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Randomization-only Inference in Experiments with Interference

In experiments that study social phenomena, such as peer influence or herd immunity, the treatment of one unit may influence the outcomes of others. Such"interference between units"violates traditional approaches for causal inference, so that additional assumptions are often imposed to model or limit the underlying social mechanism. For binary outcomes, we propose an approach that does not require such assumptions, allowing for interference that is both unmodeled and strong, with confidence intervals derived using only the randomization of treatment. However, the estimates will have wider confidence intervals and weaker causal implications than those attainable under stronger assumptions. The approach allows for the usage of regression, matching, or weighting, as may best fit the application at hand. Inference is done by bounding the distribution of the estimation error over all possible values of the unknown counterfactual, using an integer program. Examples are shown using using a vaccination trial and two experiments investigating social influence.


Introduction
In experiments where the assumption of "no interference between units" does not apply, the effects of the treatment may extend to units receiving the control. Examples include vaccination studies where units receiving the placebo may be protected by the vaccine through herd immunity; economic effects such as those occurring in a marketplace; or social networks in which units may be influenced by information received from others. In such settings, generally an assumption is made to limit the effects of interference; for example, one might divide the units into groups that are assumed not to interfere with each other. In settings where such restrictions are implausible or have questionable validity, analyses relying on those assumptions may yield misleading conclusions.
For such settings, we propose to estimate contrasts in attributable treatment effects. The attributable effect is the difference between a unit's observed outcome and that which would have resulted under a uniformity trial, such as the counterfactual in which all units had received the control (Rosenbaum, 2001). In this paper, we show that such effects can be partially characterized as a function of each unit's direct treatment and indirect exposure to the treatment of others, potentially with no assumptions on interference.
For example, to give a simple characterization we might regress effects against treatment, where Effect i is the attributable effect for unit i, and Treatmenti is the binary indicator of that unit's treatment assignment. This is equivalent to the least squares problem, As a more complex example, given an observed social network we might regress effects against each unit's treatment, their number of treated friends, and an interaction term, β3 · (Treatmenti · # Treated Friends i ) In both (1) and (3), the variable Effect is not observed, and hence statistical inference is required to estimate the regression parameters.
The main result of this paper is that in regression specifications such as (1) and (3) with binary outcomes, contrasts such as β1, β2, and β3 can be interval estimated with no assumptions beyond those regarding randomization of treatment. Thus, these parameters can be reliably inferred even when interference between individuals is difficult to accurately model, including settings in which an observed network only crudely reflects the true underlying social mechanisms. The regression may include transformations of the treatment variable, or adjustments (i.e., "controls") if the indirect exposure to treatment is non-identically distributed. The approach also generalizes beyond regression, to estimands corresponding to weighted or matching-based comparisons of units. Inference requires novel computations to bound the interval widths.
In the regression (1), the coefficient β1 measures the relative benefits of being treated versus not treated. For example, consider a vaccination trial where those receiving the placebo might be indirectly affected by the vaccines. In this setting, an appropriately signed β1 would indicate that the vaccinated units were relatively more protected than those who received the placebo, by an additional β1 cases prevented per capita. Similarly, in (3), the coefficients β1, β2, and β3 characterize the relative effects as a function of direct and indirect exposure to treatment. In vaccination settings, this might imply that units were relatively more protected when vaccinated, and additionally that placebo units were relatively more protected when their friends were vaccinated.
Relative effects are a partial characterization, and carry the caveat that "more protected" may actually mean "less harmed", if making the treatment available causes everyone to become worse off. For example, a vaccine trial might prevent an even more effective intervention from being deployed. Such scenarios, when legitimately plausible, will have implications for all methods of analysis.
How might such estimates be used? Decision-makers must often operate with incomplete information, and a rigorous estimate of relative effects might be more convincing than one that measures total effects, but hides uncertainty by making overly strong assumptions. When communicating with policy makers, Manski (2013) and Nagin and Sampson (2019) emphasize the importance of properly conveying uncertainties that might otherwise be hidden by strong assumptions, with Nagin and Sampson (2019) specifically focusing on the challenges of interference. Along these lines, doing an analysis both with and without questionable assumptions may communicate the range of possible answers to a question. Thus our approach might complement others.
In some settings, the research question may be of the form "is X contagious?", for behaviors and conditions such as product adoption, criminal behavior, and obesity. In such studies, the treatment might serve primarily to trigger a social influence mechanism so that it can be observed under randomization. Then estimation of relative effects might advance knowledge by showing that a social effect exists, and that it can be partially identified in a rigorous way. This could fill an important role. For example, Christakis and Fowler (2007) studied contagion of obesity and received widespread attention, but also strong criticism for lack of rigor (Lyons, 2011).

Related Work
Our work is part of a growing literature on statistical inference in the presence of interference between units. Approaches vary in their target estimand and severity of modeling assumptions, with stronger inferences generally requiring stronger assumptions.
Under the assumption of a known exposure model (Aronow and Samii, 2017;Eckles et al., 2017), the outcome of each unit depends on the treatments through a set of statistics, termed the unit exposure; for example, a unit's exposure might equal the treatment of its neighbors in an ellicited social network. For this setting, Aronow and Samii (2017) gives propensity-weighted estimates and confidence intervals for the average treatment effect, which they define to be the difference in average outcome between two treatment allocations (such as full treatment and full control).
The papers Hudgens and Halloran (2008); Sävje et al. (2021); Leung (2019); Liu and Hudgens (2014);Hu et al. (2021); Li and Wager (2020) consider the expected effects of intervening on the treatment of a single unit, assuming the treatment of all other units to be randomized according to the experiment design. Estimands of this type (sometimes termed the EATE) have been defined for direct and indirect effects (Hu et al., 2021), and also generalized to misspecified exposure models (Leung, 2019). For this class of estimands, unbiased point estimation requires no assumptions beyond randomization; however, variance estimates and valid confidence intervals require assumptions on interference, although not on its exact structure. For example, Leung (2019) requires a bandwidth parameter to be chosen according to the strength of the assumed interference; Sävje et al. (2021) proposes variance inflation factors based on the degrees of the underlying dependency graph; and Li and Wager (2020) consider random networks with distributional interactions between units.
With the exception of Section 4.3, we will assume only that treatments are randomized, so that interference may be unknown and unbounded in strength. Previous work in this setting includes testing for null hypotheses related to peer effects, such as the hypothesis of direct effects but no spillovers (Athey et al., 2018;Aronow, 2012;Basse et al., 2019); and estimation of effects on the ranks of the treated and control units when ordering by outcome (Rosenbaum, 2007).
Other related works Estimation under parametric modeling assumptions is studied in Rigdon and Hudgens (2015), and under an assumption that the effect is nonnegative in Choi (2017). The definition and estimation of vaccine-specific effects is an active field, whose breadth is beyond our scope; we refer to Cai et al. (2021) for a recent discussion. Inference in observational studies with interference is also an active area of research, and we refer to Forastiere et al. (2021) and Ogburn et al. (2017). A technical report (Choi, 2018) considers the estimand τ1 given by (6), but without generalization to other regressions, weighting, or matching.

