Spillover Effects in Cluster Randomized Trials with Noncompliance

Submitted to the Annals of Statistics arXiv: arXiv:0000.0000

SPILLOVER EFFECTS IN CLUSTER RANDOMIZED TRIALS WITH NONCOMPLIANCE

By Hyunseung Kang, Luke Keele University of Wisconsin-Madison and University of Pennsylvania

Cluster randomized trials (CRTs) are popular in public health and in the social sciences to evaluate a new treatment or policy where the new policy is randomly allocated to clusters of units rather than individual units. CRTs often feature both noncompliance, when individuals within a cluster are not exposed to the intervention, and individuals within a cluster may influence each other through treatment spillovers where those who comply with the new policy may affect the outcomes of those who do not. Here, we study the identification of causal effects in CRTs when both noncompliance and treatment spillovers are present. We prove that the standard analysis of CRT data with noncompliance using instrumental variables does not identify the usual complier average causal effect when treatment spillovers are present. We extend this result and show that no analysis of CRT data can unbiasedly estimate local network causal effects. Finally, we develop bounds for these causal effects under the assumption that the treatment is not harmful compared to the control. We demonstrate these results with an empirical study of a deworming intervention in Kenya.

1. Introduction. Policy interventions are often evaluated by randomized controlled trials as random allocation of policy/treatment removes se- lection biases. However, there are two well-known complications in such trials. First, an individual’s outcome may be influenced by him/her as well as his/her peers’ treatment assignment, a phenomena known as interference [15], and spillover effects [54] may occur. To mitigate concerns from spillovers, investigators often use clustered treatment assignments, usually in the form of cluster randomized trials (CRTs), to allow for arbitrary treatment spillovers within clusters [14, 43, 34]. Second, subjects in the study may not comply with their randomized treatment assignment. For example, arXiv:1808.06418v2 [stat.ME] 15 Aug 2019 some may refuse to take the treatment or seek out treatment contrary to their treatment allocation. The method of instrumental variables (IV) is a well-understood framework to analyze randomized experiments with noncompliance; see Angrist and Krueger [5], Hernánand Robins [21], Imbens

MSC 2010 subject classiﬁcations: Primary 62K99, 62K99; secondary 62K99 Keywords and phrases: interference, cluster randomized trial, noncompliance, instrumental variables 1 2 KANG AND KEELE

[31] and Baiocchi, Cheng and Small [7] for overviews. Increasingly, policy interventions exist at the intersection of these two complexities and our goal is to explore the consequences of spillovers and noncompliances in CRTs. There is a large literature on both treatment spillovers and noncompliance, but typically these two topics are studied in isolation. In the literature on noncompliance in CRTs [18, 53, 35, 29, 51], treatment spillovers are generally considered a nuisance and their effects are minimized by clustered treatment assignment. For example, Small, Ten Have and Rosenbaum [53] notes that “the issue of interference...does not arise” in CRTs (Section 2.1 of Small, Ten Have and Rosenbaum [53]) and Imai et al. [29] assumes no interference (Assumption 3 in Section 6.2 of Imai et al. [29]). In the growing literature on interference and spillover effects [19, 20, 54, 25, 49, 27, 57, 58, 59, 10,6], the primarily focus is on defining or estimating network causal quantities and treatment compliance is ignored. Some notable exceptions include Sobel [54], Hong [24],Forastiere, Mealli and VanderWeele [17], Kang and Imbens [36], and Imai, Jiang and Malai [28]. Sobel [54] highlighted problems when noncompliance and interference are both present in non-clustered designs, but did not provide methods to estimate the spillover effects formalized in Hud- gens and Halloran [27]. Forastiere, Mealli and VanderWeele [17] studied noncompliance and interference under a Bayesian paradigm. Kang and Imbens [36] and Imai, Jiang and Malai [28] studied noncompliance and interference under multi-level designs where randomization occurs multiple times and in different hierarchical levels. In contrast, CRTs have only have one level of randomization, which is at the cluster level. Hong [24], in Chapter 15.2, studied noncompliance and interference under the mediation framework. Here, we study the identification of causal effects in CRTs when both noncompliance and interference are present. First, we show that the standard analysis of CRTs with noncompliance using the instrumental variables (IV) framework, following the methods in Small, Ten Have and Rosenbaum [53], Jo, Asparouhov and Muthén[35], and Schochet and Chiang [51], does not identify the usual causal estimand known as the complier average causal effect (CACE) in the presence of spillover effects. Second, we extend our result and show that no analysis of CRTs can unbiasedly estimate network effects under noncompliance when interference is present; specifically, we show that there does not exist a function of the observed data from CRTs that can unbiasedly estimate the causal parameters. The second result suggests that CRTs, as an experimental design, are generally unsuited to learn about treatment spillovers in the presence of noncompliance and a new experimental design or stronger assumptions about the data are necessary to study network effects in the presence of noncompliance. Third, we show SPILLOVER EFFECTS WITH NONCOMPLIANCE 3 that for data from CRTs with noncompliance, investigators can estimate bounds on spillover and total effects under an assumption about treatment monotonicity.

2. Preliminaries: Notation and Assumptions. We structure the notation and motivate the assumptions using a public health intervention called the Primary School Deworming Project (PSDP), which we analyze in later sections. PSDP was conducted by a Dutch nonprofit organization, International Christelijk Steunfonds Africa (ICS), in cooperation with the Busia District Ministry of Health office [42]. The intervention consisted of deworming treatments for intestinal helminths such as hookworm, round- worm, whipworm, and schistosomiasis, delivered to school children in south- ern Busia, an area in Kenya with the highest helminth infection rates. The primary goal was to evaluate whether the deworming treatments on reduced intestinal helminths infections among students. The intervention was evaluated using a CRT, where the new treatment was randomly allocated to different schools that served as clusters, and as such, all students in treated schools were offered deworming treatments in the form of oral medications. The medication was believed to have both direct and spillover effects; it not only killed helminths among those who took them (i.e. direct effect), but also decreased disease transmission among peers by reducing the number of helminths in the environment (i.e. a spillover effect) since students were primarily exposed to intestinal helminths through environmental exposures such as outdoor defecation and contact with infected fresh water. Also, unit level noncompliance occurred as the investigators were required to obtain parental consent for the study. Even when parental consent was obtained, students in treated schools did not always take the deworming treatments.

2.1. Notation. There are J clusters indexed by j = 1,...,J and for each cluster j, there are nj individuals, indexed by i = 1, . . . , nj. There are PJ N = j=1 nj total individuals in the study population. Let Zj ∈ {0, 1} denote the treatment assignment of cluster j where Zj = 1 indicates that cluster j was assigned to treatment and Zj = 0 indicates that cluster j was assigned to control. Let Dji ∈ {0, 1} denote the observed treatment receipt of individual i in cluster j where Dji = 1 indicates that individual i actually took the treatment and Dji = 0 indicates that individual i did not take the treatment (i.e. control). Note that while the treatment is assigned at the cluster level, the decision to comply occurs at the unit level and hence, there is an extra subscript i in Dji. This is important because in the aforementioned PDSP study, schools were assigned to the intervention, but each student and parent in a school could choose to comply with the 4 KANG AND KEELE intervention. Let Yji ∈ R represent the observed outcome of individual i in cluster j. Let Y = (Y11,Y12,...,YJnJ ), D = (D11,D12,...,DJnJ ), and Z = (Z1,...,ZJ ) be the outcome, compliance, and treatment assignment vectors, respectively. Let Bp = {0, 1}p be the set of all binary vectors of length p. For any p vector v ∈ B and integer k ∈ {1, . . . , p}, let v−k denote the vector v with the kth index removed. Let I(·) denote an indicator function where I(·) = 1 if the event inside the indicator function is true and 0 otherwise. Finally, let 1 = (1,..., 1) ∈ Bp be a vector of ones.

