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Identifying Causal Effects in Experiments with Social Interactions and Non-compliance

This paper shows how to use a randomized saturation experimental design to identify and estimate causal effects in the presence of social interactions--one person's treatment may affect another's outcome--and one-sided non-compliance--subjects can only be offered treatment, not compelled to take it up. Two distinct causal effects are of interest in this setting: direct effects quantify how a person's own treatment changes her outcome, while indirect effects quantify how her peers' treatments change her outcome. We consider the case in which social interactions occur only within known groups, and take-up decisions do not depend on peers' offers. In this setting we point identify local average treatment effects, both direct and indirect, in a flexible random coefficients model that allows for both heterogenous treatment effects and endogeneous selection into treatment. We go on to propose a feasible estimator that is consistent and asymptotically normal as the number and size of groups increases.


Introduction
Random saturation experiments provide a powerful tool for estimating causal effects in the presence of social interactions-also known as spillovers or interference-by generating exogenous variation in both individuals' own treatment offers and the fraction of their peers who are offered treatment (Hudgens and Halloran, 2008). These two sources of variation allow researchers to study both direct causal effects-the effect of Alice's treatment on her own outcome-and indirect causal effects-the effect of Bob's treatment on Alice's outcome. A complete understanding of both direct and indirect effects is crucial for program evaluation in settings with social interactions. When considering a national job placement program, for example, policymakers may worry that the indirect effects of the program could completely offset the direct effects: in a slack labor market, job placement could merely change who is employed without affecting the overall employment rate (Crépon et al., 2013).
In this paper we provide methods that use data from a randomized saturation design to identify and estimate direct and indirect causal effects in the presence of social interactions and one-sided non-compliance. In real-world experiments non-compliance is the norm rather than the exception. In their study of the French labor market, Crépon et al. (2013) found that only 35% of workers offered job placement services took them up. Despite pervasive non-compliance in practice, most of the existing literature on randomized saturation designs either assumes perfect compliance-all subjects adhere to their experimentallyassigned treatment allocation-or identifies only intent-to-treat-effects-the effect of being offered treatment. In contrast, we use the experimental design as a source of instrumental variables to estimate local average treatment effects (LATE) when subjects endogenously select into treatment on the basis of their experimental offers. In a world of homogeneous treatment effects, a simple instrumental variables (IV) regression using individual treatment offers and group saturations as instruments would identify both direct and indirect effects. In most if not all real-world settings, however, treatment effects vary across individuals. In the presence of heterogeneity, this "naïve" IV approach will not in general recover interpretable causal effects. To allow for realistic patterns of heterogeneity in a tractable framework, we study a flexible random coefficients model in which causal effects may depend on an individual's treatment take-up as well as that of her peers.
Our approach relies on four key assumptions. First is partial interference: we assume that each subject belongs to a single, known group and that social interactions occur only within groups. This is reasonable in many experimental settings where, for example, groups correspond to villages, and social interactions across them are negligible. Second is anonymous interactions: we assume that individuals' potential outcome functions depend on their peers' treatment take-up only through the average take-up in their group. Under this assumption only the number of treated neighbors matters, not their identities (Manski, 2013). In the absence of detailed network data, the assumption of anonymous interactions is a natural starting point and is likely to be reasonable in settings such as the labor market example described above. Third is one-sided non-compliance: we assume that the only individuals who can take up treatment are those to whom treatment was offered via the experimental design. One-sided non-compliance is relatively common in practice, for example when an "encouragement design" is used to introduce a new program, product or technology that is otherwise unavailable (e.g. Crépon et al., 2013;Miguel and Kremer, 2004). We refer to our fourth key assumption as individualized offer response, or IOR for short. IOR requires that each subject's treatment take-up decision depends only on her own treatment offer, and not on the offers made to her peers. While IOR is a strong assumption, it is testable and a priori reasonable in many contexts. In Crépon et al. (2013), for example, local labor markets are large and potential participants in the job placement program are unlikely to know each other in advance. As such, they are unlikely to influence each other's treatment take-up decisions, even if they may impose employment externalities on one another. IOR is also reasonable in online settings where other subjects' take-up decisions are unobserved (Anderson et al., 2014;Bond et al., 2012;Eckles et al., 2016) or confidential (Yi et al., 2015).
Because it rules out any form of strategic take-up, IOR allows us to divide the population into never-takers and compliers, two of the traditional LATE strata. 1 Under the randomized saturation design and a standard exclusion restriction, we show how to construct valid and relevant instruments that identify the average causal effects of interest. The key to our approach is a result showing that conditioning on group size n and the share of compliers c in a group breaks any dependence between peers' average take-up and an individual's random coefficients. Under the randomized saturation design, the share of Alice's neighbors who are offered treatment is exogenous. Under IOR, their average take-up depends only on how many of them are compliers and whether they are offered treatment. Thus, conditional on n andc, any residual variation in the take-up of Alice's neighbors comes solely from the experimental design. Although group size is observed, the share of compliers in a given group is not. In a large group, however, the rate of take-up among those offered treatment, call it c, closely approximatesc. Using this insight, we provide feasible estimators of direct and indirect causal effects that are consistent and asymptotically normal in the limit as group size grows at an appropriate rate relative to the number of groups. After constructing the appropriate instruments, our estimators can be implemented as simple IV regressions without the need for non-parametric estimation. This paper relates most closely to recent work by Kang and Imbens (2016) and Imai et al. (2018), who also study randomized saturation experiments with social interactions under non-compliance. Imai et al. (2018) identify a "complier average direct effect" (CADE), in essence a Wald estimand calculated for all groups with the same share of offers (saturation). While it is identified under a weaker condition than IOR, the CADE is in fact a hybrid of direct and indirect effects unless one is willing to impose IOR. Under IOR, the CADE quantifies the effect of an individual's own treatment take-up, given that her group has been assigned a particular saturation. In contrast, the direct effects that we recover below quantify the effect of an individual's own treatment take-up given that a certain share of her neighbors have taken up treatment. Kang and Imbens (2016) identify effects similar to those of Imai et al. (2018) using a variant of our IOR assumption that they call "personalized encouragement." Both Kang and Imbens (2016) and Imai et al. (2018) identify well-defined effects while placing limited structure on the potential outcome functions. The cost of this generality is that the effects they recover have a "reduced form" flavor, and are only defined relative to the specific saturations used in the experiment. While our random coefficients model is slightly more restrictive over the potential outcome functions, it allows us to recover "fully structural" causal effects that are not specific to the design of the experiment.