Basic Approach
To introduce the main concepts, and to draw parallels with existing approaches, we first describe our method for the simple regression (1) that measures differences in attributable effects for the treated and control.

Defining the Attributable Effect
We assume a randomized experiment on N units, and let X ∈ {0, 1} N denote the treatment assignment (whose distribution is known), Y ∈ {0, 1} N the observed outcomes 1 , and θ ∈ {0, 1} N the counterfactual outcomes that would result under a "uniformity trial" (Rosenbaum, 2007). Under the uniformity trial, the random treatment assignment X is generated but not actually administered, so that the outcomes are unaffected by it. A common choice of uniformity trial is to let θ denote the outcomes if all units were to receive the control regardless of X. We do not assume or require θ to be observed (even indirectly) for any unit. We define the individual-level attributable treatment effect to be the vector Y − θ.
For example, in a vaccination trial the treatment Xi might denote whether unit i received the vaccine or a placebo, Yi whether the unit had the disease, and θi the counterfactual outcome that would have resulted if all units were given the placebo. Letting an outcome of 1 denote the disease and 0 otherwise, an effect of Yi − θi = −1 would mean that unit i did not have the disease, but would have if the placebo had been administered to all participants. In such a case, it can be said that administering the vaccine prevented this unit from having the disease. This can occur even if the unit received the placebo in the trial, due to social effects such as herd immunity. The vector Y − θ clearly has a causal interpretation, and is the effect of the treatment under the observed treatment assignment. It can be seen that averaging Y − θ equals the attributable effect which is studied in Rosenbaum (2001). Our focus will be to partially characterize Y − θ by estimating a partial regression coefficient, or a weighted or matching-based comparison of the unit outcomes. We will typically make no assumptions on θ except on its range of allowable values. In particular, we do not assume that θ is observed for any unit, and even allow Y to be uninformative for the values of θ.

A Simple Example
Let N1 and N0 denote the number of treated and control units, and let X = N1/N denote the average treatment. We consider a slight modification of the regression (1), which is equivalent to the least squares problem It can be seen that the intercept τ0 and slope τ1 are given by so that τ0 is the average attributable effect, and τ1 is the difference in attributable effects for the treated and control. The estimand τ1 answers whether the units receiving the treatment were affected differently than those receiving the control (and by how much), while knowledge of both parameters (τ0, τ1) specifies the attributable effects for each group.
To give a possible usage for τ1, suppose that an intervention is believed to have positive effects, perhaps due to previous experiments in which units were effectively isolated, preventing interference. Then given a more operational deployment in which the treatments are not isolated, one might ask if the assignment was sufficiently dense to saturate the population. For example, one might wish to know whether placebo units were nearly as well-protected as those receiving a vaccination, or whether an assignment of service providers provided evenly distributed spatial coverage. Estimating τ1, the difference in effects that were experienced by treated and untreated units, could be part of an analysis to answer such questions.
Estimation of τ 1 The quantity τ1 is not a parameter, but rather an unobserved random variable. Conservative prediction intervals (PIs) can be found for τ1 when X is assigned by sampling without replacement. Lettingτ1 denote a point estimate equal to the difference in observed outcomesτ it can be seen that the estimation error τ1 −τ1 is given by which is the difference between a random sample and its complement from the unknown θ. As a result, we can apply a finite population central limit theorem to find a prediction interval for (τ1 −τ1), and hence for the estimand τ1. The width of this interval will depend on the unknown variance σ 2 θ , given bȳ Proposition 1 gives the prediction interval, using the bound σ 2 θ ≤ 1/4 which holds for binary outcomes. It is proven in Section B.1 of the supplement.
Comparison with SATT The point estimateτ1 given by (7) is the difference in mean outcomes, and also appears in estimation for the average treatment effect (ATE), the average treatment effect on the treated (ATT), and the expected average treatment effect (EATE).
The prediction interval for τ1 is most closely related to that of the sample ATT discussed in Sekhon and Shem-Tov (2021). To see this, assume an experiment where treatment is assigned by sampling without replacement, and letȲ1 andȲ0 respectively denote the average observed outcomes for the treated and control groups, and let θ denote the counterfactual outcomes that would occur if all units received the control, with θ1 andθ0 defined analogously.
In the absence of interference, it holds for the control units that Yi = θi. The sample ATT is defined as the difference between the observed and counterfactual outcomes for the treated units, The estimatorτ1 equalsȲ1 −Ȳ0, and has errorτ1 −τ SATT =θ0 −θ1, where we have usedȲ0 =θ0. This error is zero mean and has variance with σ 2 θ given by (9). Since Yi = θi for the control units, the empirical variance of the control outcomes {Yi : Xi = 0} is consistent for σ 2 θ and can be plugged into (10) to estimate Var τ1 − τ SATT .
In the presence of interference, θi need not equal Yi for the control units. For example, the effects of the treatment may be redistributive, helping the treated by hurting the control. Thenθ might approximately satisfyȲ0 ≤θ ≤Ȳ1. More generally,θ ∈ [0, 1] if no assumptions are made.
In such settings, we cannot estimate τ SATT , but we can estimate τ1, the difference in effects for the treated and control. As shown by (8), the estimation errorτ1 − τ1 again equalsθ1 −θ0, and hence its variance is the same as (10). However, σ 2 θ can no longer be estimated from the control outcomes, and must be bounded by 1/4 if no further assumptions are made, resulting in a prediction interval that is wider than that of τ SATT by a factor of (2σY 0 ) −1 .
In some cases, it may be reasonable to reduce this factor by bounding σ 2 θ =θ(1 −θ) more tightly. For example, in Section 4.3 we consider a vaccination trial in which the disease rate ranged from 0.002 to 0.005 in the preceding years. In such a case, it might reasonable to boundθ by a safety factor of the historical values, as opposed to allowingθ to equal 0.5, which would be implausibly high for this setting.
Comparison with EATE The point estimateτ1 is also unbiased for the expected average treatment effect (Sävje et al., 2021), which can be written as If the units are independently assigned to treatment or control, the EATE is the expected effect of intervening on a unit on that unit's outcome, where the expectation is taken over the randomly assigned treatment of the others. While τ1 and the EATE have the same point estimate, they have quite different sources of estimation error, which are not "nested" in any sense. Unlike τ1, the estimation error for the EATE is the difference betweenτ1 and its expectation E[τ1], and hence depends on the observed outcome vector Y , whose values may have unknown dependencies that must be controlled by additional assumptions. As a result, the confidence interval width for the EATE will depend on the strength of the assumption that is made. Under strong assumptions, the interval width for the EATE may approach those attainable under an assumption of no interference; under very weak assumptions, consistent estimation of the EATE may not be possible.
To give a simple example of the latter case, suppose that the outcomes are given by so that depending on the treatment of unit 1, the outcome of unit i is given either by fi(Xi) or by gi(Xi). In this case the point estimate will be inconsistent for the EATE (while remaining √ N -consistent for τ1), as the EATE depends on both f and g, but only one of the two will be observed.