2.2. Potential Outcomes, SUTVA, and Treatment Compliance Hetero- geneity. We define causal effects using the potential outcomes notation (zj ) [45, 50]. For each zj ∈ {0, 1}, let Dji denote individual i’s potential (zj ) treatment receipt if his cluster j were assigned treatment zj. Let Dj = (D(zj ),...,D(zj )) denote the vector of potential treatment receipts for cluster j1 jnj j. For each zj ∈ {0, 1}, dji ∈ {0, 1} and dj−i = (dj1, . . . , dji−1, dji+1, . . . , djnj ) ∈ (z ,d ,d ) nj −1 j ji j−i B , let Yji denote individual i’s potential outcome if his cluster j were assigned treatment zj, his treatment compliance were dji, and his peers’ (zj ) (zj ) (zj ,Dji ,Dj−i ) treatment receipt were dj−i. Also, let Yji denote individual i’s potential outcome if his cluster j were assigned treatment zj and he and his (zj ) (zj ) peers’ treatment receipts were their “natural” compliances Dji and Dj−i , (zj ) (zj ) (zj ) (zj ) (z ,D ,D ) (zj ,D ,D ) (zj ) j j1 j−1 jni j−ni respectively. Let Yj = (Yj1 ,...,Yji ) denote the (zj ,dji,dj−i) (zj ) vector of potential outcomes for cluster j. Let F = {Yji ,Dji | n −1 zj, dji ∈ {0, 1}, dj−i ∈ B j , j = 1, . . . , J, i = 1, . . . , nj} be the set of all potential outcomes, which we assume to be fixed and unknown. Our notation assumes what Sobel [54] called partial interference, which is a particular violation of the stable unit treatment value assumption (SUTVA) (zj ) [50]. Specifically, the potential treatment receipt and outcome, Dji and (zj ,dji,dj−i) Yji respectively, are only affected by values from cluster j, specifically zj, dji, and dj−i; the potential treatment receipt and outcome are not 0 affected by values from other clusters j 6= j, say by zj0 , dj0i, and dj0−i. Also, in a CRT, clustered treatment assignment implies that we only observe the potential treatment receipt of individual i in cluster j when all (1) individuals in cluster j are assigned treatment, Dji , or when all individuals (0) are assigned control Dji ; we do not observe individual i’s potential treatment receipt when some individuals in cluster j are assigned treatment and SPILLOVER EFFECTS WITH NONCOMPLIANCE 5

(0,1,...,1) rest are assigned control. For example, we do not observe Dji where everyone except individual i in cluster j are assigned treatment. But, due to unit level noncompliance where only some individuals actually end up taking the treatment, our setting allows a fraction of individuals within a cluster to take the treatment so that we have variation in treatment receipt within a cluster. This is in contrast to the two-stage randomization design of Hudgens and Halloran [27] which has two stages of randomization, both at the cluster and the unit level, and treatment receipt is assumed to be randomly assigned. We consider a context where treatment receipt is self- selected because of noncompliance. Moreover, under interference, treatment compliance may be heterogeneous. The extant literature on CRTs with noncompliance has used po- (zj ,dji) tential outcomes of the form Yji where the outcome of individual i is a function of his own treatment receipt dji and his cluster treatment assignment zj [18, 53, 35, 29, 51]. The potential outcomes notation in this paper, (zj ,dji,dj−i) Yji , is a generalization of prior literature’s notation because individual i’s potential outcome is aﬀected both by his own compliance dji and the compliances of his peers dj−i. As a concrete example, in a hypothetical cluster of size nj = 2 that is assigned treatment zj = 1, individual i = 1’s (1) (1) (1,Dj1 ,Dj2 ) (1,1,0) potential outcome could be Yj1 = Yj1 if individual i = 1 ac- (1) tually took the treatment so that Dj1 = 1 and individual i = 2 did not (1) take the treatment so that Dj2 = 0. Alternatively, individual i = 1’s po- (1,0,0) tential outcome could be Yj1 if individual i = 1 refused treatment so (1) that Dj1 = 0. Prior literature’s notation would assume these two potential (zj ,0,1) (zj ,0,0) outcomes are equal, Yj1 = Yj1 . In contrast, our notation makes it explicitly clear that interference can exist and if it exists, it originates from heterogeneous noncompliance of each individual unit.

2.3. Assumptions. Next, we review the assumptions that are standard in the literature on noncompliance and interference; detailed discussions can be found in Angrist, Imbens and Rubin [4] and Baiocchi, Cheng and Small [7] (for noncompliance) and Hudgens and Halloran [27] (for interference). We invoke this set of assumptions to understand what can be identiﬁed from CRTs under extant assumptions. (A1) Cluster Randomized Assignment. Let Z be the set that consists of J PJ vectors z = (z1, . . . , zJ ) ∈ B such that m = j=1 zj for 0 < m < J. Then, m out of J clusters are randomly assigned treatment and J − m 6 KANG AND KEELE

are assigned control. 1 P (Z = z | F, Z) = P (Z = z | Z) = J m (A2) Non-Zero Causal Eﬀect of Z on D. The treatment assignment has a non-zero average causal eﬀect on compliance.

J nj 1 X X (1) (0) τ = D − D 6= 0 D N ji ji j=1 i=1

(A3) Network Exclusion Restriction. Given individual i’s compliance dji and n −1 the compliances of others dj−i ∈ B j , the treatment assignment zj has no impact on the potential outcome of individual i.

(1,dji,dj−i) (0,dji,dj−i) (dji,dj−i) Yji = Yji ≡ Yji

(0) (1) (A4) Monotonicity. For every individual i in cluster j, we have Dji ≤ Dji . (A5) Stratiﬁed Interference. Given individual i’s compliance dji, his cluster treatment assignment zj, and a whole number k ∈ {0, 1, . . . , nj − 1}, the potential outcomes of individual i are equivalent when exactly k of his peers are taking the treatment.

(zj ,dji,dj−i) (zj ,dji,dej−i) (zj ,dji,[k]) nj −1 X X Yji = Yji ≡ Yji , ∀dj−i, dej−i ∈ B where k = dji0 = deji0 i06=i i06=i

We briefly comment on these assumption within the context of the PSDP, our motivating example. Assumption (A1) is approximately satisfied by the design of the PSDP where the deworming intervention was randomized to schools (i.e. clusters); see Miguel and Kremer [42] and Hicks, Kremer and Miguel [22] for additional details on the treatment assignment process. As- sumption (A1) also allows us to test assumption (A2) in the PSDP by taking the stratified difference-in-means of the observed compliance values Dji between the treated and control clusters; see Section5 for a numerical illustra- tion. Assumption (A3), like the usual exclusion restriction in the noncompliance literature [4], cannot be tested with data because it requires observing potential outcomes under both treatment zj = 1 and control zj = 0; typically, subject-matter expertise must be used to justify this assumption. In the PSDP, assumption (A3) implies that the random assignment of the deworming treatments had an effect on the outcome, say a student’s infection status, only through students taking the oral medications. If the random SPILLOVER EFFECTS WITH NONCOMPLIANCE 7

assignment induced better hygiene at the school leading to lower infection rates and this is not captured by the treatment receipt values dji or dj−i, the exclusion restriction would be violated. Assumption (A4) can be interpreted by partitioning the study population into four groups, compliers (CO), always-takers (AT), never-takers (NT), and defiers (DF) [4]. In the PSDP, compliers are students who fol- (1) (0) low the intervention, Dji = 1 and Dji = 0. Always-takers are students who always take the deworming treatments, irrespective of the intervention, (1) (0) Dji = Dji = 1. Never-takers are students who never take the deworming (1) (0) treatments, irrespective of the intervention, Dji = Dji = 0. Defiers are the opposite of compliers in that they systematically defy the intervention, (1) (0) Dji = 0 and Dji = 1. Assumption (A4) implies that there are no defiers in the PSDP population. In many CRTs, including the PSDP, assumption (A4) can be satisfied by the study design by denying individuals in clusters that are randomized to the control to seek out the treatment; in the PSDP, the students in the control clusters did not have access to the new deworming medications. This is commonly referred to as one-sided noncompliance and is formalized as assumption (A4.1). (A4.1) One-Sided Noncompliance. For every individual i in cluster j, we have (0) Dji = 0 An implication of assumption (A4.1) is that there are no always-takers and defiers in the study population. Finally, assumption (A5) states that conditional on individual i’s compliance to treatment dji and his cluster treatment assignment zj, individual i’s (zj ,dji,dj−i) potential outcome Yji only depends on the number of individual i’s peers who took the treatment, not necessarily who took the treatment. Hudgens and Halloran [27] talks about the plausibility of this assumption in practice, especially in infectious disease studies like the PSDP, as well as the statistical importance of having this assumption to estimate standard errors and conduct asymptotics [39]. In our work, we make this assumption not out of technical necessity, but out of better interpretability; see Section 3.2 for details. Also, note that combining assumptions (A3) and (A5) leads to the original stratified interference assumption stated in Hudgens and Halloran [27].

2.4. Review: Causal Eﬀects under Noncompliance and Interference. Next, we review two causal estimands of interest when noncompliance or interference are present. First, under noncompliance, but without interference, the 8 KANG AND KEELE

(zj ,dji,dj−i) (zj ,dji) potential outcome Yji collapses to Yji and two causal effects of primary interest are the average intent-to-treat (ITT) effects and the ratio of these effects to identify the complier average treatment effect (CACE) [32,4]. The first ITT effect is with respect to Y and is denoted as τY :

J nj 1 X X (1,D(1)) (0,D(0)) τ = Y ji − Y ji Y N ji ji j=1 i=1

τY is the population average eﬀect of treatment assignment, not treatment receipt, on the outcome. The second ITT eﬀect is with respect to D and is denoted as τD: J nj 1 X X (Z(1)) (Z(0)) τ = D ji − D ji D N ji ji j=1 i=1

τD is also known as the compliance rate. Let τ be the ratio of the average ITT effect τY to the average effect of treatment assignment on compliance τ , D τ τ = Y τD where we assume (A2) holds so that τ is well-defined. Then, under (A2)-(A4) without interference, τ equals the complier average treatment effect.