Our paper also relates to the applied literature that estimates spillover effects in various settings. This includes "partial population" studies in which a subset of subjects in the treatment group are left untreated and their outcomes are compared to those of subjects in a control group (Angelucci and De Giorgi, 2009;Barrera-Osorio et al., 2011;Bobonis and Finan, 2009;Duflo and Saez, 2003;Haushofer and Shapiro, 2016). It also includes cluster-randomized trials where groups are defined by a spatial radius within which social interactions may arise (Bobba and Gignoux, 2014;Miguel and Kremer, 2004) and more recent papers that use a randomized saturation design (Banerjee et al., 2012;Bursztyn et al., 2019;Giné and Mansuri, 2018;Sinclair et al., 2012). In general, this literature estimates intent-to-treat (ITT) effects. Two notable exceptions are Crépon et al. (2013) and Akram et al. (2018) who estimate effects that are similar in spirit to the CADE of Imai et al. (2018).
Our identification approach also relates to a large literature on random coefficients models, the closest being Wooldridge (2004) and Masten and Torgovitsky (2016), as well as methods that identify structural effects using control functions (Altonji and Matzkin, 2005;Imbens and Newey, 2009). The remainder of the paper is organized as follows. Section 2 details our notation and assumptions, while section 3 presents our identification results. Section 4 provides consistent and asymptotically normal estimators of the effects identified in section 3, and Section section 5 concludes. Proofs appear in the appendix.

Notation and Assumptions
We observe N individuals divided between G groups. We assume throughout the paper that each group has at least two members so there is scope for social interactions. Let g = 1, . . . , G index groups and i = 1, . . . , N g index individuals within a given group g. Using this notation, For each individual (i, g) we observe a binary treatment offer Z ig , an indicator of treatment take-up D ig , and an outcome Y ig . For each group g we observe a saturation S g ∈ [0, 1] that determines the fraction of individuals offered treatment in that group. A bold letter indicates a vector and a g-subscript shows that this vector is restricted to members of a particular group. For example Z is the N-vector of all treatment offers Z ig while Z g is the N g -vector obtained by restricting Z to group g. Define D and D g analogously and let S denote the G-vector of all S g . At various points in our discussion we will need to refer to the average value of a variable for everyone in a group besides person (i, g). As shorthand, we refer to these other individuals as person (i, g)'s neighbors. To indicate such an average, we use a bar along with an (i, g) subscript. For instance,D ig denotes the treatment take-up rate in group g excluding (i, g), whileZ ig is the analogous treatment offer rate: Note that, under this definition,D ig andZ ig vary across individuals in the same group depending on their values of D ig or Z ig . For example in a group of eleven people, of whom five take up treatment,D ig = 0.5 if D ig = 0 and 0.4 if D ig = 1. We now introduce our basic assumptions, beginning with the experimental design.
Assumption 1 (Assignment of Saturations). Let S = {s 1 , s 2 , . . . , s J } where s j ∈ [0, 1] for all j. Saturations are assigned to groups completely at random from S such that m j groups are assigned to saturation s j with probability one, where J j=1 m j = G. In other words, Assumption 1 details the first stage of the randomized saturation design. In this stage, each group g is assigned a saturation S g drawn completely at random from a set S. In the example from Figure 1, fifty groups (balls) are divided equally between five saturations (urns), namely S = {0, 0.25, 0.5, 0.75, 1}. The saturation drawn in this first stage determines the fraction of individuals in the group that will be offered treatment in the second stage. Figure 1, for example, depicts a group of eight individuals that has been assigned to the 0% 25% 50% 75% 100% 0 0 1 0 0 0 0 1 Figure 1: Randomized Saturation Design. In the first stage groups (balls) are randomly assigned to saturations (urns). In the second stage, individuals within a group are randomly assigned treatment offers at the saturation selected in the first stage. The figure zooms in on a group of size eight that has been assigned to a 25% saturation: two individuals are offered treatment.
25% saturation: two are offered treatment and six are not. For simplicity we assume that treatment offers in the second stage follow a Bernoulli design, in which S g determines the probability of treatment rather than the number of treatment offers. 2 Assumption 2 (Bernoulli Offers).
The randomized saturation design creates exogenous variation at the individual and group levels. Within a group some individuals are offered while others are not. Between groups, some have a large number of individuals offered treatment-a high saturation-while others do not. Many randomized saturation experiments, like the illustration in Figure 1, feature a 0% saturation or even a 100% saturation. We refer to 0% and 100% saturations collectively as corner saturations to distinguish them from all other saturations, which we call interior. There is no variation in treatment offers between individuals in a group assigned a corner saturation. For this reason, as we discuss in section 3 below, the number of interior saturations in the design will determine the flexibility with which we can model potential outcome functions. Assumptions 1-2 concern the design of the experiment. Our remaining assumptions, in contrast, concern the potential outcome and treatment functions. Without imposing any restrictions, an individual's potential outcome function Y ig (·) could in principle depend on the treatment take-up of all individuals in the sample. We denote this unrestricted potential outcome function by Y ig (D). Assumption 3 restricts Y ig (·) to depend only on D ig andD ig via a random coefficients model.
Assumption 3 (Random Coefficients Model). Let f(·) be a K-vector of known functions where θ ig and ψ ig are K-dimensional random vectors that may be dependent on (D ig ,D ig ).
The first equality in Assumption 3 is the so-called partial interference assumption, used widely in the literature on spillover effects. This assumption states that there are no social interactions between individuals in different groups: only the treatment take-up of individuals in group g affects the potential outcome of person (i, g). The second equality in Assumption 3 states that person (i, g)'s potential outcome is only affected by the treatment take-up of the others in her group through the aggregateD ig . 3 This is related to the anonymous interactions assumption from the network literature as it implies that only the number of (i, g)'s neighbors who take up treatment matters for her outcome; the identities of the neighbors are irrelevant (Manski, 2013). The third equality in Assumption 3 posits a finite basis function expansion for the potential outcome functions Y ig (0,D ig ) and Y ig (1,D ig ), namely or, written more compactly in matrix form, where the coefficient vectors θ ig and ψ ig , and hence B ig , are allowed to vary arbitrarily 3 Recall thatD ig is defined to exclude person (i, g).
across groups and individuals. If, for example, person (i, g) has some prior knowledge of her potential outcome function Y ig (·, ·), her take-up decision may depend on θ ig and ψ ig . More generally, the same unobserved characteristics that determine a person's decision to take up treatment could affect her potential outcomes. To account for these possibilities, we allow arbitrary statistical dependence between (D ig ,D ig ) and B ig .