General Case
We generalize τ1 to allow the estimand to be a linear function of Y − θ, where the weight w should depend only on X and be approximately zeromean in order for our interval estimates to be small. To implement this requirement when the treatment (or the indirect exposure to treatment) is non-identically distributed, we can use matching, weighting, or regression adjustment to draw approximately unbiased comparisons between units.
Preliminaries To measure each unit's indirect exposure to the treatment of others, let A ∈ {0, 1} N ×N denote the adjacency matrix of an observed network. Given a treatment assignment X, let Z = (Z1, . . . , ZN ) denote the number of treated neighbors for each unit, and let W = (W1, . . . , WN ) the thresholding at a fixed level zmin: We will assume that the units can be partitioned into K propensity classes Π1, . . . , ΠK , where n k = |Π k | denotes the size of class k, and k(i) equals the propensity class of unit i. Nominally, Zi and Zj should be identically distributed if k(i) = k(j). For example, if X is assigned by sampling without replacement, then the distribution of Zi varies only with i's number of neighbors in the network A. In some cases, the propensity classes may be misspecified, so that units belonging to the same class may have nonidentical exposure distributions. Then our approach will produce wider intervals, so as to not be invalidated.

Examples
Regression Let β ∈ R d denote a general regression specification, solving the least squares problem . Then β is given by and it can be seen that the th entry of β can be written in the form w(X) T (Y − θ) for w given by where e ∈ R d is the th column of the d × d identity matrix. We give two examples. Let β adj denote the partial regression coefficient that arises when regressing the treatment effects Y − θ on the exposures Z and the set of K indicator variables representing the membership of each unit in the propensity classes Π1, . . . , ΠK : where ζ k is the average exposure for the kth propensity class To interpret β adj , we may say that for two individuals in the same propensity class, a unit difference in the level of exposure is associated with a β adj difference in their individual-level attributable effects. As a second example, regress Y − θ on a set of indicator variables for the possible values of Z and also on the K propensity classes. This results in the least squares problem where D denotes the maximum value of Z. Here the regression coefficients γ0, . . . , γD correspond to the levels of Z, and ν corresponds to the propensity classes. We may then choose the contrasts γ d − γ0, for d = 1, . . . , D, as the estimand of interest. To interpret these contrasts, we may say that γ d − γ0 predicts the difference in attributable effects for a unit with exposure level d compared to one in the same propensity class who had zero exposure.
Weighting and Matching Given thresholded exposures W and propensity classes Π1, . . . , ΠK , let n k1 and n k0 denote the number of units in Π k for which Wi = 1 and Wi = 0, respectively. Let τ weighted denote the weighted difference which can be interpreted as the difference in attributable effects within each propensity class, averaged together after weighting by class size. It can be seen that τ weighted can be written in the form w(X) T (Y − θ) for w(X) given by Alternatively, we can construct a matched subset of units by randomly pairing units within the same propensity class (where one unit in each pair has Wi = 1 and the other has Wi = 0), without replacement until no more pairs can be formed. Let M denote the set of all units included in the matching, and let m = |M|/2 denote the number of matched pairs. Let τ matched denote the difference in attributable treatment effects between the matched units, The value τ matched is analogous to τ , measuring the difference in attributable effects for the units in the matching. It can be seen that τ matched equals w(X) T (Y − θ) for w(X) given by As units are randomly paired within the same propensity class, the quantity τ matched is random given X. If this is undesireable, the expectation of τ matched may be used instead. This quantity closely resembles τ weighted , and is given by where m k = min(n k1 , n k0 ) equals the number of matched pairs formed in the kth strata, with m = k m k .

