofthe error between treated individuals in the same cluster isE[εic εjc |Tic = Tjc = 1] = τ 2 +∑1
p2 f (p)(Y (1, p) − Y (1))2 .
(η 2 + µ2 )p∈Π\{0}Similarly,∑∑E[εic εjc |Sic = Sjc = 1] = τ +2p∈Π\{0} p(1 − p)f (p)(Y (1, p) − Y (1))(Y (0, p) − Y (0))∑

E[εic εjc |Tic = Sjc = 1] = τ 2 +p∈Π\{0} p(1 − p)f (p),22p∈Π\{0} (1 − p) f (p)(Y (0, p) − Y (0))∑,
2p∈Π\{0} (1 − p) f (p)and E[εic εjc |Cic = Cjc = 1] = τ 2 . Errors across clusters are not correlated since outcomes
across clusters are not correlated.
Proof of Corollary 3.

Recall Y (1) ≡ µ1∑p∈Π\{0} pf (p)Y (1, p). Suppose treatment effects∑
are constant on Π. Then Y (1, p) = Y (1) for all p. Therefore, ϕT ≡ µ1 p∈Π\{0} pf (p)Y (1, p)2 −∑Y (1)2 = µ1 p∈Π\{0} pf (p)Y (1)2 − Y (1)2 = 0. Similarly, ϕS = 0, ϕT T = 0, ϕSS = 0 and
ϕT S = 0. Therefore, the variance-covariance matrix reduces to a block-diagonal structurewith variance σ 2 + τ 2 and covariance τ 2 .
For the other direction, suppose the variance-covariance matrix is block-diagonal with∑variance σ 2 + τ 2 and covariance τ 2 . Then ϕT = 0. Therefore, µ1 p∈Π\{0} pf (p)Y (1, p)2 =Y (1)2 . But then there must be no variation in the population average potential outcome
across saturations for treated individuals. Similarly, ϕS = 0 and there must be no variationin the population average potential outcome across saturations for within-cluster controls.
Therefore, treatment effects are constant on Π.
A.3

Proofs of Optimal Design Results

The proof of Corollary 1 follows directly from Theorem 1.
Proof of Corollary 2.

Consider an RS design with at least two interior saturations.

Without loss of generality assume pk > pj and fix the share of clusters allocated to thesesaturations at f (pk ) + f (pj ) = F . Denote the size of saturation bin j by f (pj ) = f and bin
k by f (pk ) = F − f . Let pj = p and denote the distance between the two saturations by37∆ ≡ pk − pj . Then minimizing (4) is equivalent to solving:
( (
)
(
))
1
1
1
1
1
1
1
+
+ (1 − ρ)+++min min min 2 nρ
p ∆
∆
f
f
F −f
f p (F − f )(p + ∆) f (1 − p) (F − f )(1 − ∆ − p)
For each ∆, the minimum occurs at the p that solvesp(1 − p)f = (p + ∆)(1 − ∆ − p)(F − f ).

(13)

For any (p, ∆, f ) that satisfy (13) such that f ̸= F/2, there exists a (p′ , ∆′ , F/2) that1also satisfy (13) and strictly lower the objective function, since it lowers the term f1 + F −f

without affecting the term inside (1 − ρ).

Therefore, the optimal size of each saturation

bin is equal, f = F/2. Given ∆ and f = F/2, the optimal saturations are pj = (1 − ∆)/2and pk = p + ∆ = (1 + ∆)/2, which are symmetric about 1/2. The ∆ that minimizes (4) isequivalent to solving:
1
min 2
∆ ∆

(
(
nρ + (1 − ρ)

2
1 − ∆2)).

The optimal ∆∗ solves:nρ2∆2 − 1=.
2(1 − ρ)∆(1 − ∆2 )2√
If ρ = 0, then 2∆2 − 1 = 0, yielding ∆∗ = 2/2. Note that (2∆2 − 1)/(∆(1 − ∆2 )2 ) is√monotonically increasing for ∆ ∈ [0, 1), and strictly positive for ∆ > 2/2. The left hand√side is increasing in ρ, and strictly positive when ρ > 0. Therefore, ∆∗ > 2/2 for ρ > 0,and ∆∗ is increasing in ρ and n. If ρ > 0, then the left hand side converges to ∞ as n → ∞,which requires ∆∗ → 1. At the extreme, when ρ = 1, the optimal saturations are thefurthest apart saturations that maintain one treated individual and one with-cluster control
individual in each saturation, p∗j = 1/n and p∗k = (n − 1)/n.
Proof of Corollary 4.