Ideally, our goal would be to identify the average direct and indirect causal effects of the binary treatment D ig . Under Assumption 3, we define these as follows, building on the definitions of Hudgens and Halloran (2008). The direct treatment effect, DE, gives the average effect of exogenously changing an individual's own treatment D ig from 0 to 1 while holding the share of her treated neighborsD ig fixed atd, namely where the expectations are taken over all individuals in the population from which our experimental subjects were drawn. Recall thatD ig excludes person (i, g), ensuring that DE(d) is well-defined. An indirect treatment effect, in contrast, gives the average effect of exogenously increasing a person's share of treated neighborsD ig fromd tod + ∆ while holding her own treatment D ig fixed at d, in other words where ∆ is a positive increment. There are two indirect treatment effect functions, IE 0 and IE 1 , corresponding to the two possible values at which we could hold D ig fixed: a spillover on the untreated, and a spillover on the treated. Because the direct and indirect causal effects are fully determined by [B ig ] under Assumption 3, this is our object of interest below. For example, if f(x) ′ = [1 x] we obtain a linear model of the form In this case the direct effect is Figure 2 presents a hypothetical example of (5) in a setting with employment displacement effects. Suppose that Y ig is Alice's probability of long-term employment. Both Y ig (1,d) and Y ig (0,d) have a negative slope. This means that Alice's probability of long-term em- ployment decreases if more of her neighbors obtain job placement services. But since δ ig is positive, the spillover is more harmful if Alice is untreated. Alice's direct effect of treatment Y ig (1,d) − Y ig (0,d) is positive for alld in this example and increases asd does: job placement services are more valuable to Alice when more of her neighbors obtain them. By averaging these effects for everyone in the population, we obtain IE 0 , IE 1 , and DE.
Under perfect compliance D ig would simply equal Z ig , making both D ig andD ig exogenous. In this case a sample analogue of [Y ig (d,d)] could be used to recover all of the treatment effects discussed above, at least at values ofd that arise in the experimental design. Unfortunately non-compliance is pervasive in real-world experiments, greatly complicating the identification of causal effects. In a large-scale experiment carried out in France, for example, only 35% of unemployed workers offered job placement services took them up (Crépon et al., 2013). Those who did take up treatment likely differ in myriad ways from those who did not: they may, for example, be more conscientious. One way to to avoid this problem of self-selection is to carry out an intent-to-treat (ITT) analysis, conditioning on Z ig and S g rather than D ig andD ig . But with take-up rates as low as 35%, ITT estimates could be very far from the causal effects of interest. In this paper we adopt a different approach. Following the tradition in the local average treatment effect (LATE) literature, we provide conditions under which direct and indirect causal effects-rather than ITT effectscan be identified for well-defined sub-populations of individuals. We focus on the case of one-sided noncompliance, in which only those offered treatment can take it up. One-sided non-compliance is fairly common in practice (e.g. Crépon et al., 2013) and simplifies the analysis considerably. 4 Assumption 4 (One-sided Non-compliance). If Z ig = 0 then D ig = 0.
To account for endogenous treatment take-up, we define potential treatment functions D ig (·). In principle these could depend on the treatment offers of every individual, Z in the experiment. The following assumption restricts D ig (·) to permit identification of the direct and indirect causal effects described above.
The first equality of Assumption 5 is a partial interference assumption: it requires that there are no social interactions in take-up between individuals in different groups. The second equality of Assumption 5 states that person (i, g)'s take-up decision depends on the treatment offers of others in her group only through the fractionZ ig of treatment offers made to the others in her group. 5 Unfortunately these first two equalities are not in general sufficient to point identify direct and indirect causal effects. The third equality, which we call individualistic offer response or IOR for short, imposes the further restriction that each person's take-up decision depends only on her own treatment offer. IOR states that there are no social interactions in take-up. 6 This is a strong assumption, but one that has also appeared in the existing literature. Kang and Imbens (2016), for example, employ a variant of IOR that they call "personalized encouragement." And while Imai et al. (2018) derive their so-called "complier average direct effect (CADE)" under a weaker condition than IOR, the CADE is in fact a hybrid of direct and indirect effects unless one is willing to assume that there are no social interactions in take-up. Fortunately, IOR is testable: it implies, for example, that [D ig |Z ig = 1, S g = s] does not vary with s. If the observed average take-up rate among individuals who are offered treatment varies with saturation, this indicates a violation of IOR.
Under IOR and one-sided non-compliance (Assumptions 4 and 5), we can divide individuals into never-takers and compliers, two of the principal strata from the LATE literature. Never-takers are defined as those for whom D ig (0) = D ig (1) = 0, while compliers are those for whom D ig (z) = z for all z. 7 Defining C ig to be the indicator that person (i, g) is a complier, Assumptions 4-5 imply that By analogy toZ ig andD ig , we defineC ig to be the share of compliers among person (i, g)'s neighbors in group g, namelyC Note thatC ig varies across individuals in the same group, depending on their values of C ig .
Finally, let C g denote the vector of C ig for all individuals in group g.
Our final assumption is an exclusion restriction for the treatment offers Z g and saturation S g . To state it we require two additional pieces of notation. First, let B g denote the vector that stacks B ig for all individuals in group g. Second, following Dawid (1979) indicates that X is conditionally independent of Y given Z. Using this notation, the exclusion restriction is as follows.
Intuitively, Assumption 6 states that (C g , B g , N g ) are "predetermined" with respect to the treatment offers and saturations. In a traditional LATE setting, the counterparts of Assumption 6 are the "unconfounded type" assumption and the independence of potential outcomes and treatment offers. Assumption 6 could be violated in a number of ways. If, for example, individuals chose their group membership based on knowledge of their group's saturation, N g would not be independent of S g . Similarly, if some individuals decided to comply with their treatment offers only because their group was assigned a high saturation, C g would not be independent of S g . This latter possibility illustrates that Assumption 6 partially embeds IOR by ruling out "selection into compliance." More prosaically, Assumption 6 would be violated if either S g or Z ig had a direct effect on the random coefficients B g . Notice that part (ii) of Assumption 6 conditions on (S g , N g ). This is because the second stage of the randomized saturation experiment assigns Z g conditional on this information: see Assumption 2.

Identification
Under Assumption 3, the functional form of the random coefficients model is known. So why not simply use (Z ig , S g ) as instrumental variables for D ig and f(D ig )? If the first-stage relationship between instruments and endogenous regressors is homogeneous, two-stage least squares identifies the average effects in a random coefficient model, i.e. [θ ig ] and [ψ ig −θ ig ] under (2) (Heckman and Vytlacil, 1998;Wooldridge, 1997Wooldridge, , 2003Wooldridge, , 2016. In our case, however, this result does not apply: the following lemma shows that the first stage is heterogeneous because the conditional distribution ofD ig given S g varies with (C ig , N g ).