Estimation
In principle, estimation for the general estimand w(X) T (Y − θ) proceeds similarly to that of τ1, by defining the point estimate to equal w(X) T Y .
This point estimate will usually take intuitive form. For example, if the estimand w(X) T (Y − θ) is a regression on the attributable effects, then w(X) T Y is simply the regression applied to the observed outcomes. Likewise, if the estimand is weighted or matching-based comparison, then w(X) T Y is simply that comparison applied to the observed outcomes. This point estimate need not be unbiased, in the sense that the estimation error w(X) T θ may not be zero-mean; however, the expectation of the error can be bounded by which can be easily evaluated when Ew(X) is known, as is the case for a randomized experiment.
To find a prediction interval, we will first show that a central limit theorem holds for w(X) T θ, wherew T θ is a location parameter for the asymptotic distribution. This implies a normal-based interval for w(X) T θ given bȳ As θ is unobserved, the boundaries of this interval are unknown, but we can find an outer bound by maximizing and minimizing over the unknown values of θ, resulting in the upper and lower bounds U and L given by and a (1 − 2α) level prediction interval for the estimand is given by Proposition 2 gives conditions under which prediction intervals for a variety of estimands will asymptotically have correct coverage. It assumes a sequence of experiments in which the number of units N goes to infinity, where the estimation error w(X) T θ is a smooth function h of an averaged random vector T (X) of sufficient statistics. The theorem applies the delta method and uses a central limit theorem for sums of variables whose dependency graph has bounded degree (Rinott, 1994, Thm 2.2), whose application requires Bernoulli randomization of the treatment vector X.
Proposition 2. Given constants dmax, ρ, B, q,Σ ∈ R q×q ,T ∈ R q , and mapping h : R q → ∞ that is continuously differentiable in a neighborhood ofT , assume a sequence of experiments with estimands w(X) T (Y − θ), in which N → ∞ and the following hold A.1 Each unit is assigned to treatment independently with probability ρ ∈ (0, 1) A.2 The adjacency matrix A ∈ {0, 1} N ×N has in-degree and out-degree bounded by dmax so that each φi depends only on the treatment of unit i and i's neighbors in A.
A.4 ET (X; θ) converges toT , and √ N · T (X; θ) has covariance matrix converging toΣ, which is non-zero but may be non-invertible Under these conditions, letw satisfyw T θ = h(ET ), and let U and L equal (25) and (26) respectively. Then the quantity Corollary 1 gives conditions under which Proposition 2 can be applied to the regression weights β given by (15).
Corollary 1. Assume a sequence of experiments with N → ∞ which satisfy conditions A.1 and A.2 of Theorem 2, where w(X) as given by (16) for any satisfies condition A.5, with ξi satisfying ξi(X) ∞ ≤ B for all X, and ξi(X) = ξi(X ) if Xi = X i and Xj = X j for all j : Aij = 1 so that ξi(X) depends only on the treatment of unit i and i's neighbors in A. Let φi(X) be given by where ⊗ denotes kronecker product, and let T (X) = N −1 i φi(X) satisfy condition A.4. Then for the estimand β given by (15), the conclusions of Proposition 2 apply to the interval estimation of β withw given bȳ Corollary 2 gives conditions under which Proposition 2 can be applied to the weighted contrast τ weighted , as given by (19).
Corollary 2. Assume a sequence of experiments with N → ∞ which satisfy conditions A.1 and A.2 of Theorem 2, with w(X) given by (20) for fixed K satisfying condition A.5. Let φi(X) ∈ R 4K be given by where ⊗ denotes kronecker product and e k denotes the kth column of the K × K identity matrix, with n k /N ≥ 1/B for all k ∈ [K], and T (X) = N −1 i φi(X) satisfying condition A.4. Then the conclusions of Proposition 2 apply to the interval estimation of τ weighted , withw given byw Remarks 1. Conditions A.1 and A.2 of Proposition 2 are required to apply the central limit theorem of (Rinott, 1994, Thm 2.2), which applies to sums of dependent variables, such as the entries of W . Condition A.4 of the proposition implies √ N -asymptotics, under which A.5 is required for the delta method to yield intervals with the desired coverage. Conditions A.1 and A.5 can potentially be removed when delta method and central limit theorem of Rinott (1994) are not used, as shown for τ1 in Proposition 1 and for β adj in Proposition 3 contained in the appendix.
2. To enforce the degree constraint given by A.2, we might sparsify the observed network A, for example by considering only sameneighborhood connections. This changes the regression specification or estimand that is being considered. However, it does not assume interference to be limited to the sparsity pattern of A.
3. While Corollary 1 implies that prediction intervals can be found for all entries of β and will have correct coverage, the intervals may be vacuously wide for entries corresponding to non-contrasts (such as the intercept term), or if the regression does not include adjustment for non-identically distributed X or Z. In such cases the entries of w may be large, resulting in large bounds for U and L.

Computation
As Var(w T θ) equals θ T Qθ for Q = Eww T − EwEw T , solving for U given by (25) requires solving the optimization problem max ϑ∈{0,1} Nw To ensure coverage of the prediction intervals, a local optimum to (29) is not sufficient -either the global solution or an upper bound must be found. As Q is positive semi-definite, this requires maximization of a convex objective, which is computationally difficult even if the integer constraint on ϑ is relaxed to the convex set [0, 1] N .
To solve or upper bound (29), we proceed in two steps. First, we find a diagonal matrix D such that Q − D is negative semidefinite. This can be done by solving the semidefinite program where ≥ 0 denotes nonnegativity and 0 denotes negative semidefinite. Then, we can rewrite (29) as max ϑ∈{0,1} Nw It can be seen that the objective of (30) is concave, but equals that of (29) for ϑ ∈ {0, 1} N , since x = x 2 if x is binary valued. (30) can be solved or bounded by Gurobi using branch-and-bound methods. For faster computation, an upper bound can be found by relaxing the integrality constraint of (30) to ϑ ∈ [0, 1] N , resulting in a concave maximization problem whose global optimum can be efficiently found. Solving for L given by (26) proceeds analogously. In principle, assumptions on θ may be incorporated in the optimization of (25) and (26), in the form of additional constraints. Doing so may result in smaller confidence intervals. Such assumptions may be easier to consider than those that directly bound interference; for example, in Section 4.3 we consider a bound on θ based on historical rates of the outcome in the years prior to treatment.