J nj 1 X X (1) (0) (1) τ = (Y − Y )I(ji is CO) N ji ji CO j=1 i=1

In equation (1), NCO is the total number of compliers in the study population, which is non-zero because of (A2) and (A4). The CACE is also referred to as a local effect because it only represents the treatment effect of a particular subgroup in the population [32]. The CACE can be estimated by plugging in estimates of τY and τD that make up τ. Specifically, τY and τD can each be unbiasedly estimated under (A1) by taking the stratified difference-in-means of the observed outcomes Yji and treatment receipts Dji, respectively, between the treated and control clusters; see Section4 for details. This ratio estimator is known as the “Wald” or the IV estimator, and it is a special case of the two stage least squares (TSLS) estimator in the literature. However, when interference is present, it is unclear whether the ratio can be interpreted as the CACE. We explore this in Section 3.2. Second, under interference, but with full compliance, the potential out- (zj ,dji,dj−i) (dji,dj−i) come Yji collapses to Yji and causal effects of interest are the total, direct, and spillover effects, denoted as TEji, DEji, and PEji, SPILLOVER EFFECTS WITH NONCOMPLIANCE 9 respectively [27]. Formally, under stratified interference (A5), given two 0 nj −1 vectors of treatment receipts dj−i, dj−i ∈ B and two whole numbers k1, k0 ∈ {0, 1, . . . , nj − 1} that count the number of i’s peers that took the P P 0 treatment, i.e. k1 = i06=i dji0 and k0 = i06=i dji0 , the individual total, direct, and spillover/peer effects are defined as

0 (1,dj−i) (0,dj−i) TEji(1, k1; 0, k0) = Yji − Yji

(1,dj−i) (0,dj−i) DEji(1, k1; 0, k1) = Yji − Yji 0 (0,dj−i) (0,dj−i) PEji(0, k1; 0, k0) = Yji − Yji 0 (1,dj−i) (1,dj−i) PEji(1, k1; 1, k0) = Yji − Yji

TEji(1, k1; 0, k0) is individual i’s total casual effect if individual i and k1 of his peers took the treatment versus if individual i did not take the treatment while k0 of his/her peers did take the treatment. DEji(1, k1; 0, k1) is individual i’s direct causal effect if individual i took the treatment versus if individual i did not take the treatment and his peers’ treatment receipt was fixed at k1, i.e. if k1 of his peers took the treatment. PEji(0, k1; 0, k0) is individual i’s spillover causal effect if k1 of his peers took the treatment versus if k0 of his peers took the treatment and individual i’s treatment receipt remained fixed at dji = 0, i.e. individual i did not take the treatment. PEji(1, k1; 1, k0) is the same as PEji(0, k1; 0, k0) except individual i’s treatment receipt is fixed at dji = 1, i.e. individual i took the treatment. Without noncompliance, the population averages of individual total, direct, and spillover effects can be identified under a two-stage randomization design of Hudgens and Halloran [27] where some clusters are randomly allocated to the “k1 policy” that assigns k1 individuals in the cluster to treatment while the rest are assigned the “k0 policy” where k0 individuals in the cluster are treated and each individual are assigned treatment based on his cluster randomization policy.

3. Identiﬁcation.

3.1. Target Causal Estimands. To discuss the results in the paper, we introduce three causal estimands which may be of natural interest in CRTs when both noncompliance and interference are present and to the best of our knowledge, have not been discussed in either literature on noncompliance or interference. Broadly speaking, our three proposed causal estimands are the network estimands in Hudgens and Halloran [27] speciﬁc to subgroups of compliers, always-takers, and never-takers in Angrist, Imbens and Rubin 10 KANG AND KEELE

[4]. We also note that while a richer combinations of these two literatures and their effects are possible, we only discuss three combinations as they are the most relevant in our paper. AT CO NT Let nj , nj , and nj be the number of always-takers, compliers, and AT PJ AT CO never-takers, respectively, in cluster j and let N = j=1 nj , N = PJ CO NT PJ NT j=1 nj , and N = j=1 nj be the total number of always-takers, compliers, and never-takers, respectively, in the population. For each cluster j, let k0j, k1j ∈ {0, 1, . . . , nj −1}, k0j < k1j, indicate two different numbers of peers actually taking the treatment, similar to k0 and k1 in Section 2.4. For instance, in a hypothetical cluster of size nj = 10, k0j = 5 would indicate that 5 peers are taking the treatment in cluster j and k1j = 7 would indicate that 7 peers are taking the treatment in cluster j. Let k0 = (k01, . . . , k0J ) and k1 = (k11, . . . , k1J ) be collections of k0j and k1j, respectively, across all J clusters. We define the population average total effect of treatment on the outcome among compliers (CO)

J nj CO 1 X X (2) TE (1, k ; 0, k ) = TE (1, k ; 0, k )I(ji is CO) 1 0 N CO ji 1j 0j j=1 i=1

Each individual total effect in equation (2), i.e. TEji(1, k1j; 0, k0j)I(ji is CO), is the total effect of complier i when k1j of his peers are taking the treatment versus him not taking the treatment while k0j of his peers are taking the treatment. Note that each cluster has different numbers of peers taking the treatment; this is in contrast with the effects defined by Hudgens and Halloran [27] where because the treatment policies are fixed, there are (two) fixed number of people taking the treatment. Also, while individual i is a complier, his peers may be a mixture of compliers, always-takers, and CO never-takers. In the PSDP, we expect that TE (1, k1; 0, k0) > 0, that is the deworming treatment has a net positive benefit to complier students who take the assigned medication. Also, we define the population average spillover effect of treatment on the outcome among always-takers (AT)

J nj AT 1 X X (3) PE (1, k ; 1, k ) = PE (1, k ; 1, k )I(ji is AT) 1 0 N AT ji 1j 0j j=1 i=1

Equation (3) implicitly assumes that there is at least one always-taker in the population so that N AT 6= 0. Each individual spillover effect in equation (3), i.e. PEji(1, k1j; 1, k0j)I(ji is AT), is the spillover effect of always- taker i when when k1j versus k0j of always-taker i’s peers in cluster j take SPILLOVER EFFECTS WITH NONCOMPLIANCE 11 the treatment while he takes the treatment. Note that similar to equation (2), always-takers’ peers may be a mixture of compliers, never-takers, and AT always-takers. If PE (1, k1; 1, k0) = 0, having additional always-takers’ peers take the treatment does not affect, on average, the always-takers’ out- AT comes. When PE (1, k1; 1, k0) > 0, having additional always-takers’ peers take the treatment benefits the always-takers’ outcomes. In the PSDP, we AT expect PE (1, k1; 1, k0) ≥ 0, that is more always-takers’ peers taking the deworming medication is not harmful to the always-taker students. AT Finally, we define a parallel effect to PE (1, k1; 1, k0), the population average spillover effect among never-takers.

J nj NT 1 X X (4) PE (0, k ; 0, k ) = PE (0, k ; 0, k )I(ji is NT) 1 0 N NT ji 1j 0j j=1 i=1

Equation (4) implicitly assumes that there is at least one never-taker in the population so that N NT 6= 0. Each individual spillover effect in equation (4), i.e. PEji(0, k1j; 0, k0j)I(ji is NT), is the spillover effect of never-taker i when k1j versus k0j of never-taker i’s peers in cluster j take the treatment while never-taker i does not take the treatment. Like the spillover effect NT among always-takers in equation (3), PE (0, k1; 0, k0) can be thought of as the additional effect on never-takers when more of their peers take the treatment. In the PSDP, the spillover effect among never-takers is likely non- NT negative, i.e. PE (0, k1; 0, k0) ≥ 0, since peers of never-takers who take the deworming treatment reduce the likelihood of infections to everyone, including the never-takers who refuse to take the medication. The spillover effect among never-takers may be a practically useful estimand because it helps investigators understand how the treatment spills over to individuals who will never take the treatment irrespective of the intervention assignment. For example, in the PSDP, the never-takers students could be students who cannot take the new medication due to side effects or students who are immunocompromised. In vaccine studies, understanding how the peers of never-takers taking the treatment affect the never-takers’ outcomes could be useful for informing vaccination policies, say by understanding the effect of herd immunity of vaccines among individuals who refuse (or medically cannot) to take the vaccine. This is in contrast to the usual local estimands in noncompliance, such as the CACE where its significance and merit are debated [16, 30, 31,7, 55].

3.2. Standard IV Analysis Does Not Identify CACE. The first identification result we prove is that the standard IV estimator based on a ratio 12 KANG AND KEELE of the ITT effects as described in Section 2.4 does not identify the CACE when interference is present.

Theorem 1. Suppose assumptions (A1)-(A5) hold and suppose there is at least one complier in cluster j. Then, the ratio of τY to τD, τ, is a mixture of causal eﬀects among compliers, always-takers and never-takers.