Lemma 1. Letc be a value in [0, 1] such that (n − 1)c is a non-negative integer. Under Assumptions 1-2 and 4-6 and conditional on (N g = n, S g = s, C g = c,C ig =c, Z ig = z), Intuitively, the problem presented by the Lemma 1 is as follows. Although S g is randomly assigned, the variation that it induces inD ig is mediated by the share of compliersC ig . Accordingly ifC ig -a source of first-stage heterogeneity-is correlated with the random coefficients in the second stage, the IV estimator will not identify the effects of interest. To make this problem more concrete, consider the linear potential outcomes model from (5) and let ϑ IV be the IV estimand using instruments (1, Z ig , S g , Z ig S g ). In this example ϑ IV takes a particularly simple form, as shown in the following lemma.
assuming that [Z ig X ′ ig ] is invertible. Then, under (5) and Assumptions 1-2 and 4-6, As we see from Lemma 2, IV identifies the population average of α ig , along with the population average of β ig for the subset of individuals who select into treatment. Neither of these, however, is itself a causal effect. In general, IV recovers neither direct nor indirect causal effects for any well-defined group of individuals. Specializing (4) to the linear model from (5) gives IE 0 (d, ∆) = [γ ig ]∆. In other words, [γ ig ] is an average spillover. Lemma 2 shows that IV fails to identify this quantity unless the individual-specific spillovers γ ig are uncorrelated with the share of compliersC ig . This condition could easily fail in practice. In the labor market example from the introduction, cities with a particularly depressed labor market might be expected to contain a large share of compliers. If negative spillovers are more intense in such cities, IV will not recover the average indirect effect. A similar problem hampers the interpretation of δ IV . Under (5) the average direct effect for compliers, as a function ofd, is given by [β ig |C ig = 1] + [δ ig |C ig = 1]d. While IV identifies the intercept of this function, it only identifies the slope if δ ig is uncorrelated withC ig for compliers.
As this example illustrates, identifying direct and indirect causal effects requires us to correct for possible dependence between individual-specific coefficients and group-level takeup that arises from the first-stage relationship in Lemma 1. The key to our approach, as shown in the following theorem, is to condition onC ig and N g .
Theorem 1 implies that conditioning on (C ig , N g ) is sufficient to break any dependence between f(D ig ) and (B ig , C ig ) that may be present. The intuition for this result is as follows. Conditional onC ig and N g , we know precisely how many of (i, g)'s neighbors are compliers.
Given this information, IOR implies that all remaining variation inD ig is arises solely from experimental variation in the saturation S g assigned to different groups, and the share of compliers offered treatment across groups assigned the same saturation. So long as Z ig and S g do not affect (B ig , C g ), Assumption 6, it follows that (Z ig ,D ig , S g ) are exogenous given (C ig , N g ), even when individuals decide whether or not to take up treatment based on knowledge of their potential outcome functions.
Before stating our identification results, we require some additional notation and one further assumption. Define the vector W ig and matrix-valued functions Q, Q 0 , Q 1 as follows: We use Q, Q 0 , Q 1 below to construct instrumental variables that are not subject to the shortcomings of Z ig from Lemma 2 discussed above. The final ingredient that we need to construct these alternative instruments is a rank condition.
Part (i) of Assumption 7 asserts that there is at least some degree of non-compliance with the experimental treatment offers, (C ig ) < 1, and that the population contains at least some compliers, (C ig ) > 0. Part (ii) requires that the matrix-valued function Q defined in (8) is full rank when evaluated at any share of compliersc and group size n that occur in the population. Assumption 7 does not explicitly restrict Q 0 or Q 1 . By the linearity of conditional expectation, however, so Assumption 7(ii) could equivalently be stated in terms of Q 0 and Q 1 .
We discuss low-level conditions for the invertibility of (Q 0 , Q 1 ), and hence Q, below. Having assumed the necessary rank condition, we can now state our main identification results. The following theorem shows how Q 0 (C ig , N g ) and Q 1 (C ig , N g ) can be used to construct instrumental variables that identify average values of the random coefficients for well-defined groups of individuals.

Theorem 2. Define the instrument vectors
where Q 0 , Q 1 , Q, and W ig are as given in (8)-(10). Then, under Assumptions 3-5 and 7 and assuming that ( The first part of Theorem 2 identifies the average effects that the naïve IV approach from Lemma 2 in general fails to. Rather than using the randomly assigned saturation S g as a source of instruments for f(D ig ) we transform this vector of endogenous regressors into a set of exogenous instruments using Q 0 (C ig , N g ) −1 and Q 1 (C ig , N g ) −1 . Parts (ii) and (iii) use a similar approach to obtain moment equations for the average value of ψ ig for compliers and θ ig for never-takers. Given part (i), part (iv) is technically redundant, but it is convenient to have an expression for (θ ig ) in isolation. To understand the intuition behind the instruments from Theorem 2, consider the linear potential outcomes example from (5) above. Here we have f(x) = (1, x) ′ and thus It follows after a few steps of algebra that WhileD ig is endogenous, we see that the scaled difference betweenD ig and its conditional expectation is a valid instrument under the linear potential outcomes model. Intuitively, this transformation adjusts for the first-stage heterogeneity discussed at the beginning of this section: after controlling for differences in (C ig , N g ), the remaining variation inD ig arises only from the experimentally-assigned saturations. Thus, rather than using S g as an instrument directly, we use it indirectly to generate variation inD ig given (C ig , N g ). As discussed below, this is crucial for part (ii) of Assumption 7. Notice that Theorem 2 does not explicitly invoke the randomized saturation design, Assumptions 1-2, or the exclusion restriction, Assumption 6. Using this result for identification, however, requires two conditions. First we need to satisfy (Z ig ,D ig ) |= (B ig , C ig )|(C ig , N g ). As shown in Theorem 1 above, the randomized saturation design and exclusion restriction are sufficient for this condition to hold under one-sided non-compliance and IOR, Assumptions 4 and 5. Second, we need to show that the functions Q 0 , Q 1 are identified in order to construct the instruments from Theorem 2. Fortunately, these functions are in fact known under the randomized saturation design and exclusion restriction. 8 In particular, they depend only on the distribution ofD ig |(Z ig ,C ig , N g ), which can be calculated from Lemma 1, and the distribution of Z ig |(C ig , N g ), which coincides with its unconditional distribution by Lemma A.2. As such, we can always calculate Q 0 (C ig , N g ) and Q 1 (C ig , N g ) by simulating the experimental design. Depending on the choice of f, analytical expressions for Q 0 , Q 1 may be available, as shown below for the linear potential outcomes model from (5).
Constructing the instruments that appear in Theorem 2 requires us to evaluate Q 0 and Q 1 at (C ig , N g ). While the group size N g is observed, the share of compliersC ig is not. In large groups, however,C ig can be precisely estimated by calculating the rate of treatment take-up among the neighbors of (i, g) who are offered treatment. In the following section we use this approach to provide consistent and asymptotically normal estimators of the parameters from Theorem 2. For the remainder of this section, however, we consider identification conditional on knowledge ofC ig . Subject to this qualification, the following result catalogues the full set of causal effects that are identified under our assumptions.