Social Networks and the Decision to Insure
In the experiment described in Cai et al. (2015), rural farmers in China were randomly assigned to information sessions where they would be given the opportunity to purchase weather insurance 3 . First round sessions were held three days before second round sessions, so that first round attendees could have informal conversations with their second round friends, in which they might share their opinions about the insurance product. A major goal of the experiment was to demonstrate the effects of information sharing through this channel.
The farmers were instructed to list 5 close friends with whom they specifically discussed rice production or financial issues. One of the conclusions of Cai et al. (2015) was that the decision to purchase insurance was affected not only by a farmer's own treatment assignment, but also by that of their friends; specifically, farmers assigned to a second round session were more likely to purchase insurance if more of their listed friends in the first round were assigned to a high-information session.
Setup We let M and N denote the number of units in the first and second rounds, and define X, Y , Z, and θ as follows. For the first round units, let X ∈ {0, 1} M indicate whether each unit was assigned to a high or low information session. For the second round units, let Y ∈ {0, 1} N indicate whether or not they purchased insurance; Z their number of samevillage first round friends assigned to a high information session; and θ ∈ {0, 1} N their outcomes that would have occurred under a counterfactual in which the first round sessions were not held. For example, if Yi = 1 and θi = 0, then unit i purchased insurance, but would not have done so if the first round sessions were not held. Thus Y − θ equals the effect of the first round sessions on the purchasing decisions of the second round.
We will assume that X is randomized by simple random sampling within each village, inducing propensity classes that were the interaction of village and number of first round friends. In fact, Cai et al. (2015) reports that treatments were stratified by family size and amount of land used for rice farming; however, further details are not included, and additionally these variables are missing for a significant fraction of the first round units. For this reason, our results for this example should be viewed primarily as a illustration of the proposed method.
Results Table 1 gives estimates for various parameters described in Section 3.1. The point estimate for β adj suggests that for two farmers in the same propensity class, a unit difference in their number of high information first round friends was associated with a 0.08 difference in the effects of the first round sessions. However, the interval is weakly non-significant (95% PI: [0.0, 0.16]).
The contrasts γ d − γ0 suggest an effect threshold at 2 high information friends. Units with 1 high information friend experienced effects that were indistinguishable from those with zero such friends. In comparison, units with 2 such friends were more strongly encouraged to purchase insurance, with effects that were 22% larger (95% PI: [2%, 41%]) than the effects on those with zero high info friends. Contrasts γ d − γ0 for d ≥ 3 were nonsignificant due to small numbers of units with Z ≥ 3. Similar differences in effect were estimated by the weighted and matching-based estimands τ weighted , τ matched , and E[τ matched |X], using the thresholded exposures Wi = 1{Zi ≥ 2}.
The interpretation of our estimates is that the second round units were affected by the first round sessions, with effects that correlated with the information content given to their first round friends, and in particular with whether at least two such friends received high information content.

Simulated Vaccine Trial
We analyze the vaccinesim dataset, which simulates a vaccine trial using models that were partially fit to an actual cholera vaccine trial, as described in Perez-Heydrich et al. (2014)  Yi = 1 that the unit had cholera; θi their outcome under the counterfactual in which all units had received the placebo; and Vi their neighborhood vaccination rate which equals the fraction of individuals in i's neighborhood (including non-participants) who were assigned to vaccination. Participants were assigned independently with probability 2/3 to receive the vaccine, otherwise receiving the placebo. Supplement C contains additional simulation details.
Results We estimate τ1 given by (6) and β1, β2, and β3 in the regression of effects on direct treatment, neighborhood vaccination rates, and their interaction, where the control terms are the expectations E[Vi] and E[XiVi], which depend on (and control for) the number of participants and non-participants in each neighborhood. Table 2 shows the resulting estimates. They suggest that vaccinated units were relatively more protected than placebo units, and that placebo units were relatively more protected when their neighbors were vaccinated. Estimates for β1, β2 and β3 had high uncertainty, and 90% prediction intervals are shown. τ1 indicates that vaccinated units were relatively more protected than placebo, with 0.12 additional cases prevented per capita. However, this may underrepresent the effects of the vaccine, as placebo units may have been protected by the vaccines. To see this, observe that the point estimates for β1 and β3 suggest that the relative effects varied with neighborhood vaccination rates, with 0.22 − 0.29 · vaccination rate additional cases prevented per capita for vaccinated units versus placebo. Thus in neighborhoods with low vaccination rates, the difference in effects for vaccinated and placebo units may have been significantly larger than the overall difference given by τ1.
where E[ · | · ; α] denotes expectation under i.i.d. Bernoulli(α) randomization of treatment for all individuals, including non-participants. It can be seen that DE(α) is the expected effect of intervening on a single random unit, if all individuals (including non-participants) were randomized to receive the vaccine with probability α. Similarly, IE0(α, α ) is the expected effect on a placebo unit of changing the probability of vaccination for all individuals from α to α. Figure 1 shows estimates and true values for IE0(α, 0.4) and DE(α) for a range of α values. In comparison to β, have similar values, but show less uncertainty and describe the overall effects of possible interventions, rather than relative effects of the observed treatment. However, they assume no interference between neighborhoods, and also assume that the decision to participate followed a known functional form dependent only on observed covariates.

Coverage of Confidence Intervals
Using the simulation parameters given in Perez-Heydrich et al. (2014), we may generate the unknown counterfactual outcomes θ and simulate X to measure the coverage rates of our confidence intervals. In 10K simulations, the intervals for β1, β2,  Fig. (c) and (d) show effects relative to that of 40% vaccination. and β3 achieved coverage but were as much as 2.2 times wider than necessary. However, for other values of θ, found by solving (25), the coverage of the 90% interval was as low as 91%. This suggests that the interval widths were necessary in order to have coverage for all possible values of θ, as required without further assumptions.