Fixing µ and ψ, Var(β̂1 ) and Var(β̂2 ) are both minimized at

ηT2 = 0. This corresponds to a partial population experiment with a control group of size ψand a treatment saturation of p = µ/(1 − ψ).

38Proof of Corollary 5.

A partial population design with share of control clusters ψ andshare of treated individuals µ has SEs
√
{ (
)
(
)}
τ 2 + σ21
1
1∗ nρ+ (1 − ρ)+SE(β̂1 ) =nC(1 − ψ) ψ
µ ψ
√
{ (
)
(
)}
τ 2 + σ21
1
1SE(β̂2 ) =∗ nρ
+ (1 − ρ)+.
nC(1 − ψ) ψ
1−µ−ψ ψFixing ψ, the optimal treatment share solves
min SE(β̂1 ) + SE(β̂2 ),µwhich has solution µ = (1 − ψ)/2. This implies µS = µ, which corresponds to a partial
population experiment with treatment saturation p = 1/2. Plugging in µ = (1 − ψ)/2 yields
√
{ (
)
(
)}
1
1+ψ
τ 2 + σ2SE(β̂1 ) = SE(β̂2 ) =∗ nρ
+ (1 − ρ)nC
ψ(1 − ψ)ψ(1 − ψ)Thus, the optimal share of control clusters solves
(
)
(
)
1
1+ψ
min nρ
+ (1 − ρ).
(14)ψψ(1 − ψ)ψ(1 − ψ)√When ρ = 0, (14) is minimized at ψ ∗ = 2 − 1. When ρ = 1, (14) is minimized at ψ ∗ = 1/2.
When ρ ∈ (0, 1), the general FOC for (14) is(1 − ρ)(ψ 2 + 2ψ − 1) + nρ(2ψ − 1) = 0.
Using the quadratic formula with a = 1 − ρ, b = 2(1 − ρ + nρ) and c = −(1 − ρ + nρ) to solvefor ψ yields the optimal control group size. Given that (1 + ψ)/ψ(1 − ψ) and 1/ψ(1 − ψ) areboth convex and have unique minimums, any weighted sum of these functions is minimized
at a value ψ ∗ that lies between the minimum of each function. Therefore, when ρ ∈ (0, 1),√ψ ∗ ∈ ( 2 − 1, 1/2).

B

Additional Analysis

This section presents additional uses of an RS design. First, we compute the power of an RS
design to detect treatment effects when it is determined ex post that there are no spillover
effects. We show that the SE of an RS design is nested between the SE of a blocked design
39and the SE of clustered design. Second, we present a parametric linear model of spillovers
and illustrate how an RS design can consistently estimate the pure control outcome. Thisis a useful result for situations in which institutional constraints prohibit including a pure
control group.
B.1

Using Within-cluster Controls as Counterfactuals

Suppose there is no evidence of spillovers on untreated individuals – the estimate of SN T (p)is a precise zero for all p. Then the within-cluster controls are not subject to interference
from the treatment and they can be used as counterfactuals to increase the power of thetreatment effect estimates.
Assumption 3. Y (0, p) = Y (0, 0) for all p ∈ Π.28
Given Assumption 3, the researcher can pool within-cluster and pure controls, and estimate a simpler model to measure treatment effects,
Yic = β0 + β1 Tic + εic .

(15)This regression returns ITˆT = β̂1 .29 Power is significantly improved by the larger counterfactual, particularly when τ is high. Theorem 3 characterizes the pooled SE when thewithin-cluster controls are included in the counterfactual.
Theorem 3 (SE with Within-Cluster Controls). Let (Π, f ) be a RS design. Assume Assumptions 1, 2 and 3. The SE of IT T is:
√
( (
)
(
))
τ 2 + σ2
η2
1
SEIT T =nρ+ (1 − ρ).
nCµ2 (1 − µ)2µ(1 − µ)Theorem 3 nests the SE of this model between the more familiar expressions for the
SE of the blocked and clustered designs. An immediate corollary is that the power of thepooled treatment effect in any RS design lies between the power of the treatment effect in
the blocked and clustered designs.