Theorem 3. Given knowledge ofC ig the following are identified under Assumptions 1-7: Part (i) of Theorem 3 is an indirect treatment effect, as defined in (4) above. It measures the causal impact of increasing the treatment take-up rate among Alice's neighbors fromd to (d + ∆) when Alice's own treatment is held fixed at zero. In the Crépon et al. (2013) experiment discussed in our empirical example below, this corresponds to the average labor market displacement effect. Whereas part (i) is an average treatment effect, parts (ii)-(iv) are the effects of treatment on the treated. 9 Part (ii) gives the direct effect of treating Alice while holding the treatment take-up rate of her neighbors fixed atd, while (iii) and (iv) give the indirect effect of increasing her neighbors' treatment take-up fromd tod + ∆ while holding Alice's treatment fixed at either zero, part (iii), or one, part (iv). Part (v) is a LATE generalization of Equation 4: it gives the indirect effect for never-takers, holding their treatment fixed at zero. While we identify the full set of direct and indirect effects for the treated sub-population, we only identify a subset of these effects for other groups. By definition, never-takers cannot be observed with D ig = 1. As such, we cannot identify direct treatment effects for this group or indirect treatment effects when D ig is held fixed at one.
This in turn implies that we cannot identify the average direct effect for the population as a whole, DE(d), or the average indirect effect when D ig is held fixed at one, IE 1 (d, ∆).
Given that Q 0 and Q 1 are completely determined by the experimental design, we can directly check part (ii) of Assumption 7 for any choice of basis functions f and probability distribution over saturations. Consider again the linear potential outcomes model from (5).
In this example f (x) = (1, x) ′ and thus, by Bayes' Theorem, the Law of Total Probability, and Lemmas 1 and A.2. Suppose first that there is a single saturation s. Then (12) and (13) simplify to yield so that Q 0 (c, n) and Q 1 (c, n) are both invertible for any n and allc greater than zero provided that 0 < s < 1. The identifying power of this "degenerate" randomized saturation design, however, is weak: Q 0 , Q 1 are arbitrarily close to being singular for anyc if n is sufficiently large. Consider next a so-called "cluster randomized" experiment in which there are two saturations, 0 and 1, and È(S g = 1) = p. Calculating the expectations in (12) and (13), In this case neither Q 0 nor Q 1 is invertible for any values of n andc. Finally, consider a design with two distinct, equally likely saturations s L < s H . For this design, straightforward but tedious algebra gives .
So long as neither s L nor s H equals zero or one, both terms in each expression are strictly positive for anyc > 0, so that Q 0 and Q 1 are invertible. Moreover, in contrast to the single saturation design discussed above, this design does not suffer from a weak identification problem. While the second term in each of the preceding equalities vanishes for large n, the first term does not. Thus, two interior saturations are sufficient to strongly identify the linear potential outcomes model. 10 As the three preceding examples show, two distinct sources of experimental variation determine the rank of Q 0 (c, n) and Q 1 (c, n): "between" saturation variation, and "within" saturation variation. Our first example lacks "between" variation because each group is assigned the same saturation, S g = s. Yet even with a single saturation, there is still "within" variation under Assumption 2, because the number of offers made to a given group is random. This "within" variation, however, is negligible when n is large. In our second example, the cluster randomized experiment, the situation is reversed. Because everyone in a given group is either offered (S g = 0) or unoffered (S g = 1), this design generates no "within" variation. While a cluster randomized design does generate some "between" variation, it is too coarse to identify our effects of interest: under our assumptionsD ig equals zero when S g = 0 andC ig when S g = 1. Our third example, with two saturations 0 < s L < s H < 1, features sufficient "between" variation to identify the effects of interest even when n is so large that "within" variation becomes negligible.

Estimation and Inference
IfC ig were observed, a handful of just-identified IV regressions would suffice to estimate the causal effects from Theorem 3. WhileC ig is unobserved in practice, fortunately we can estimate it under one-sided non-compliance by comparing treatment take-up to the share of treatment offers, i.e.
where we arbitrarily define C ig = 0 if none of (i, g)'s neighbors are offered treatment. 11 In this section we use (14) to derive feasible, consistent, and asymptotically normal estimators of the direct and indirect causal effects identified in section 3. For simplicity, we assume throughout that the random saturation S g is bounded below by s > 0. Because we cannot  (15) for the four sample analogue estimators corresponding the parts of Theorem 2. In each part, the vector of regressors is X ig , the true instrument vector is Z ig ≡ R(C ig , N g ) −1 W ig , and the estimated instrument vector is Z ig ≡ R( C ig , N g ) + W ig , where M + denotes the Moore-Penrose inverse of a square matrix M, and C ig is as defined in (14). The functions Q, Q 0 , Q 1 are as defined in (8)-(10).
estimateC ig when S g = 0, experiments that include a 0% saturation require a slightly different approach. We explain these differences in Appendix B.
In the interest of brevity, we introduce shorthand notation and high-level regularity conditions that apply to all four of our sample analogue estimators. These take the form where Y ig is the outcome variable from Assumption 3, and M + denotes the Moore-Penrose inverse of a square matrix M. Table 1 gives the definitions of X ig , R, and W ig corresponding to each part of Theorem 2. The "estimated" instrument Z ig is a stand-in for the unobserved "true" instrument Z ig ≡ R(C ig , N g ) −1 W ig . While R(C ig , N g ) is invertible under Assumption 7, R( C ig , N g ) may not be so, since C ig could fall outside the support set ofC ig or even equal zero. For this reason we define Z ig using the Moore-Penrose inverse, which always exists and coincides with the ordinary matrix inverse when R( C ig , N g ) is indeed invertible. As G grows, so does the number of unknown valuesC ig that we must estimate to construct the instrument vectors Z ig . 12 For this reason, we consider an asymptotic sequence in which the minimum group size n grows along with the number of groups G. Under appropriate assumptions, this implies that the limit behavior of ϑ coincides with that of the infeasible estimator that uses the true instrument vector Z ig instead of its estimate Z ig . Like Baird et al. (2018), we take an infinite population approach to inference, assuming that the researcher observes a random sample of size G from a population of groups. Unlike Baird et al. (2018), we allow these groups to differ in size. Upon drawing a group g from the population, we observe the group-level random variables (S g , N g ) along with the individuallevel random variables (Y ig , D ig , Z ig ) for each member of the group: 1 ≤ i ≤ N g . We further assume that observations are identically distributed, but not independent, within groups. 13 Groups are only observed as a unit: either everyone from the group appears in the sample or no one does. For this reason, some care is needed in defining random variables to represent our sampling procedure and expectations to represent the population averages that define our causal effects of interest. The expectations in Theorems 2-3 are averages that give equal weight to each individual in the population, or sub-population if we condition on C ig . Analogously, the estimator in (15) is an average that gives equal weight to each individual in the sample. Both of these are precisely what we want, as our goal is to identify and estimate average causal effects for individuals. Under the sampling assumptions introduced in the preceding paragraph, (Y ig , D ig , Z ig ,D ig ) are random variables that are drawn by choosing a group uniformly at random from the population of groups, and then a single person from the chosen group. If all groups were the same size, this would be equivalent to choosing a person uniformly at random from the population of individuals. When groups vary in size, however, the equivalence no longer holds. 14 This creates the possibility for ambiguity when taking the expectation of an individual-level random variable, such as Y ig , without conditioning on group size: is the expectation intended to give equal weight to groups or individuals? Fortunately this is only a question of defining appropriate notation. Our group sampling procedure unambiguously gives equal weight to each individual in the population because we observe not isolated individuals but whole groups. While small groups are just as likely to be drawn as large groups, large groups make a greater contribution to the sample averages from (15) because they contain more people. 15 The question is merely how to represent this 13 The assumption that observations are identically distributed within group amounts to stipulating that the indices 1 ≤ i ≤ N g are assigned at random.