Real Vaccine Trial (Aggregate Outcomes)
The paper Ali et al. (2005) analyzes the actual results of the cholera vaccine trial, in order to investigate the possibility of indirect (herd) protection under high levels of vaccination. A table of aggregate outcomes for the actual cholera vaccine trial is given, which we aggregate further in Table 3 into two groups of roughly equal size, by dividing the units according to whether their neighborhood vaccination rate was ≤ 40% or > 40%. We consider the regression (Yi − θi) ∼ β1Xi + β2(Xi · i ∈ group 1) + controls, where the control terms are the membership indicators for groups 1 and 2.
With no further assumption on θ, we allow for the possibility that in the absence of the vaccinations, the cholera rate could have been hundreds of times larger than the observed rate of 2.8 cases per thousand. As this may be unrealistic, we will consider an additional assumption based on past cholera rates. The trial covered the Matlab region of Bangladesh in 1985, and cholera rates for this region are given in (Zaman et al., 2020, Fig . 1). We will assume that under the counterfactual θ in which all units receive the placebo, the cholera rate for the participants would be upper bounded by 7 cases per thousand, which is substantially higher than the highest observed rate of 5 per thousand in the ten years before the trial. As the participants (≈ 30% of the population) are not a random sample, some caution is required; however,   (31) may easier to consider than a bound on interference between neighborhoods.
The coefficients β1 and β2 characterize the relative effects of receiving the vaccine versus placebo, in each group. Table 4 shows the results. The estimates suggest that vaccinated units were relatively more protected that placebo ones, by a difference of 1.3 + 2.2 · 1{unit is in group 1} additional cases prevented per thousand. Prediction intervals (weakly) exclude zero for the interaction term β2, indicating that the relative effects were different for the two groups, and also for β1 + β2, which gives the relative effects for group 1 which had lower vaccination rates. These results suggest that the overall difference in outcomes between treatment and control, which equaled 2.4 cases per thousand, may under-represent the effects of the vaccine, as larger relative effects occurred when vaccination rates were low.

Conclusions
We have presented an approach for partial estimation of unit-level attributable effects given a randomized trial on a single network with strong unmodeled interference. The approach goes beyond testing to give a partial characterization, returning interval estimates for the relative effects of treatment.

Supplemental Materials
The supplement contains analysis of a social experiment (Paluck et al., 2016); proofs; and data summaries.

Supplemental Material for "Randomizationonly Inference in Experiments with Interference"
A Support for Conflict Reduction in Schools The paper Paluck et al. (2016) describes an experiment 5 in which public middle schools were randomized to receive a treatment designed to encourage anti-conflict norms and behavior in students. Within each treated schools, a small subset of eligible students (between 40-64) were randomized between treatment and control. Treated students were invited to participate in bi-monthly meetings in which they designed and enacted strategies to reduce schoolwide conflict. Outcomes for all students in each school included the self-reported wearing of an orange wristband representing support for anti-conflict norms. Network information ("spent time with") was recorded for all students. Estimation of effects on the wristband outcome has been used in Aronow (2012) and Leung (2019) to illustrate their proposed methods, as we do here.
Setup Let Xi denote if student i was invited to participate in the anticonflict meetings (which can only equal 1 for eligible students), and Yi their outcome of whether they self-reported wearing the wristband representing support for anti-conflict norms. Breaking slightly from the previous examples, we define the counterfactual θi to denote their outcome if all eligible units were invited to participate in the meetings ("full treatment"). With θ so defined, the difference Y − θ is interpretable as the effect of not inviting the control units to participate.
Results Following Aronow (2012) and Leung (2019), we estimate differences in treatment effect on four groups of students, corresponding to whether or not they were invited to participate in the meetings, and also whether or not they had at least one network connection who was invited to participate. Figure 2a shows estimates of E[τ matched ] for units that were matched based on school and number of eligible friends. Similar results were found using weighting or matching. A significant difference in effects was found between two groups; as a result of not inviting the control units to participate, units in control whose friends were also in control were affected more adversely than those who were treated and had at least one treated friend.

B Proofs
We prove Propositions 1 and 2, Corollaries 1 and 2, and also state and prove Proposition 3, which gives an alternate interval estimate for β adj .

B.1 Proof of Proposition 1
Our proof of Propositions 1 and 3 will use the following finite population central limit theorem. Lemma 1 gives a simpler expression for the difference in means of θ, from which its variance can be derived.
Lemma 1. Let X be assigned by sampling N1 units without replacement, and letθ and σ 2 θ denote the mean and variance of θ. Then it holds that which is the average of N1 samples without replacement from the finite population u1, . . . , uN , where ui = (θi −θ)N/N0, and which has variance Proof of Lemma 1.
This equals the average of N1 samples without replacement from the finite population u1, . . . , uN , where ui = (θi −θ)N/N0, which is known to have variance equal to 1 N 1 N 0 N −1 multiplied by the variance of {ui}, which equals (S.2).
Proof of Proposition 1. It can be seen that τ1 −τ1 equals By Lemma 1, this equals the average of N1 samples without replacement from the finite population u1, . . . , uN , where ui = (θi −θ)N/N0, with variance given by (S.2). Hence the terms mN and vN as defined in Theorem 1 can be bounded by To prove the proposition, we will divide the sequence of experiments into two subsequences: (i) those for which σ 2 θ ≥ (log N )/N , and (ii) those for which σ 2 θ < (log N )/N , and then show coverage of the proposed interval for each subsequence separately.
For subsequence (ii), plugging σ 2 θ < (log N )/N into (S.2) implies that Var(τ1 −τ1) is a vanishing fraction of z1−α 1 4 N N −1 N N 1 N 0 , the width of the proposed confidence interval. As a result, for this subsequence it holds by Chebychev's inequality that and hence that τ1 is in the intervalτ1 ± z1−α 1 4 N N −1 N N 1 N 0 with the same probability.