ˆ T (p).
This assumption is testable using any RS design that yields a consistent estimate of SN
Saturation weights are necessary if there are spillover effects on treated individuals, ST (p) ̸= 0 for somep ∈ Π.
28

29

40

RS

Corollary 6. Let SEIT T be the standard error for an RS design with share of treated individuals µ. Then

where SEB
IT T√

2 +nτ 21
∗ σµ(1−µ)
nC

√
=

RS
C
SEB
IT T < SEIT T < SEIT T ,1
σ2∗ µ(1−µ)nC

is the SE in a blocked design with saturation µ and SEC
IT T =

is the SE in a clustered design with share of treatment clusters µ.

This follows directly from Theorem 3, noting that the blocked design corresponds to η 2 = 0
and the clustered design corresponds to η 2 = µ(1 − µ).
Corollary 6 provides context for a well-known result. Fixing the treatment share µ, theSE is decreasing in the variance of the treatment saturation η 2 , and minimized when thisvariation is zero, which corresponds to the blocked design. Second, fixing η 2 , the SE is
minimized when µ(1 − µ) is maximized, which occurs at µ = 1/2. As is well known, in theabsence of spillovers, the optimal design is a blocked study with equal size treatment andcontrol groups.
B.2

Inference in a Linear Model

It is also possible to measure slope effects by imposing a functional form on the shape of thespillover effects. For example, we could use an affine model to estimate the first order slope
effect.
Assumption 4 (Linearity). Y (t, p) is affine in p for t ∈ {0, 1}.
Given Assumption 4, it is natural to estimate:
Yic = α0 + α1 Tic + δ1 Pc + δ2 Tic Pc + εic(16)ˆ T = α̂1 .
This regression identifies the TUT as the intercept of the treatment effect, T U
The coefficients δ1 and δ2 are slope terms estimating how spillover effects change with theˆ /dp = δ̂1 + δ̂2 and dSN
ˆ T /dp = δ̂1 . A test for dST /dp = dSN T /dp is given
saturation, dST
by the hypothesis test δ2 = 0.3030

In order to test the linearity assumption, one could estimate
Yic = α0 + α1 Tic + α2 Sic + δ1 Pc + δ2 Tic Pc + εic .

(17)

The intercept δ2 estimates the spillover effect on untreated individuals at saturation zero. This should be

41

Theorem 4 characterizes the standard errors of the slope estimands in an affine model,
which is proportional to SE(δˆ1 + δˆ2 ) for treated individuals and SE(δˆ1 ) for untreated individuals.
Theorem 4 (Affine Slope SE). Assume Assumptions 1 and 2 and let (Π, f ) be a randomized
saturation design with κ ≥ 2 interior saturations. The SE for the slope effect of treated√individuals is:
SEDT =
where mx ≡ C1∑C

x
c=1 Pc =∑xp∈Π p f (p) and

(
h1 ≡

1
∗ {nτ 2 h1 + σ 2 h2 }nC

(η 2 + µ2 )2 − 2µ(η 2 + µ2 )m3 + µ2 m4((η 2 + µ2 )2 − µm3 )2

and

(
h2 ≡

η 2 + µ2(η 2 + µ2 )2 − µm3)).

An analogous expression characterizes the slope effect of untreated individuals, denoted SEDN T .
B.3

Inference Without a Pure Control

The RS design opens up unique empirical possibilities in studies where there is no pure control
group. This is particularly important for settings in which a pure control is not feasible due
to regulatory requirements or other exogenous restrictions.31 Without a pure control group,
a study’s counterfactual is subject to within-cluster spillovers. An RS design has the distinct
advantage of allowing a researcher to test for the presence of spillover effects and estimate
the unperturbed counterfactual. If the spillover effect is continuous at zero, the researcher
can use the variation in treatment saturation to project what would happen to untreatedindividuals as the saturation approaches zero.32 With this unperturbed counterfactual in
hand, it is possible to correctly estimate the ITˆT .
zero, as SN T (0) = 0 by definition, so α2 = 0 serves as a hypothesis test for the linearity of the spillover
relationship.
31
For example, in McIntosh et al. (2013), a Mexican government rule required that each participatingcluster (municipality) be guaranteed at least one treated sub-unit (neighborhood).
32
Although continuity is a reasonable assumption, it is not universally applicable. Consider signalling ina ground-hog colony. Individuals are ‘treated’ by being alerted to the presence of a nearby predator, and thepossible individual-level outcomes are ‘aware’ and ‘not aware’. The animal immediately signals danger tothe rest of the colony, and control outcomes will be universally ‘aware’ for any positive treatment saturation,but ‘unaware’ when the saturation is exactly zero.