14 Consider a population of 100 groups, half of which have 5 members and the rest of which have 15 members so that 250 of the 1000 people in the population belong to a small group and the remaining 750 belong to a large group. Suppose first that we choose a single group at random and then a single person within the selected group. Then someone from a small group has probability 1/500 of being selected while someone from a large group has probability 1/1500 of being selected. 15 Continuing from the example in the preceding footnote: suppose that we randomly sample 10 groups and observe everyone in the selected group. Then, on average, our sample will contain 5 small groups and mathematically. Let ρ g ≡ N g / (N g ) denote the relative size of group g. We write [Y ig ] to denote the average that gives equal weight to groups-choosing one person at random from a randomly-chosen group-and [ρ g Y ig ] to denote the average that gives equal weight to individuals-observing an entire group chosen at random. It is the latter expectation that appears in our asymptotic results below, as it denotes the population equivalent of the double sums from (15). While this is a slight abuse of notation, expectations from section 3 above that involve individual-level random variables but do not condition on group size should be interpreted as (implicitly) weighting by relative group size. Using the notation and sampling scheme defined above, we now state high-level sufficient conditions for the consistency of ϑ from Equation 15.
Theorem 4. Let ρ g ≡ N g / (N g ) and suppose that (i) we observe a random sample of G groups, where observations within a given group are identically distributed although not necessarily independent, Then ϑ, defined in (15), is consistent for ϑ as G → ∞.

Condition (i) of Theorem 4 simply restates our group sampling assumption. Conditions
(ii) and (iii) hold under the assumptions of Theorem 2, as shown in the proof of that result: for each average effect ϑ from the theorem, we can define an appropriate error term U ig , vector of regressors X ig , and vector of instruments Z ig such that Y ig = X ′ ig ϑ + U ig where Z ig is an exogenous and relevant instrument. Moreover, for each part of Theorem 2, (ρ g Z ig X ′ ig ) equals the identity matrix. 16,17 Conditions (iv) and (v) of Theorem 4 would be implied by requiring that the second moments of ρ g Z ig X ′ ig and ρ g Z ig U ig exist and are bounded. We 16 For effects that condition on C ig = c, e.g. those from parts (ii) and (iii) of Theorem 2, the appropriate 17 Given that (ρ g Z ig X ′ ig ) = Á, we could have defined our estimator to be 1 N G g=1 Ng i=1 Z ig Y ig rather than ϑ. It is more convenient both for our asymptotic derivations and practical implementation, however, to work with an IV estimator. choose to state these conditions in a slightly weaker form because the distribution of ρ g necessarily changes with G if we consider an asymptotic sequence in which the minimum group size n increases with the number of groups, as we will assume below. Requiring the relevant expectations to be o(G) in principle allows the variance of relative group size ρ g to grow along with the number of groups, provided that it does not grow too quickly. Conditions (i)-(v) together are sufficient for the consistency of an infeasible estimator that uses the true instrument vector Z ig instead of its estimate Z ig . The final two conditions of Theorem 4 assume that Z ig is a sufficiently accurate estimator of Z ig to ensure that ϑ = ϑ + o È (1). In the setting we consider here, this will require a condition on how quickly the minimum group size n grows relative to G, as we discuss in detail below. Strengthening conditions (v) and (vii) and adding one further assumption implies that ϑ is asymptotically normal.
Theorem 5. Suppose that Then, under the conditions of Theorem 4, Combined with the first four conditions of Theorem 4, (i) and (ii) from Theorem 5 are sufficient for the asymptotic normality of ϑ, the infeasible estimator defined in (16). Condition (i) implies that the rate of convergence of ϑ is G −1/2 . Obtaining a rate of convergence that depends on the total number of individuals rather than groups in the sample would require assumptions that are implausible in typical applications of the randomized saturation design. 18 Conditions (ii) and (iii) strengthen (v) and (vii), respectively, from Theorem 4: (ii) is sufficient for the Lindeberg condition, which we use to establish a central limit theorem, while (iii) ensures that the limit distribution of the feasible estimator ϑ coincides with that of the infeasible estimator ϑ. 18 Obtaining the faster rate of convergence would require Var 1 Ng Ng i=1 ρ g Z ig U ig → 0 as G → ∞. Because we consider an asymptotic sequence in which the minimum group size grows with G, this is technically possible. It would, however, require us to assume that both heterogeneity between groups and dependence within groups to vanish in the limit.
Conditions (vi)-(vii) of Theorem 4, along with condition (iii) of Theorem 5, require the difference ( Z ig − Z ig ) to be sufficiently small on average that the limiting behavior of ϑ coincides with that of the infeasible estimator. We now provide low-level sufficient conditions for this to obtain. By definition, Accordingly, so long as R is a sufficiently well-behaved function, ( Z ig − Z ig ) will be small if | C ig −C ig | is. As shown in the following lemma, a sufficient condition for this difference to vanish uniformly over (i, g) is for the minimum group size n to be large relative to log G.
Lemma 4. Suppose that 0 < s ≥ S g and n ≤ N g . Under Assumptions 1-2 and 4-6 The following regularity conditions are sufficient for R( C ig , N g ) + −R(C ig , N g ) −1 to inherit the asymptotic behavior of ( C ig −C ig ).
Parts (i) and (ii) of Assumption 8 require that R is well-defined and uniformly invertible over a range of values forc that includes the support ofC ig and excludes zero. Part (iii) is a variant of Lipschitz continuity that holds in the limit as n grows. These conditions are mild: they amount to a slight strengthening of the rank condition from Assumption 7. In the linear basis function example from (12) and (13), for instance, Assumption 8 holds whenever C ig is bounded away from zero and S g takes on at least two distinct values between zero and one. 19 More generally, provided that Assumption 7 holds, wheneverC ig is bounded away from zero and the basis functions f are well-behaved, we can always extend the definitions of Q 0 , Q 1 from (9)-(10) to ensure that Assumption 8 holds. See Appendix C for full details. Under this assumption, we can derive sufficient conditions on the rates at which G and n approach infinity to ensure that the difference between Z ig and Z ig is negligible.