(5) AT NT CO N AT N NT τ = TE (1, k − 1; 0, k ) + · PE (1, k − 1; 1, k − 1) + · PE (0, k ; 0, k ) 1 0 N CO 1 0 N CO 1 0

AT CO AT CO AT AT where k1 = (n1 + n1 , . . . , nJ + nJ ) and k0 = (n1 , . . . , nJ )

Theorem1 highlights that when both noncompliance and interference are present in a CRT, the standard Wald estimator must be interpreted as a mixture of treatment effects from different subgroups. Each effect in the mixture is associated with a particular subgroup, such as the spillover effects being associated with always-takers or never-takers instead of compliers. This is because, by definition, spillover effects fix individuals’ own treatment assignments, but vary the peers’ treatment assignments. Hence, to observe spillover effects under noncompliance, individuals must always take the treatment (or control) irrespective of the intervention assignment and only always-takers and never-takers have this trait. In contrast, the definition of total effects vary individuals and their peers’ treatment assignments. To observe total effects under noncompliance, individuals must comply with their treatment assignments so that there is variation in their treatment receipts and only compliers have this trait. Intuitively, the result in Theorem1 is based on the fact that under interference, the noncompliers’ potential outcomes, i.e. the never-takers and the always-takers’ outcomes, are affected by the behavior of their complier peers. For example, for never-takers in cluster j, if their cluster j is assigned CO AT treatment, there are nj + nj peers of never-takers taking the treatment AT and if their cluster j is assigned control, there are nj peers of them taking the treatment. The never-takers potential outcomes under these two randomization arms are different because more peers are taking the treatment when the cluster is randomized to treatment than control. Consequently, the difference in their potential outcomes between treatment and control is NT non-zero and remain as spillover effects PE (0, k1; 0, k0) in the expression for τ. In contrast, without interference, the never-takers’ potential outcomes do not depend on their peers’ treatment receipt. Therefore, their outcomes when the cluster is assigned treatment or control is always the outcome SPILLOVER EFFECTS WITH NONCOMPLIANCE 13 when they themselves do not take the treatment. This means that the difference in the two potential outcomes will be zero and the never-takers’ treatment effects do not appear in τ of Theorem1. A formal argument is in the Appendix, where we also prove Theorem1 with and without stratified interference (A5). We also take a moment to relate our results to those in the literature on interference and noncompliance. First, a key difference between the population effects in Theorem1 and those in Hudgens and Halloran [27] is that Hudgens and Halloran [27] studied contrasts between two fixed treatment policies applied to clusters, say treatment policy 1 that randomly assigns 50% of individuals in a cluster to treatment, and treatment policy 2 that randomly assigns 30% of individuals in a cluster to treatment. Additionally, their population average effects averaged over all individuals in the study. In our setting, because of noncompliance, each cluster may have different numbers of people who (non-randomly) take the treatment and thus, the number of individuals actually taking the treatment varies across clusters. Also, CO AT our population average effects TE (1, k1 −1; 0, k0), PE (0, k1; 0, k0), and NT PE (0, k1; 0, k0) are averaged over subgroups in the population. Our population average effects become those in Hudgens and Halloran [27] if everyone in the study is a complier; under this case, our population average effects would become contrasts between two treatment policies, one where everyone in a cluster is treated and one where everyone is not treated, and τ reduces to the population average total effect of Hudgens and Halloran [27]. Sec- ond, Theorem1 can be seen as a generalization of the classical identification results of CACE [32,4] that allows for interference. In particular, without interference, the spillover effects in τ equal zero, the total effect is the direct effect [27] and τ in Theorem1 reduces to the CACE. Finally, the peers’ “observable” values of Y in a CRT with interference do NT not involve the never-takers nj when stratified interference (A5) holds. In CO fact, the number of compliers nj is a key quantity in the spillover effects in Theorem1, as having zero compliers would lead to zero spillover effects. This is similar in spirit to the non-interference case in a CRT where the compliers play a pivotal role in defining the effect of the treatment receipt [4]. Under interference, the compliers also drive the effect of the treatment receipt by being influencers among their peers and changing the number of compliers may enlarge the contrasts k1j and k0j in the estimands under a AT CRT. In contrast, the number of always-takers nj provide a “baseline” for the contrast in the spillover or the total effects and changing it does not change the said contrasts. Corollary1 states the form of τ under one-sided noncompliance in as- 14 KANG AND KEELE sumption (A4.1).

Corollary 1. Suppose the assumptions in Theorem1 hold except we replace (A4) with (A4.1). Then, τ becomes

NT CO N NT τ = TE (1, k − 1; 0, k ) + · PE (0, k ; 0, k )(6) 1 0 N CO 1 0

CO CO where k1 = (n1 , . . . , nJ ) and k0 = 0.

We end the section by briefly discussing the relationship between instrument strength and our identification result. Broadly speaking, an instrument is strong when there are more compliers than non-compliers so that NT CO AT CO N /N ≈ 0, N /N ≈ 0 and τD is far away from 0. When the instrument is strong, τ in Theorem1 mainly consists of compliers, specifically their total effects. However, if the instrument is weak and there are more never- takers or always-takers than compliers (i.e. N NT/N CO or N AT/N CO are far away from zero), τ predominantly represents the always-takers or never- takers in the population, and the effects among compliers may make up a small portion of τ. However, this general observation won’t hold when each subgroup has non-comparable magnitudes of treatment effects, such as if the compliers have substantially larger treatment effects than non-compliers.

3.3. Unbiased Estimation of Network Effects is Generally Impossible. Thus far, we proved that the standard IV estimate is a mixture of network treatment effects. Next, we address whether any analysis with the observed data, not just the IV analysis in the prior section, can be informative about these network treatment effects. Formally, consider again the estimands defined in Section 3.1, the total effect among compliers and the spillover effects among always-takers and never-takers. Unbiased estimators exist for the denominators of these quantities, which are the number of compliers, always-takers, and never-takers; see Section4 for details. Hence, to learn more about total and spillover treatment effects from data, we need to be able to estimate the numerator of these quantities, which are the sums of individual total and spillover SPILLOVER EFFECTS WITH NONCOMPLIANCE 15 effects among their respective subgroups.

(7) J nj CO X X AT CO AT TEsum(1, k1 − 1; 0, k0) = TEji(1, nj + nj − 1; 0, nj )I(ji is CO) j=1 i=1 (8) J nj AT X X AT CO AT PEsum(1, k1 − 1; 1, k0 − 1) = PEji(1, nj + nj − 1; 1, nj − 1)I(ji is AT) j=1 i=1 (9) J nj NT X X AT CO AT PEsum(0, k1; 0, k0) = PEji(0, nj + nj ; 0, nj )I(ji is NT) j=1 i=1

AT CO AT CO AT AT Here, we denote k1 = (n1 +n1 , . . . , nJ +nJ ) and k0 = (n1 , . . . , nJ ). We focus on these speciﬁc forms of k1 and k0 because for a given study, they are the only ones that can be observed. Theorem2 shows that no unbiased estimators exist for these sums in CRTs with noncompliance and interference.

Theorem 2. Suppose the assumptions in Theorem1 or Corollary1 hold. Then, there does not exist unbiased estimators for sums in equations (7)-(9) from the observed data Y, D, and Z.

Broadly speaking, the result of Theorem2 comes from the fact that for an unbiased estimator T to exist for the three local estimands, the unbiased estimator must be able to classify all individuals into the three compliance types only based on the observed data. But, this is impossible, since it re- (1) (0) quires observing both potential outcomes Dji and Dji . In contrast, without interference, the unbiased estimator for the CACE does not need to classify individuals, since we are only able to estimate the compliers’ effect; specifically, without interference, only the compliers’ effect remains in the ITT effect [4]. The proof of Theorem2 states this more precisely, stating that an unbiased estimator, if it were to exist, must be able to differentiate individuals between different compliance types from the observed data, which is not possible with all values of the parameter space. We remark that a variation of Theorem 1 in Basse and Airoldi [9] can also be used prove our Theorem 2. As a negative result, Theorem2 highlights that traditional CRTs have fundamental limitations as experimental designs to elucidate network causal 16 KANG AND KEELE effects under noncompliance and interference and a need for either alternative experimental designs or stronger structural assumptions. The result is similar in spirit to negative results in Manski [40],Shalizi and Thomas [52], Manski [41], and Basse and Airoldi [9] in that additional assumptions are needed to estimate effects under noncompliance and interference. Indeed, even with stratified interference (A5), which can be argued as a strong assumption primarily to estimate variances of estimators, we are unable to identify the sums of the total or spillover effects. We remark that our result differs from classic results in the IV literature that states that moments do not exist for ratio estimators since our focus in Theorem2 is on the numerator; see Lemma 5 of Nelson and Startz [44] and references therein. Finally, while Theorem2 proves that total and spillover effects are generally impossible to unbiasedly estimate under assumptions (A1)-(A5), they do not rule of local conditions that allow unbiased estimation. For exam- CO ple, if all the subjects are compliers, then we can estimate TE (1; 0) from data by using the standard IV method since the terms that are associated with non-compliers and that make up τ in Theorem1 go away. Similarly, under one-sided noncompliance, when all subjects are never-takers, we can NT estimate PE (0) by using the standard IV method. These are two spe- cific, local data generating scenarios that allow identification. However, in practice, such scenarios are rare.