B.2 Proof of Theorem 2
The proof of Theorem 2 will use several tools.
The Cramer-Wold device (Van der Vaart, 2000, Sec 2.3) states that a sequence of random vectors Xn ∈ R d converges in distribution to X if and only if T Xn converges in distribution to T X for all vectors t ∈ R d .
Theorem 2 describes a uniform delta method (Van der Vaart, 2000, Thm 3.8), which implies that if √ nX converges to a multivariate normal distribution, then f (X) does so as well after centering and rescaling, if f is continuously differentiable around the limit point of X.
Theorem 2. (Van der Vaart, 2000, Thm 3.8) Let f : R d → R be a continuously differentiable mapping in a neighborhood ofT , and let random vectors Tn ∈ R d and non-random (Tn, rn) ∈ R d × R satisfy thatTn →T , rn → ∞, and rn(Tn −Tn) converges in distribution to a random vector T .
Then rn(f (Tn) − f (Tn)) converges in distribution to ∇f (T ) T T , the inner product of T and the gradient of f atT . Moreover, the difference between rn(f (Tn) − f (Tn)) and ∇f (T ) T rn(Tn −Tn) converges in probability to 0. Theorem 3 is a central limit theorem (Rinott, 1994, Thm 2.2) that requires the notion of a dependency graph: Given a collection of dependent random variables X1, . . . , XN , a graph with N nodes is said to be its dependency graph if for any two disjoint subsets S1 and S2, if there is no edge in the graph connecting S1 to S2 then the sets of random variables {Xi : i ∈ S1} and {Xi : i ∈ S2} are independent.
Theorem 3. (Rinott, 1994, Thm 2.2) Let X1, . . . , XN be zero-mean random variables having a dependency graph whose maximal degree is strictly less than D, satisfying |Xi − EXi| ≤ B a.s., i = 1, . . . , N , and Var N i=1 Xi = σ 2 > 0. Let Φ denote the CDF of a standard normal. Then for all t ∈ R it holds that Lemma 2 bounds the degree of the dependency graph for the thresholded exposures.
Lemma 2. Let the assumptions and definitions of Theorem 2 hold. Then the random vectors φ1(X), . . . , φN (X) have dependency graph with maximum degree bounded by d 2 max . Proof of Lemma 2. Let G denote the graph with N nodes which has an edge between i and j if A i = A j = 1 for any node , so that is a common neighbor of both i and j. Since A has maximum degree dmax, it can be seen that G has maximum degree d 2 max . To see that G is the dependency graph for φ1(X), . . . , φN (X), we observe that since treatments are assigned independently, if nodes i and j are not connected in G, they have no common neighbors in A, and hence φi(X) and φj(X) depend on disjoint treatments and are independent. Similarly, given disjoint subsets S1 and S2 with no edges between them in G, it follows that the sets {φi(X) : i ∈ S1} and {φi(X) : i ∈ S2} also depend on disjoint treatments and are are independent, making G the dependency graph of φ1(X), . . . , φN (X).
Proof of Theorem 2. Let Σ equal the covariance matrix of √ N T (X), which may be non-invertible. We will show that T T (X) is asymptotically normal for every non-zero vector ∈ R L , from which multivariate normality of T (X) will follow by Cramer-Wold device 6 . In turn, the delta method will imply that h(T (X)) is asymptotically normal after centering and rescaling.
Given ∈ R L , it can be seen from condition A.3 that Dividing by Var( T T (X)) = T Σ /N yields For any fixed not in the nullspace ofΣ, (S.8) can be seen to equal a sum of N zero-mean random variables that are bounded by O(1/ √ N ), where we have used that φi is bounded, and that T Σ → TΣ , which is bounded away from zero for not in the nullspace. As the variables in the sum are scaled and centered functions of {φi(X; θi)}, their dependency graph has maximum degree d 2 max by Lemma 2. As a result, for / ∈ nullspace(Σ), Theorem 3 can be applied to show that To apply Cramer-Wold, we must show that √ N · T (T −ET ) converges in distribution to N (0, TΣ ) for all vectors . To show this result for / ∈ nullspace(Σ), (S.9) implies that . As a result, by Cramer-Wold it follows that √ N (T − ET ) is asymptotically N (0,Σ). By the delta method (Theorem 2), this implies that √ N (h(T )−h(ET )) is asymptotically normal, with non-vanishing variance by assumption A.5. Letting U = max ϑ w T ϑ + z1−α Var(w(X) T ϑ) , it follows that where (S.10) holds because h(T (X)) = w(X) T θ, h(ET ) =w T θ, and N Var(w(X) T θ) → N Var[h(T (X))] > 0, and (S.11) follows from the asymptotic non-degenerate normality of √ N h(T (X)). As this shows that w T θ ≤ U with probability asymptotically at least 1 − α, it follows that holds with the same probability. This proves the lower bound of the prediction interval for w T (Y − θ). The proof of the upper bound proceeds analogously.

B.3 Proof of Corollaries 1 and 2
To prove Corollaries 1 and 2, we must show that w(X) T θ = h(T (X)) for some smooth function h, and verify thatw T θ = h(ET ), as required to apply Proposition 2.
Proof of Corollary 1. Let M ∈ R d×d and v ∈ R equal It can be seen that T (X) = N −1 i φi(X) equals where vec(M ) denotes the vector in which the columns of M are stacked on top of each other. Since w(X) T θ satisfies it follows that w(X) T θ can be written as h(T (X)) for a smooth function h. From this and the assumptions of Corollary 1, condition A.3 of Proposition 2 is fulfilled. It can also be seen thatw T θ = h(ET ). As the remaining conditions of Proposition 2 are assumed by the corollary, the proposition follows.
Proof of Corollary 2. Let v 1 , v 2 , v 3 , v 4 ∈ R K be given by v (1) It can be seen that T (X) = N −1 i φi(X) equals It can be seen that w(X) T θ can be written as h(T (X)) for a smooth function h, by the following steps From this and the assumptions of Corollary 2, condition A.3 of Proposition 2 is fulfilled. It can also be seen thatw T θ = h(ET ). As the remaining conditions of Proposition 2 are assumed by the corollary, the proposition follows.