19 See the discussion in section 3 immediately following (12) for details. Theorem 6. Suppose that ρ 2 g ||W ig X ′ ig || 2 and ρ 2 g ||W ig U ig || 2 are both o(G). Then, under condition (i) of Theorem 4 and the conditions of Lemma 4, (i) log G/n → 0 is sufficient for conditions (vi)-(vii) of Theorem 4.
(ii) G log G/n → 0 is sufficient for condition (iii) of Theorem 5.
Taken together, Theorems 4-6 establish that ϑ from (15) is consistent, and asymptotically normal in the limit as G and n grow at an appropriate rate. In practical terms, our estimators are appropriate for settings with many large groups such as the experiment of Crépon et al. (2013). To implement them in practice, all that is required is to calculate the estimated instrument Z ig and then run the appropriate just-identified IV regression from Table 1 with standard errors clustered by group.

Conclusion
In this paper we have proposed methods to identify and estimate direct and indirect causal effects under one-sided non-compliance, using data from a randomized saturation experiment.
Under appropriate assumptions, we show that the key source of unobserved heterogeneity is the share of compliers within a given group. In a setting with many large groups, this quantity can be estimated and yields a simple IV estimator that is consistent and asymptotically normal in the limit as group size and the number of groups grow. A possible extension of the methods described above would be to consider settings with two-sided non-compliance.
In this case our identification approach would condition on the share of always-takers in addition to the share of compliers. Another interesting extension would be to consider relaxing Assumption 5 to allow some dependence of individuals' take-up decisions on the offers of their peers. Work currently in progress explores this possibility.

A Proofs
The following lemma, taken from Constantinou and Dawid (2017) summarizes several useful properties of conditional independence that we use in our proofs below. The names attached to properties (i) and (iii)-(v) are taken from Pearl (1988). For the purposes of this document, we call the second property "redundancy." Lemma A.1 (Axioms of Conditional Independence). Let X, Y, Z, W be random vectors defined on a common probability space, and let h be a measurable function. Then: For simplicity, our proofs below freely use the "Symmetry" property without comment, although we reference the other properties when used. We also rely on the following corollary of Lemma A.1.
Proof of Lemma 1. Applying Corollary A.1 and the Decomposition property to Assumption 6(ii) yields Z g |= (C g ,C ig )|(N g , S g ). By the definition of conditional independence, it follows that the distribution of Z g |(N g , S g , C g ,C ig ) is the same as that of Z g |(N g , S g ): È(Z g = z|N g = n, S g = s, C g ,C ig ) = È(Z g = z|N g = n, S g = s).
where the first equality uses the fact that A implies N g = n, and the second uses the fact that A implies C g = c, so we know precisely which of the indicators C jg equal zero and which equal one. Under Assumption 2, (A.1) implies that Z g |A ∼ iid Bernoulli(s). By our definition of C(i) it follows that, conditional on A, the subvector of Z g that corresponds to C(i) constitutes an iid sequence ofc(n − 1) Bernoulli(s) random variables, each of which is independent of Z ig . Hence, conditional on (A, Z ig ), we see that j∈C(i) Z jg ∼ Binomial c(n − 1), s .
since Z ig and B ig are R ig -measurable. Now, applying Decomposition and Corollary A.1 to part (ii) of Assumption 6 gives Z ig |= (C ig ,C ig , B ig )|(S g , N g ). Under Bernoulli offers, however, this conditional distribution does not involve N g , so we obtain Similarly, applying Decomposition to part (ii) of Corollary A.1, we see that (C ig ,C ig , B ig ) |= S g . Combining this with (A.2), the Contraction axiom yields (C ig ,C ig , B ig ) |= (Z ig , S g ), implying that (Z ig Z ′ ig ) is independent of both Λ ig and (Λ ig B ig ). Accordingly, By the definitions of ϑ IV , Λ ig and B ig it follows that By iterated expectations over C ig , we obtain β IV = [β ig |C ig = 1] while Similarly, again taking iterated expectations over C ig , Proof of Theorem 1. Assumption 6(i) implies (C g , B g ) |= S g |N g by Weak Union and Decomposition. Combining this with Assumption 6(ii) gives by Contraction. Now let C −ig denote the subvector of C g that excludes element i. Applying Decomposition, Corollary A.1, and Weak Union to (A.3), becauseC ig is a function of (C g , N g ). By Lemma 1, Applying Decomposition to (A.4) gives C −ig |= (S g , Z ig )|(N g ,C ig ). Combining this with (A.5), by Contraction. Now, applying Weak Union, Decomposition, and Corollary A.1 to (A.4), sinceD ig is a function of (Z g , C −ig , N g ). Finally, applying Contraction to (A.6) and (A.7), and the result follows by a final application of Decomposition.
Proof of Lemma 3. Define the shorthand U ≡ Q(c, n), A ≡ Q 0 (c, n), and B = Q 1 (c, n) so that Using this notation, we are asked to show that U is invertible if and only if A and B are both The "if" direction follows by direct calculation: V U = U V = Á. For the "only if" direction, suppose that U is invertible. Partitioning U −1 into blocks (C, D, E, F ) conformably with the partition of U , we have Proof of Theorem 2. For each part, it suffices to find an appropriate outcome variable Y ig , regressor vector X ig , and instrument set Z ig such that we can write Y ig = X ′ ig ϑ + U ig where ϑ is the parameter of interest, [ Z ig U ig ] = 0, and [ Z ig X ′ ig ] is invertible. Note that ( X ig , Y ig , Z ig ) are placeholders for quantities that differ in each part of the proof: for part (i) they represent (X ig , Y ig , Z W ig ) while for part (ii) they stand for D ig f (D ig ), D ig Y ig , Z 1 ig , for example. The definitions of U ig and ϑ are also specific to each part of the proof.

We begin by showing that
Since M ig is symmetric, by Decomposition, since W ig W ′ ig is a measurable function of (Z ig ,D ig ) and M ig (B ig − ϑ) is a measurable function of (C ig , B ig ). Substituting into the expression for [ Z ig U ig ], . The remainder of the argument is similar to that of part (i). Taking Z ig ≡ Z 1 ig and substituting D ig = Z ig C ig gives . The remainder of the argument is similar to that of part (i).
It follows that [ Z ig X ′ ig ] is invertible by Assumption 7.
Since (C ig ) = (D ig |Z ig = 1), it follows that (θ ig |C ig = 1) is identified. Under IOR and one-sided non-compliance {D ig = 1} = {C ig = 1, Z ig = 1}, and applying Weak Union and Decomposition to Lemma A.2, we see that Z ig |= B ig |C ig . Thus, Proof of Theorem 4. Substituting the model into the definition of ϑ and ρ g ≡ N g / (N g ), By assumption, both || G g=1 R (1) g || and || G g=1 R (2) g || are o È (G) and thus Now, since we observe a random sample of groups and A g is a group-level random variable  where the second equality uses iterated expectations and linearity, the third uses the assumption of identical distribution within groups, and the the fourth uses iterated expectations a second time. Now consider an arbitrary entry A (j,k) g of the matrix A g and let · F denote the Frobenius norm. By the triangle and Cauchy-Schwarz inequalities, and using the assumption of identical distribution with group, we have since all finite-dimensional norms are equivalent and Á. An analogous argument shows that The result follows by the continuous mapping theorem.