3.4. Nonparametric Bounds under the Assumption of Non-Negative Treat- ment Effects. The results in Sections 3.2 and 3.3 imply analyzing a CRT with noncompliance and interference for network treatment effects is hope- less and one should focus on ITT effects. This pessimism is not entirely warranted and we show that in such CRTs with one-sided noncompliance, we can use one additional assumption to calculate informative bounds on the total effect among compliers and the spillover effect among never-takers. The assumption we invoke is one of non-negative treatment effects. For- mally, a treatment is not harmful, or has non-negative total and spillover effects, if the following hold.

(A6) Non-Negative Treatment Eﬀects. For any 0 ≤ k0 < k1 ≤ nj − 1 and individual i in cluster j, we have

(10) 0 ≤ TEji(1, k1; 0, k0), 0 ≤ PEji(0, k1; 0, k0) We note that assumption (A6) is similar to an assumption used by Choi [13] about treatment monotonicity. In the PSDP, assumption (A6) is reasonable because it is unlikely that exposure to deworming treatments would increase the presence of infection. SPILLOVER EFFECTS WITH NONCOMPLIANCE 17

CO NT Let y = TE (1, k1; 0, k0) and x = PE (0, k1; 0, k0). Then, under one- sided compliance, we can write τ in equation (6) as

N NT (11) y = τ − x N CO Equation (11) suggests an inverse relationship between the total average effect among compliers and the spillover average effect among never-takers. Specifically, as the spillover average effect becomes positive, the total average effect must become negative. Moreover, under (A6), 0 ≤ y and 0 ≤ x, which, along with equation (11), gives us bounds on both the total and the spillover effect. CO CO NT N (12) 0 ≤ TE (1, k ; 0, k ) ≤ τ, 0 ≤ PE (0, k ; 0, k ) ≤ τ 1 0 1 0 N NT The boundaries of the bounds in equation (12) are achieved when either CO effect is at the extreme. For example, TE (1, k1; 0, k0) reaches its lower NT N CO NT bound of 0 if PE (0, k1; 0, k0) = τ N NT and PE (0, k1; 0, k0) reaches its CO lower bound of 0 if TE (1, k1; 0, k0) = τ. If the outcome is binary, we can impose tighter constraints on both equations (11) and (12)

N NT (13) y = τ − x, 0 ≤ y ≤ 1, 0 ≤ x ≤ 1 N CO which leads to NT N CO max 0, τ − ≤ TE (1, k ; 0, k ) ≤ min(1, τ)(14) N CO 1 0 CO CO N NT N (15) max 0, (τ − 1) ≤ PE (0, k ; 0, k ) ≤ min 1, τ N NT 1 0 N NT

In equation (15), if the number of compliers exceeds the number of never- takers, this tightens the lower bound for the total effect. However, if the number of never-takers increases and exceeds the number of compliers, we have a tighter upper bound for the spillover effect. This is consistent with Theorem1 where τ is a weighted mixture of subgroup effects and the weights are proportional to the number of individuals in each subgroup. Figure1 summarizes the characteristics of the bounds in equations (14) and (15) by plotting the range of spillover and total effects as a function of the proportion of compliers N CO/N and τ. For example, when τ = 0.75, as the number of compliers increase, the plausible range of the total effect 18 KANG AND KEELE

Tau = 0.75 Tau = 1.25 1.0 1.0

75% CO 0.8 0.8 0.6 0.6

75% CO 50% CO 0.4 0.4 Total Total Effect Compliers Among Total Effect Compliers Among 0.2 0.2

25% CO 50% CO 25% CO 0.0 0.0

0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.2 0.4 0.6 0.8 1.0 Spillover Effect Among Never-Takers Spillover Effect Among Never-Takers

Fig 1. A Numerical Example of Bounding Total Effect Among Compliers and Spillover Effect Among Never-Takers in a One-Sided Noncompliance CRT with Binary Outcomes. among compliers decreases. However, as the number of compliers decrease, τ becomes more representative of the never-takers and hence, the range of plausible values for the spillover effect is shorter and range of plausible values for the total effect is wider. Note that the upper bound on the total effect is 0.75 and it has a non-trivial (i.e. non-zero) lower-bounded if the compliance rate is high. When τ = 1.25, the spillover effect among never-takers is always bounded away from zero; more generally, if τ > 1, the lower bound on the spillover effect is always bounded away from zero. The upper bound depends on the compliance rate. For example, if the compliance rate is high, say 75%, there are tight bounds for both the spillover and the total effect. However, if the compliance rate is 50%, both the spillover and total effect have wide bounds, although neither include zero. Finally, if the compliance rate is 25%, the bound on the total effect is not informative, i.e. it ranges from 0 to 1, but the bound on the spillover effect becomes narrower. As a general rule of thumb for binary Y , the numerical example suggests that for CRTs with one-sided noncompliance where assumption (A6) is plausible, informative analysis is possible for spillover and total treatment effects. Specifically, with τ > 1 and a high compliance rate, we can obtain tight bounds on both the total and spillover effects. If τ > 1 and the com- SPILLOVER EFFECTS WITH NONCOMPLIANCE 19 pliance rate is low, then we can obtain tight bounds on the spillover effect, but not the total effect. If τ < 1 and the compliance rate is high, then we can also obtain tight bounds on the total effect, but not the spillover effect. If τ < 1 and the compliance rate is low, then we can only obtain tight upper bounds on both the total and spillover effects.

4. Estimation and Inference of Bounds.

4.1. Estimation. We now outline how to estimate the bounds in Sec- tion 3.4 when the outcome is binary as it is in the PSDP. Generally, estimation of the three key values that make up the bounds, τ, N CO, and N NT, directly follow from literature on IV estimation. To estimate τ, we can use the ratio of the estimated ITT effect with the estimated compliance effect, i.e.   J nj J nj J nj 1 X J X X J X 1 X J X τ = Z Y − (1 − Z ) Y , τ = Z D bY N  m j ji J − m j ji bD N m j ji j=1 i=1 j=1 i=1 j=1 i=1 τbY τb = τbD As mentioned earlier, τbD is also an estimator of the compliance rate or the proportion of compliers and it ranges between 0 and 1. Kang and Keele [37] prove that this version of the ratio estimatorτ ˆ is superior in terms of its finite sample properties compared to other IV methods for CRTs; see Kang and Keele [37] for details. To estimate the subgroup sizes, N CO and N NT, we use the following estimators

J nj CO X J X NT CO Nb = Zj Dji, Nb = N − Nb m j=1 i=1

Under assumptions (A1), these estimators are unbiased for N CO and N NT. CO N NT CO NT N CO Let LTE = max 0, τ − N CO ,UTE = min(1, τ), LPE = max 0, N NT (τ − 1) , NT N CO and UPE = min 1, τ N NT be the lower and upper bounds of the total and NT spillover effects in equations (14) and (15). Let LbCO = max 0, τ − Nb , UbCO = TE b NbCO TE CO CO min(1, τ), LbNT = max 0, Nb (τ − 1) , and UbNT = min 1, τ Nb be the b PE NbNT b PE bNbNT plug-in estimates for these bounds. The following theorem shows that these plug-in estimators are consistent estimators under the asymptotic regime where the cluster size remains fixed while the number of clusters go to infinity. 20 KANG AND KEELE

Theorem 3. Suppose assumptions (A1)-(A4.1) and (A5)-(A6) hold and we have binary outcomes. Consider the asymptotic regime where the number of clusters go to inﬁnity while the cluster size remains bounded, i.e. J, J − m → ∞ where (i) m/J → p ∈ (0, 1), (ii) nj ≤ B for some constant B, (iii) τD and τY are ﬁxed for all J. Then,

Conditions (i) and (ii) in Theorem3 are standard asymptotic regimes for CRTs where the number of clusters go to infinity while the cluster size remains fixed; Kang and Keele [37] shows that in the opposite asymptotic regime where the number of clusters remain fixed, but the cluster size goes to infinity, typical CRT estimators exhibit poor properties. Condition (iii) follows Chapter 4.4 of Lehmann [38] where in finite sample settings, the asymptotic embedding sequence has the same mean for every N; this type of asymptotics has been used in noncompliance settings [8]. Condition (iii) can be generalized to a condition where τY and τD converge as sample size increases; in this case, τD must be bounded strictly away from 0 and 1. We will use Theorem3 as a basis for constructing bounds in our empirical example in Section5.