B.4 An Alternate Prediction Interval for β adj
Proposition 3 gives an alternative prediction interval for β adj , whose validity holds under different conditions than those assumed by Proposition 2. In particular, here we assume that treatments are assigned by sampling without replacement, and we do not require the variance of √ N · w(X) T θ to be non-vanishing.
Letβ adj denote the estimatê and let a(X) ∈ R and v(X) ∈ R N be given by (S.14) and let σ 2 u be given by Then the variance of v(X) T θ is given by is asymptotically normal distributed.
The proof of Lemma 3 will use the Azuma-Hoeffding (or McDiarmid's) inequality (Boucheron et al., 2013, Thm 6.2), which states that given independent variables X = (X1, . . . , XN ), and a function satisfying the bounded difference property i . We first prove Proposition 3, and then give proofs for Lemmas 3, and 4.
Proof of Proposition 3. Let σ 2 u be defined as in the statement of Lemma 4, and divide the sequence of experiments assumed by Proposition 3 into two subsequences: (i) those for which σ 2 u > N −1 1 log N , and (ii) those for which σ 2 u ≤ N −1 1 log N . Let a and v abbreviate a(X) and v(X). To prove the proposition, we will show that the probability that av T θ exceeds the upper bound of the prediction interval is asymptotically bounded by α for both subsequences (i) and (ii). For subsequence (i), this probability satisfies where (S.15) follows from Slutsky's theorem as a/ā →p 1 by Lemma 3, and converges in distribution to a standard normal by Lemma 4, and hence their product is asymptotically normal as well. We now show the same for subsequence (ii). Let rn = (log N ) 2 /N 2 . It holds that where (S.16) follows from Slutsky's theorem as a/ā →p 1 by Lemma 3, and by Chebychev's inequality as rn Var(v(X) T θ) for subsequence (ii), implying that their product converges to zero as well.
Combining (S.15) and (S.16) implies that for both subsequences (i) and (ii). Substituting av T θ =β adj − β adj , and and hence that β adj ≥β adj − U with probability at least 1 − α + o(1) as well. This is the lower bound of the PI for β adj . The proof of the upper bound proceeds analogously.
Proof of Lemma 3. We will couple X with a vectorX ∈ {0, 1} N whose entries are i.i.d. Bernoulli(N1/N ). To do this, letÑ1 denote the number of selected units inX,Ñ and let X be generated fromX in the following manner. IfÑ1 > N1, randomly sampleÑ1 − N1 entries without replacement from {i :Xi = 1}, and change their values to 0; ifÑ1 ≤ N1, randomly sample and alter N1 −Ñ1 entries from {i :Xi = 0} in likewise fashion. The resulting vector has exactly N1 entries equal to 1, and is uniformly drawn from the set of all such vectors; hence, the resulting vector has the required distribution for X.
To prove the proposition, we will show 3 steps. First, we show that b satisfies a bounded difference property, so that if x and x are vectors in {0, 1} N differing in a single entry, then Second, we will use (S.18) to show that a(X) =ā(1 + oP (1)).

(S.19)
Third, we will show that a(X) = a(X)(1 + oP (1)). (S.20) Together (S.19) and (S.20) imply that a(X) =ā(1 + oP (1)), proving the claim. We first show (S.18). It can be seen that Z = AX, and that the vector v(X) can be written as where we have used the identity that (I − P ) T (I − P ) = I − P when P is a projection matrix. Letting X = X + δ, it thus follows that For X and X differing in only one entry, δ is equal to the vector of all zeros except one entry equal in [−1, 1], and it follows that which proves (S.18). Here we have used that A has maximum in-degree and out-degree dmax, and that the entries of v(X) are bounded by dmax/N . We next show (S.19). Using the bounded difference property (S.18), the Azuma-Hoeffding inequality implies that which implies that b(X) →p Eb(X). Using this with Eb(X) = Ω(1) and a(X) = 1/b(X), it follows that a(X) =ā(1 + oP (1)). This shows (S.19). We finally show (S.20). We observe that since EÑ1 = N1, Heoffding's inequality implies that which implies that X − X 1 = op( √ N log N ). Hence by the bounded difference property (S.18) it holds that |b(X) − b(X)| = oP (1), and hence by continuity that a(X) − a(X) = oP (1) = oP (a(X)) as well, proving (S.20). This completes the proof of the lemma.
Proof of Lemma 4. We begin with the observation that This can be seen to equal the average of N1 units sampled without replacement from u1, . . . , uN , and thus has variance It can be seen that

C Summary Information for Data Sets
Here we give tables to summarize the simulated cholera trial outcomes released by Perez-Heydrich et al. (2014), insurance takeup by farmers in the experiment of Cai et al. (2015), and wristband-wearing decisions made by students in the school interventions described in Paluck et al. (2016). An aggregate table of the actual outcomes for the cholera trial is given by   3 shows that the actual population is much larger than the simulated data set (N =74K vs 1.7K), and has much lower rates of cholera incidence (0.003 vs 0.17). As the simulated outcomes were fit to the actual data as a function of treatment (including neighborhood vaccination) and observed covariates (age and distance to water), we speculate that the covariate distributions were shifted to a higher-risk subpopulation. Perez-Heydrich et al. (2014) gives some information regarding the simulation parameters, stating that the outcome for unit j in neighborhood i was determined by a logistic regression model log oddsP (Yij = 1) = 0.5−0.788a−2.953αi−0.098Xij1−0.145Xij2+0.35aαi, where a is the unit treatment; αi was the neighborhood vaccination rate if j's treatment equals a; Xij1 and Xij2 denote j's age (in decades) and distance to the nearest river (in km), which were randomly generated. Treatments were assigned i.i.d. Bernoulli(2/3). Units were generated by simulating the covariate X, and then selecting units to participate in the trial by a logistic regression model log oddsP (participate ij ) = 0.2727 − 0.0387Xij1 + 0.2179Xij2 + bi, where bi is a random neighborhood-level effect. Table S6 gives summary statistics for the experiment of Cai et al. (2015). In this experiment, units were randomized not only by first or second round and by high or low information, but also whether or not the second round units were shown a list of names corresponding to people who had purchased the insurance product in the first round. When studying the effects of informal communication between rounds, the analysis of Cai et al. (2015) is restricted to the "no info" group which excludes those units who were shown such a list, and we follow their example in our analysis as well.

Exposure
Insurance Takeup Table S7 gives summary statistics for the experiment of Paluck et al. (2016). For this experiment, the analysis of the wristband outcomes in Paluck et al. (2016) and Aronow and Samii (2017) restricts to units who had positive probability of being assigned to one of the four treatment outcomes that were considered, meaning that they were eligible units with at least one eligible friend, and we follow their example in our analysis as well.