Proof of Theorem 5. Continuing the argument from the proof of Theorem 4, we have By assumption, || G g=1 R (2) g || = o È (G 1/2 ), and hence it suffices to apply the Lindeberg-Feller central limit theorem to P g / √ G. Because we observe a random sample of groups, Var( G g=1 P g / √ G) = Var(È g ) which by assumption converges to Σ. All that remains is to verify the Lindeberg condition, namely for any ε > 0. A sufficient condition for this to hold is G −δ/2 ||P g || 2+δ → 0 for some δ > 0.
By an argument similar to that used to establish where the second inequality follows since s ≤ s. Thus, È(Z g < s/2) = n,s È(Z g ≤ s/2|N g = n, S g = s)È(N g = n, S g = s) ≤ exp −2ns 2 /4 by the law of total probability. The result follows since È(Z g < s/2) ≤ È(Z g ≤ s/2).
Lemma A.4. LetC g = Ng j=1 C jg /N g and C g ≡ Ng j=1 D jg /N gZg , whereZ g is as defined in Lemma A.3. Under the conditions of Lemma 4 and for any t > 0, Proof of Lemma A.4. Let A ≡ C g = c, N g = n,C g =c, N gZg = m, S g = s where m > 0. Suppose first thatc = 0. In this case Moreover, since Z jg ∈ {0, 1}, each of the Z * jg is bounded between 0 and nc/m. While these random variables are identically distributed, they are not independent-like the Z jg from which they are constructed, Z * jg j∈C are draws made without replacement from a finite population. Under this form of dependence, however, Hoeffding's Inequality continues to apply (Hoeffding, 1963, p. 28) and hence where the second inequality follows because 0 <c ≤ 1. Ifc = 0, we have so this inequality holds for anyc. Applying the law of total probability as in the proof of Lemma A.3, we see that and thus 2 exp −ns 2 t 2 /2 È(N gZg = m, N g = n|Z g ≥ s/2) = exp −ns 2 t 2 /2 by a second application of the law of total probability, since n ≤ N g .

Similar manipulations giveC
by the triangle inequality. Using the fact that Z ig , D ig , and C ig are binary along with n ≤ N g and Z g > s/2 > 1/n, tedious but straightforward algebra allows us to bound the right-hand side of the preceding inequality from above, yielding C ig −C ig ≤ sn sn − 2 2 C g −C g + sn sn − 2 2 + 1 4 sn − 2 .
Since this upper bound for | C ig −C ig | does not depend on i, it follows that max 1≤i≤Ng C ig −C ig ≤ sn sn − 2 2 C g −C g + sn sn − 2 2 + 1 4 sn − 2 provided thatZ g > s/2 > 1/n. In other words, so long as sn > 2 we have Z g ≥ s/2 ∩ max 1≤i≤Ng C ig −C ig > t ⊆ Z g > s/2 ∩ C g −C g > h(sn, t) .
Therefore, by the monotonicity of probability È max 1≤i≤Ng C ig −C ig > t Z g ≥ s/2 ≤ È C g −C g > h(sn, t) Z g ≥ s/2 and the result follows by Lemma A.4.
Proof of Theorem 6. We provide the argument for condition (vii) of Theorem 4 and (iii) of Theorem 5 only. For (vi) from Theorem 4, simply replace U ig with X ig in the following derivations. By (17) and the triangle inequality where we define the shorthand Consider the second factor on the RHS of (A.9). By an argument similar to that used in the proof of Theorem 4, . Now, define the event 1 G as By assumption R(C ig , N ig ) is invertible, and conditional on C ig ≥c L /2 it follows that R( C ig , N g ) is likewise invertible. Hence, if 1 G = 1 we can write Let ||M|| 2 denote the spectral norm of a matrix M, i.e. its largest singular value. Since R(C ig , N g ) is square, symmetric, and positive definite we have ||R(C ig , N g ) −1 || 2 ≤ 1/σ < ∞. Similarly, if 1 G = 1, then ||R( C ig , N g ) −1 || 2 ≤ 1/σ < ∞. Because all finite-dimensional norms are equivalent, it follows that where 0 < K < ∞ denotes a generic, unspecified constant. Applying Lemma 4 we see that 1 G ∆ G = O È log G/n as (n, G) → ∞. Thus, by (A.9), (A.10) If log G/n → 0 as (n, G) → ∞, then the rate on the RHS of (A.10) becomes o È (G). If G log G/n → 0, it becomes o È (G 1/2 ). Finally, sincec L ≤C ig , it follows that Hence, applying Lemma 4, log G/n → 0 implies 1 G → p 1. The result follows.

B Experiments with a 0% Saturation
Some randomized saturation designs, including the experiment of Crépon et al. (2013), include a zero percent saturation, also known as a "pure control" condition. Under one-sided non-compliance S g = 0 implies Z ig = D ig =D ig = 0 for all 1 ≤ i ≤ N g . Accordingly, we cannot estimate the share of compliers C ig from (14) for groups assigned a saturation of zero. The easiest solution to this problem is simply to drop observations for any zero saturation groups. Under Assumptions 1-2 and 6 this has no effect on our identification or large-sample results provided that we replace Q, Q 0 and Q 1 with expectations that condition on S g > 0, namely Q(c, n) ≡ W ig W ′ ig |C ig =c, N g = n, S g > 0 Q 0 (c, n) ≡ (1 − Z ig )f (D ig )f (D ig ) ′ |C ig =c, N g = n, S g > 0 Q 1 (c, n) ≡ Z ig f (D ig )f (D ig ) ′ |C ig =c, N g = n, S g > 0 .
Zero percent saturation groups, however, are informative: they pin down the value of [Y ig (0, 0)] and hence can be used to improve estimates of [θ ig ]. To exploit this information, we replace the instrument vector from part (iv) of Theorem 2 with .
Calculations similar to those in the proof of Theorem 2 establish that this is a valid and relevant instrument. Because its dimension exceeds that of θ ig by one, this instrument vector provides over-identifying information. As such, the just-identified IV moment condition from part (iv) of Theorem 2 must be replaced with a linear GMM moment equation. Subject to this small change, estimation and inference can proceed almost exactly as in section 4: we merely substitute C ig for C ig in Q 0 to yield a feasible GMM estimator, e.g. two-stage least squares. With minor notational modifications, our large-sample results continue to apply.