4.2. Simultaneous Confidence Interval for Bounds. While Theorem3 provides a consistent estimator for the bounds, it does not characterize uncertainty. Indeed, the presence of min or max operators in the bounds makes it difficult to derive a closed form expression for the asymptotic distribution of bounds and bootstrap techniques have been proven to be generally invalid in this context[46,2, 47, 48,3, 23]; see Tamer [56] for a general overview. One solution is to assume an infinite population model with independent and identically distributed (IID) observables. Under an IID infinite population model, Cheng and Small [11] used the percentile bootstrap method of Horowitz and Manski [26] to construct confidence intervals for bounds in an IV setting. However, in our application, the assumption of an IID infinite population model is unrealistic given the clustered treatment assignment and interference. One alternative would be to use the methods in Chernozhukov, Lee and Rosen [12]. They developed methods for asymptotically bias-corrected estimators and confidence intervals for intersection bounds under more general sampling mechanisms. The Chernozhukov-Lee-Rosen (CLR) approach uses precision-corrected estimates of the terms in the bounding functions before SPILLOVER EFFECTS WITH NONCOMPLIANCE 21 applying the min and max operators. However, using the CLR approach requires a non-trivial coupling argument between our plug-in estimators for bounds and a suitably simple and uniformly concentrating Gaussian process to conduct inference, and is difficult to verify. Instead, we propose a finite-sample randomization inference method to test the joint hypothesis for the bounds, denoted as y and the spillover effect, denoted as x, and to invert this test to obtain simultaneous confidence intervals for both sets of bounds. Formally, consider testing the joint hypothesis

(16) H0 : x = x0, y = y0

From Corollary1, the null hypothesis H0 in (16) implies the following hypothesis about τ pNT (17) H0 : τ = τ , τ = y + x 0 x0,y0 x0,y0 0 pCO 0 where pCO = N CO/N = pCO ∈ (0, 1) and pNT = N NT/N = pNT ∈ (0, 1) are the population proportion of complier and never-takers, respectively. If pNT and pCO are known, Kang and Keele [37] provided a method to 0 test H0 by using the diﬀerence in adjusted outcomes. Speciﬁcally, for each Pnj Pj cluster j, let Yj = i=1 Yji and Dj = i=1 Dji be the sums of Y and

D respectively. Also, let Aj(τx0,y0 ) = Yj − τx0,y0 Dj be the adjusted out- PJ come of Yj by Dj and let AT = j=1 ZjAj(τx0,y0 )/m, and AC (τx0,y0 ) = PJ j=1(1 − Zj)Aj(τx0,y0 )/(J − m) be the means of these adjusted outcomes for the treated and control clusters, respectively. Then, Kang and Keele [37] 0 proposed the following test statistic for H0

AT (τx0,y0 ) − AC (τx0,y0 ) (18) T (τx0,y0 ) = p Var [AT (τx0,y0 ) − AC (τx0,y0 ) | F, Z] for some suitable estimator of the variance. For instance, a popular estimator for the variance is J 1 X 2 Vard [AT (τx ,y ) − AC (τx ,y ) | F, Z] = Zj {Aj(τx ,y ) − AT (τx ,y )} 0 0 0 0 m(m − 1) 0 0 0 0 j=1 J 1 X + (1 − Z ) {A (τ ) − A (τ )}2 (J − m)(J − m − 1) j j x0,y0 C x0,y0 j=1

If pNT and pCO are unknown, we can plug-in consistent estimators of them, NT NT CO CO say pb = Nb /N and pb = Nb /N, respectively, from Theorem3 and 22 KANG AND KEELE use τ = y + pNT/pCOx in lieu of τ . The following Theorem shows bx0,y0 0 b b 0 x0,y0 that with a plug-in estimate, the test statistic T (τ ) is asymptotically bx0,y0 pivotal under H0.

Theorem 4. Consider the assumptions in Theorem3 and suppose H0 holds. As J grows, consider a sequence of F where τY and τD are constants so that τ /τ = y + pNT/pCOx is a constant, the test statistic T (τ ) is Y D 0 0 bx0,y0 asymptotically pivotal and Normally distributed, i.e.

T (τ ) → N(0, 1) bx0,y0 in distribution.

Theorem3 provides a basis to obtain 1 −α simultaneous confidence intervals for x and y which represent the total and spillover effects. Specifically, for any α ∈ (0, 1), the 1 − α confidence set C1−α of the two effects is the set of values of x and y where

C1−α = {(x0, y0) | 0 ≤ x0 ≤ 1, 0 ≤ y0 ≤ 1, |T (ˆτx0,y0 )| ≤ z1−α/2}

Here, z1−α.2 is the 1 − α/2 quantile of the standard Normal. By the duality of testing and confidence interval, this confidence set covers a fixed true value of x and y with at least 1 − α probability; see Imbens and Manski [33] for discussion on interpreting confidence intervals for bounds. Additionally, while a grid search over x0 to y0 to find C1−α is feasible since the outcome is 0 binary, Kang and Keele [37] shows that the confidence interval for τ in H0 can be efficiently solved using a quadratic equation. Consequently, since τ is a linear w.r.t. x0 and y0, the joint confidence interval for x0 and y0 is also a solution to a quadratic equation and C1−α can be efficiently solved. This computational advantage is in contrast to many inferential methods under the partial identification literature [47, 48, 12] where expensive computation is needed. A downside of the proposed approach is that the interval may be con- servative. In particular, if the true value of x and y satisfy the equation NT CO NT CO y + p /p x = y0 + p /p x0, then the test T (τx0,y0 ) will have no power 0 to reject H0, leading to potentially large confidence regions. Nevertheless, the confidence set C1−α will still have Type I error control.

5. Application: The Effect of Deworming in the Presence of Noncompliance and Spillovers. This section revisits the statistical analysis of the PSDP intervention under the new paradigm where we allow for SPILLOVER EFFECTS WITH NONCOMPLIANCE 23 interference and noncompliance. The initial analysis of the PSDP intervention focused on estimating ITT effects, specifically the direct effect of the deworming intervention and the treatment spillover effects [42]; the original analysis did not include any analyses that focused on complier effects. The original data did, however, include detailed measures of whether students complied with cluster-level treatment assignment. In our analysis, we use an updated version of the data that corrected a series of data errors in the original data [1, 22]. We focus on the primary outcome from the original study, which was a binary indicator for the presence of a helminth infection with 1 denoting infection and 0 otherwise. We note that in this example, taking the treatment (new deworming intervention) leads to a decrease in outcome (i.e. infection) and hence, our effect estimates are negative. Also, we remind readers that the PSDP intervention had one-sided noncompliance where individuals in control clusters could not seek out the new medication. First, we carry out the standard IV analysis, which is what an investigator may naively try with CRT data with noncompliance, falsely assuming that effects from treatment spillovers are mitigated due to clustered treatment assignment. Using the methods in Kang and Keele [37] to estimate τ, the estimate of τ is −0.79 with a 95% confidence interval of −1 and −0.51. While τ is easily estimable using existing IV methods, this estimate of τ is no longer the effect for compliers alone, but also includes effects among never-takers. Next, we focus on estimating the bounds for both the total effect among CO NT compliers, TE (1; 0), and the spillover effect among never-takers, PE (0). We can plug in estimates of Nb NT, Nb CO, andτ ˆ into equation (12) to estimate the bounds. In the PDSP intervention, the instrument is fairly strong: average student compliance in schools assigned to treatment was 60%. As such, the number of compliers is higher compared to the number of never-takers, which indicates we should be able to obtain relatively informative bounds CO NT on TE (1; 0), but not on PE (0; 0). Indeed, when we plug in estimates for our bounds, we obtain estimates of −0.79 and −0.12 for the total effect among compliers and 0 and 1 for the spillover effect among never-takers. Note that by construction, the lower bound is equivalent to the estimate for τ. Next, we computed the 95% confidence interval for the total effect and the spillover effect using the proposed method. The confidence intervals are −1 and 0; in words, once the uncertainty of the bound estimates are taken into considering, the bounds for the total and spillover effects span the en- tire parameter space. We also estimated the confidence intervals using the bootstrap and the methods outlined in Chernozhukov, Lee and Rosen [12]. Both methods returned a confidence region of -1 and 0. 24 KANG AND KEELE

● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● 0.00 ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● −0.25 ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● −0.50 ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● Total Effect Among Compliers Effect Total ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● −0.75 ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● −1.00 ● ● ● ● ● ● ● ● ● ● ● ● ● ● ●

−1.00 −0.75 −0.50 −0.25 0.00 Spillover Effect Among Never−Takers

Fig 2. 95% Simultaneous Confidence Intervals for the Total Effect Among Compliers and the Spillover Effect Among Never-Takers of the New Deworming Treatment. Here, taking the treatment (i.e. new deworming medication) will lead to a smaller outcome (i.e. the presence of helminth infections) and hence, our effect estimates are negative in sign. Each point inside the shaded area represents plausible values of the total and spillover effect after taking into account the uncertainty in estimating the bounds.