42

Assumption 4 provides a simple way to estimate the pure control by assuming thatthe outcome variable is linear with respect to treatment saturation. Note that Theorem 4
requires at least two interior saturations, but does not require a pure control group.
Theorem 5 (Consistency with No Control). Assume 1, 2 and 4, and let (Π, f ) be a randomized saturation design with κ ≥ 2 interior saturations. Then the OLS estimates fromˆ T (p) = δ̂1 p.
(16) are consistent estimates of ITˆT (p) = α̂1 + (δ̂1 + δ̂2 )p and SN
Proof. Given Assumption 4, we can identify the slope of the ITT and SNT. The rest of the□proof follows easily from the Law of Large Numbers.

The hypothesis test δ1 = 0 determines whether there is a spillover effect on untreated individuals. If spillovers are present, then the counterfactual needs to be corrected. The coefficient
α̂0 is an estimate of the desired ‘pure’ control outcome, Y (0, 0).
B.4

Proofs for Theorems in Appendix B

Proof of Theorem 3.

We compute Var(β̂|X) for (9) whenx′ic = [ 1 Tic ].

Recall from Section A.1 that Var(β̂|X) = σ 2 A−1 + τ 2 A−1 BA−1 . Therefore,




C ∑
n
∑
1 Tic
1 µ

 = nC A=
2
Tic Ticµ µc=1 i=1
and
B =

C
∑
c=1



n

n
∑n

2

i=1 Tic

∑n







1
µ
n i=1 Tic,
 = n2 C ∑n222µ η +µ( i=1 Tic )

∑C ∑n
∑
∑
2
nP
=
nCµ,
and
where the second equalities follow from ni=1 Tic = nPc , C
ci=1 Tic ) =
c=1 (
c=1
∑C
2
2
2
2 2
c=1 n Pc = n C(η + µ ). This can be used to compute
[(
)
(
) ]
1
η2
1
2
Var(β̂1 ) =
∗
nτ +
σ2 .
2
2
nC
µ (1 − µ)µ(1 − µ)Fixing µ, this expression is minimized at η 2 = 0.

43

Proof of Theorem 4.

We want to compute Var(β̂|X) for (9) whenx′ic = [ 1 Tic Tic Pc Sic Sic Pc ].

Recall from Section A.1 that Var(β̂|X) = σ 2 A−1 + τ 2 A−1 BA−1 . Therefore


1
Tic
Tic PcSic
Sic Pc




2
2
 Tic
T
T
P
T
S
T
S
P
ic ic
ic ic c 
ic
ic c
C
n


∑∑

2
2
2
2
A =
 Tic Pc Tic Pc
Tic PcTic Sic Pc Tic Sic Pc 
c=1 i=1  Sic
Tic Sic Tic Sic Pc
Sic2
Sic2 Pc 


2
2
2 2
Sic Pc Tic Sic Pc Tic Sic Pc
Sic PcSic Pc1µη 2 + µ2 1 − µ − ψµ − η 2 + µ2




2
2


µ
µ
η +µ
0
0




2
2
2
2
= nC  η + µ

η +µ
m3
0
0




 1−µ−ψ001−µ−ψ
µ − η 2 + µ2 


2
2
2
2
2
2
µ−η +µ00µ − η + µ η + µ − m3


 

′ 

n
n

 

∑
∑

 

n
n




T
T
i=1 ic  i=1 ic  C∑  ∑  ∑B = ni=1 Tic Pc  ∗  ni=1 Tic Pc  

 

c=1  ∑n  ∑nSic  Sic  
i=1
i=1
 ∑
  ∑

n
n
i=1 Sic Pc
i=1 Sic Pc


1
µ
m2
1−µ−ψ
µ − m2






µ
m2
m3
µ − m2m2 − m3
2 = n C

m2
m3
m4
m2 − m3
m3 − m4 1 − µ − ψ µ − m2 m2 − m3 1 − 2µ + m2 − ψ µ − 2m2 + m3 
µ − m2 m2 − m3 m3 − m4 µ − 2m2 + m3 m2 − 2m3 + m4
where mx ≡ C1∑C

x
c=1 Pc =∑xp∈Π p f (p). Taking the diagonal entries of Var(β̂|X) yields theresult, SEDT = SE(δˆ3 ) and SEDN T = SE(δˆ4 ).

44