Figure2 graphically represents the results of the bounds from the study. Each point inside the shaded area represents plausible values of the total and spillover effect after taking into account the uncertainty in estimating the bounds. From the plot, we see that certain combinations of total effect and spillover effect values are improbable. For example, based on this study with the given sample size, it’s unlikely that the deworming treatment led to 75% reduction in helminth infections among both compliers and never-takers, as measured by the total effect among compliers and the spillover effect among never-takers. Similarly, it’s unlikely deworming treatment lead to only 25% reduction in helminth infections among both compliers and never-takers. SPILLOVER EFFECTS WITH NONCOMPLIANCE 25

6. Conclusion. In this paper, we studied CRTs with both noncompliance and treatment spillovers. In many public health interventions, subjects may refuse treatments but are partially exposed when other subjects take the treatment. In the PSDP, some students did not take the medications that comprised the treatment. However, infection levels may be lower for these unexposed students as peers who took the treatment lowered their likelihood of environmental exposure to helminths. We showed that standard causal estimands of interest cannot be estimated under the usual assumptions used with noncompliance and interference. The standard IV analysis leads to a mixture of causal effects instead of the usual complier average causal effect. We extended the result to show that unbiased estimation of key components of the causal estimands in Sec- tion 3.1 is impossible. Finally, we showed that investigators must rely on partial identification methods to place bounds on these quantities. While partial identification results often produce wide bounds that are uninforma- tive, we showed that in the PSDP data and in Figure2, the bounds can be informative even once sampling uncertainty is accounted for.

APPENDIX A: PROOFS OF KEY THEOREMS (1) (1) (1,Dji ,Dj−i) Proof of Theorem1. We start by decomposing the term Yji − (0) (0) (0,Dji ,Dj−i) Yji in τY . Under network exclusion restriction (A3) and monotonicity (A4), we have

(1) (1) (0) (0) (1,Dji ,Dj−i) (0,Dji ,Dj−i) Yji − Yji (1) (1) (0) (0) (Dji ,Dj−i) (Dji ,Dj−i) =Yji − Yji (1) (0) (1) (0) (1) (0) (1,Dj−i) (1,Dj−i) (0,Dj−i) (0,Dj−i) (1,Dj−i) (0,Dj−i) = Yji − Yji I(ji is AT) + Yji − Yji I(ji is NT) + Yji − Yji I(ji is CO)

(1) (0) (1) (0) (1) (0) =PEji(1, Dj−i; 1, Dj−i)I(ji is AT) + PEji(0, Dj−i; 0, Dj−i)I(ji is NT) + TEji(1, Dj−i; 0, Dj−i)I(ji is CO) where

(1) (0) (1) (0) (dji,Dj−i) (dji,Dj−i) PEji(dji, Dj−i; dji, Dj−i) = Yji − Yji (1) (0) (1) (0) (1,Dj−i) (0,Dj−i) TEji(1, Dj−i; 0, Dj−i) = Yji − Yji

(1) (0) Notice that so long as the vectors Dj−i−Dj−i 6= 0, we can guarantee that the spillover eﬀects for ATs and NTs do not disappear. This occurs when there 0 (1) (0) is at least one CO in cluster j, say individual i , because Dji0 − Dji0 = 1. 26 KANG AND KEELE

Then, summing these quantities over all clusters give you the sum of total effects and spillover effects for different subgroups CO, AT, and NT, all without (A5).

(1) (0) (1) (0) With (A5), PEji(dji, Dj−i; dji, Dj−i) and TEji(1, Dj−i; 0, Dj−i) simplify to (z) the sum of the vectors Dj−i for diﬀerent z ∈ {0, 1}. In particular, the sum (1) P (1) of the vector Dj−i, i.e. i06=i Dji0 , is the number of compliers and always- takers in cluster j, minus 1 if i is either a complier or an always-taker or (0) P (0) 0 otherwise. The sum of the vector Dj−i, i.e. i06=i Dji0 , is the number of always-takers in cluster j minus 1 if i is an always-taker or 0 otherwise.

In both cases, dividing this quantity τD, which constitutes the total number of compliers in the population and is non-zero because of (A2), gives the desired result. A similar argument can be used to prove the decompo- sition under one-sided noncompliance where we remove ATs in the above expression.

(z) (z) (Dji ,Dj−i) (z) Proof of Theorem2. Let F = {Yji ,Dji | j = 1, . . . , J, i = 1, . . . , nj, z ∈ {0, 1}} be the parameter set satisfying (A2)-(A4). By knowing F, we can fully characterize the distribution of the observed data Yji,Dji and Zj. An unbiased estimator S(Y, D, Z) of an estimand θ(F), say the sum of individual total effect among compliers, satisfies (19) θ(F) = E[T (Y, D, Z) | F, Z] for all parameter values. We show that for the estimands in Theorem2, such a function T does not exist. CO First, we work with TEsum(1, k1 − 1; 0, k0; F), where we add the argument F for clarity. Without loss of generality, let the first cluster j = 1 contain at least two individuals. Suppose by contradiction, there is an un- CO biased estimator T (Y, D, Z) for TEsum(1, k1 − 1; 0, k0; F) and consider two parameter sets, F and F 0. Parameter set F has at least one always-taker, say i = 1, and one complier, say i = 2, in cluster j = 1. Parameter F 0 flips the always-taker i = 1 in F to a complier and the complier i = 2 in F to an always-taker. The rest remains identical between the two parameters F and F 0, in particular the number of always-takers and compliers. Then, the difference between the two estimands under two parameters F, F 0 is CO 0 CO TEsum(1, k1 − 1; 0, k0; F ) − TEsum(1, k1 − 1; 0, k0; F) AT CO AT AT CO AT (1,[nj +nj −1]) (0,[nj ]) (1,[nj +nj −1]) (0,[nj ]) = Y12 − Y12 − Y11 − Y11 SPILLOVER EFFECTS WITH NONCOMPLIANCE 27

Also, by the deﬁnition of expectations and assumption (A1), for any F, T (Y, D, Z) must obey

E[T (Y, D, Z) | F, Z] 1 X = T (Y, D, z) J m z∈Z   1 X X = T (Y, D, 1, z ) + T (Y, D, 0, z ) J  −1 −1  m z∈Z;z1=1 z∈Z;z1=0  (z ) (1) (1) (1) (D(1) ,D(1) ) (D J ,D ) 1 X (D11 ,D1−1) 1n1 1−n1 JnJ J−nJ (1) (1) (zJ ) = T (Y ,...,Y ,...,Y ,D ,...,D ,...,D , 1, z−1) J  11 1n1 JnJ 11 1n1 JnJ m z∈Z;z1=1  (0) (0) (0) (0) (zJ ) (zJ ) X (D ,D ) (D1n ,D1−n ) (DJn ,DJ−n ) (0) (0) (z ) + T (Y 11 1−1 ,...,Y 1 1 ,...,Y J J ,D ,...,D ,...,D J , 0, z ) 11 1n1 JnJ 11 1n1 JnJ −1  z∈Z;z1=0

Taking the difference between E[T (Y, D, Z) | F 0, Z] and E[T (Y, D, Z) | F, Z] leads to  1 X (1,[nAT+nCO−1]) (1,[nAT+nCO−1]) (1) (1) = T (Y j j ,Y j j ,...,D = 1,D = 1, . . . , z = 1, z ) J  11 12 11 12 1 −1 m z∈Z;z1=1  AT AT X (1,[nj −1]) (0,[nj ]) (0) (0) + T (Y11 ,Y12 ,...,D11 = 1,D12 = 0, . . . , z1 = 0, z−1) z∈Z;z1=0  1 X (1,[nAT+nCO−1]) (1,[nAT+nCO−1]) (1) (1) − T (Y j j ,Y j j ,...,D = 1,D = 1, . . . , z = 1, z ) J  11 12 11 12 1 −1 m z∈Z;z1=1  AT AT X (0,[nj ]) (1,[nj −1]) (0) (0) + T (Y11 ,Y12 ,...,D11 = 0,D12 = 1, . . . , z1 = 0, z−1) z∈Z;z1=0  1 X (1,[nAT−1]) (0,[nAT]) (0) (0) = T (Y j ,Y j ,...,D = 1,D = 0, . . . , z = 0, z ) J  11 12 11 12 1 −1 m z∈Z;z1=0 AT AT (0,[nj ]) (1,[nj −1]) (0) (0) −T (Y11 ,Y12 ,...,D11 = 0,D12 = 1, . . . , z1 = 0, z−1) where we suppress arguments to T that do not change. By our assumption about unbiasedness, the difference in expectation has to equal to the difference in the estimand between F 0 and F. However, the estimand’s difference 28 KANG AND KEELE

AT CO AT CO (1,[nj +nj −1]) (1,[nj +nj −1]) has the terms Y12 and Y11 whereas the expectation’s diﬀerence does not contain these terms, a contradiction, and no unbiased estimator T exists.

AT Second, for PEsum(1, k1 − 1; 1, k0 − 1; F), consider an unbiased estimator T (Y, D, Z) for it and the same two set of parameters F and F 0 above. Then, the diﬀerence between the estimands is

AT 0 AT PEsum(1, k1 − 1; 1, k0 − 1; F ) − PEsum(1, k1 − 1; 1, k0 − 1; F) AT CO AT AT CO AT (1,[nj +nj −1]) (1,[nj −1]) (1,[nj +nj −1]) (1,[nj −1]) = Y11 − Y11 − Y12 − Y12

The difference in the expectations E[T (Y, D, Z) | F 0, Z] and E[T (Y, D, Z) | F, Z] remains the same as before. But, like the total effect, the terms inside AT CO AT CO (1,[nj +nj −1]) (1,[nj +nj −1]) the difference in the estimands, Y12 and Y11 , do not appear in the difference of the expectations, leading to a contradiction.

NT Finally, for PEsum(0, k1; 0, k0; F), consider an unbiased estimator T (Y, D, Z) for it and the same two set of parameters F and F 0 above except we replace the always-takers as never-takers. Then, the diﬀerence between the estimands is

NT 0 NT PEsum(0, k1; 0, k0; F ) − PEsum(0, k1; 0, k0; F) AT CO AT AT CO AT (0,[nj +nj ]) (0,[nj ]) (0,[nj +nj ]) (0,[nj ]) = Y11 − Y11 − Y12 − Y12

The difference in the expectations E[T (Y, D, Z) | F 0, Z] and E[T (Y, D, Z) | F, Z] remains the same as before. Like the spillover effect, the terms inside AT CO AT CO (0,[nj +nj ]) (0,[nj +nj ]) the difference in the estimands, Y12 and Y11 , do not appear in the difference of the expectations, leading to a contradiction.

Proof of Theorem3. The proof proceeds in two steps. We ﬁrst show CO that the estimators τ and N are consistent. Second, we utilize the con- b N NT tinuous mapping theorem to show that the estimators for the bounds are consistent. First, under (A1), the numerators and denominators that make up τb, τbY (1,D(1),D(1) ) (1) Pnj ji j−i and τbD are unbiased for τY and τD, respectively. Let Yej. = i=1 Yji SPILLOVER EFFECTS WITH NONCOMPLIANCE 29

(0,D(0),D(0) ) (0) Pnj ji j−i and Yej. = i=1 Yji . Then, the variances of τbY and τbD are

 J (1) (0) !  J X Yej. Yej. V ar [τ | F, Z] = V ar Z + | F, Z bY N j m J − m  j=1  2 2 J (1) (0) ! J (1) (0) ! J m(J − m) X Yej. Yej. 1 X Yej. Yej. = · + − + N 2 J(J − 1)  m J − m J m J − m  j=1 j=1 2 2 J (1) (0) ! J m(J − m) X Yej. Yej. ≤ · + N 2 J(J − 1) m J − m j=1 2 PJ 2 2 m(J − m) J j=1 nj ≤ J · · · 2 J(J − 1) m2(J − m)2 PJ j=1 nj J 3 JB2 ≤ · (J − 1)(m)(J − m) J 2 where the second inequality uses the boundedness of the outcome to bound (1) (0) Yej. , Yej. ≤ nj. As J, J − m → ∞, the upper bound on the variance goes to zero and we have consistency of τbY . A similar argument can be used to also prove that V ar [τbD | F, Z] → 0. Combining the two consistent estimators via Slutsky’s theorem yields τ = τY /τD → τY /τD = τ. b b b CO NbCO p Next, we show that the ratio is consistent for the ratio NT . We see NbNT p that

CO 1 PJ J Pnj 1 PJ J CO Nb N j=1 m Zj i=1 Dji N j=1 m Zjnj = = NT 1 PJ J Pnj 1 PJ J CO Nb 1 − N j=1 m Zj i=1 Dji 1 − N j=1 m Zjnj Notice that the expectation for the numerator and the denominators are unbiased estimators of the proportions pCO and pNT.

 J  1 X J N CO E Z nCO | F, Z = = pCO N m j j  N j=1

 J  1 X J N CO E 1 − Z nCO | F, Z = 1 − = pNT  N m j j  N j=1 30 KANG AND KEELE

Also, the variances of both the numerator and the denominator go to zero:

2  J  J  J  1 X J J 2 J − m X 1 X V ar Z nCO | F, Z = · · nCO − nCO N m j j  mN 2 J(J − 1)  j J j  j=1 j=1 j=1 2 PJ CO J(J − m) j=1 nj ≤ · 2 m(J − 1) PJ j=1 nj J(J − m) JB2 ≤ · → 0 m(J − 1) J 2

Consequently, we have Nb CO pCO → NT Nb NT p Finally, for any ﬁxed constants c0, c1, consider the two functions f(x) = min(x, c0) for some c and g(x) = max(x, c1). These are continuous functions of x and our bounds are of this type, we can use the continuous mapping theorem to arrive at the desired consistency for the bound estimators.

Proof of Theorem4. The proof is a direct consequence of Proposition 0 4 of Kang and Keele [37]. Specifically, H0 implies H0 : τ = τx0,y0 which is the setting in Proposition 4. Also, condition (i) in Proposition 4 of Kang and Keele [37] is satisfied because µY and µD = pCO remain fixed in such NT CO a way that µY /µD = y0 + p /p x0 = τx0,y0 remains fixed; note that pNT = 1 − pCO. Condition (ii) in Proposition 4 of Kang and Keele [37] is satisfied because the outcomes are binary. Then, by Proposition 4 of Kang and Keele [37], we have

T (τx0,y0 ) → N(0, 1) SPILLOVER EFFECTS WITH NONCOMPLIANCE 31

For the plug-in test statistic T (τ ), we have bx0,y0 N (τ − τx ,y τ ) T (τ ) = J bY b 0 0 bD bx0,y0 q Var N (τ − τ τ ) | F, Z J bY bx0,y0 bD s ! Var [τ − τ τˆ | F, Z] τ − τ τˆ (τ − τ )τ bY x0,y0 D bY x0,y0 D x0,y0 bx0,y0 bD = p + p Var [τY − τx ,y τˆD | F, Z] Var [τ − τ τˆ | F, Z] Var [τ − τ τˆ | F, Z] b b 0 0 bY x0,y0 D bY x0,y0 D s Var [τ − τ τˆ | F, Z] = bY x0,y0 D T (τ ) Var [τ − τ τˆ | F, Z] x0,y0 bY bx0,y0 D s Var [τ − τ τˆ | F, Z] (τ − τ )τ bY x0,y0 D x0,y0 bx0,y0 bD + p Var [τY − τx ,y τˆD | F, Z] Var [τ − τ τˆ | F, Z] b b 0 0 bY x0,y0 D

By the proof in Theorem3 and under H0, the following convergences in probability are true

τ = pCO → τ = pCO, τ → τ , τ → τ bD b D bY Y bx0,y0 x0,y0 so that the product converges to zero in probability, i.e. (τ −τ )τ → x0,y0 bx0,y0 bD 0. We also note that because Yji,Dji are binary and the cluster-sized are bounded, both τbY and τbD are uniformly bounded. Then, by the dominated convergence theorem, under H0, we have

E[(τ − τ τ )2 | F, Z] → (τ − τ τ )2,E[(τ − τ τ ) | F, Z] → (τ − τ τ ) bY x0,y0 bD Y x0,y0 D bY x0,y0 bD Y x0,y0 D E[(τ − τ τ )2 | F, Z] → (τ − τ τ )2,E[(τ − τ τ ) | F, Z] → (τ − τ τ ) bY bx0,y0 bD Y x0,y0 D bY bx0,y0 bD Y x0,y0 D Hence, v h i s uE (τ − τ τˆ )2 | F, Z − E [(τ − τ τˆ ) | F, Z]2 Var [τ − τ τˆ | F, Z] u bY x0,y0 D bY x0,y0 D bY x0,y0 D = u → 1 t h 2 i 2 Var [τY − τx0,y0 τˆD | F, Z] E (τ − τ τ ) | F, Z − E [(τ − τ τ ) | F, Z] b b bY bx0,y0 bD bY bx0,y0 bD and by Slutsky’s theorem, we arrive at the desired result.

ACKNOWLEDGEMENTS We thank Guillaume Basse, Guanglei Hong and participants at the Uni- versity of Chicago Quantitative Methods Committee in the Social Sciences, Berkeley Research Workshop in Quantitative Modeling, University of Wisconsin- Madison Demography Seminar, 2018 NetSci Conference, 2018 Atlantic Causal Inference Conference, and Penn Causal Inference Seminar for helpful comments. 32 KANG AND KEELE

SUPPLEMENTARY MATERIAL Replication Materials for Empirical Analysis (http://www.e-publications.org/ims/support/download/xxx). The online sup- plement contains code and replication materials for the SPILLOVER EFFECTS WITH NONCOMPLIANCE 33

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