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A Design-Based Approach to Testing and Inference in (Quasi-)Experiments with Spillovers
Economic policies can generate effects far beyond their direct targets. Because economic agents are embedded in spatial, market, and social networks, shocks may propagate through prices, local labor markets, commuting and shopping patterns, and social interactions. Classical analyses of social multipliers in economics emphasize that such spillovers can amplify or attenuate policy impacts in important ways (e.g., glaeser2003social,mani2013poverty). More recently, a growing body of experimental and quasi-experimental work in development and spatial economics has made spillovers the primary object of interest, including studies of large-scale cash transfers, public works, and transport infrastructure miguel2004worms,donaldson2016railroads,egger2022general,muralidharan2023generaleq,franklin2024urban,walker2024slack.
Despite this interest, spillovers pose econometric challenges. Unlike the standard no-interference setting (where each unit's outcome depends only on its own treatment), spillovers mean that unit $i$'s outcome can depend on many, or even all units' treatments. Whereas under the standard assumption each unit has only a small number of potential outcomes (e.g., two in the binary-treatment case), with spillovers the number of potential outcomes can be very large (e.g., $2^n$ in the binary case), since each of the possible assignments can in principle produce a different outcome for that unit.
Applied work typically makes the problem tractable by replacing the full assignment vector \(W\) with a low-dimensional exposure mapping \(g(W;X_i,\theta)\) Manski2013TreatmentResponse,AronowSamii2017\footnote{An alternative is to restrict interference to small, known groups (partial interference; e.g., households or dorm rooms), the special case in which the exposure map reads only own-group assignments. We focus on the general case because our applications feature market- and space-mediated spillovers that may cross such groupings.}. The vector \(W\) collects all units' treatment statuses, \(X_i\) contains baseline covariates such as networks or commuting flows, and \(\theta\) parameterizes features of the mapping, such as a distance radius or elasticity parameter. Examples include ring or neighborhood averages miguel2004worms,egger2022general and smooth spatial-decay kernels such as gravity or market-access measures redding2004economic,donaldson2016railroads,franklin2024urban.
This approach raises two key challenges. The first is the choice of the map structure \(g\left(W ; X_i, \theta\right)\). Often economic theory does not provide an exact functional form for this map beyond broad guidance, such as the idea that spillovers should decay with distance (in space, in a network, or along trade and commuting links). Reflecting such ambiguity, even in closely related empirical settings, different researchers make very different choices among these constructions. For example, in large-scale anti-poverty programs in low-income countries, researchers studying settings with very similar institutional features choose different exposure map functional forms egger2022general,franklin2024urban,walker2024slack.\footnote{egger2022general study large cash transfers in rural Kenya and proxy local spillovers by per-capita transfers within distance bands around each market (“distance buffers”). franklin2024urban evaluate an urban public-works program in Addis Ababa and, to capture spillovers across neighborhoods, combine a spatial-equilibrium model with commuting data so that exposure is mediated by the commuting network rather than by geographic distance alone. In related Kenyan data, walker2024slack construct gravity-style “shopping network” exposure indices that weight village-level activity by baseline shopping flows from villages to markets, and compare the performance of these network-based measures to buffer-style measures of spatial exposure in explaining cross-market inflation walker2024slack.} Even within a single paper, researchers often report multiple exposure constructions and informally compare them donaldson2016railroads,muralidharan2023generaleq.\footnote{For instance, muralidharan2023generaleq take as their main specification a ring-based exposure measure, given by the treated share of units within a 20 km radius of each location, but also show in their Appendix B that similar results obtain when exposure is measured using a market-access-style kernel. Likewise, donaldson2016railroads summarize the impact of the nineteenth-century U.S.\ railroad network through a market-access index, but Appendix Table 3 reports estimates under a range of alternative exposure maps: they redefine market access using different measures of “market size” (population versus county wealth) and restrict the set of trading partners (for example, only counties beyond certain distance thresholds, only urban counties, only major cities, or only New York City).}
Second, even given a particular functional form for the exposure mapping, empirical researchers must still select \(\theta\) and account for the uncertainty this choice introduces into downstream policy estimates. For example, egger2022general note that they “had no a priori knowledge of the relevant distances over which general equilibrium effects might operate\ldots”. In practice, applied papers often report results for several plausible values of \(\theta\), or select a preferred specification using model-selection criteria or informal diagnostics currie2015toxicplants,donaldson2016railroads,egger2022general. Yet standard errors and confidence intervals typically condition on this choice, treating \(\theta\) as fixed rather than as a source of estimation uncertainty.\footnote{In egger2022general, local price changes are regressed on exposure measures defined over multiple distance buffers, with the outer radius chosen by a Schwarz/Bayesian information criterion; the selected 0--2 km band is then used as the main exposure definition in the reduced-form analysis egger2022general. currie2015toxicplants estimate effects within several distance bands around polluting manufacturing plants and report alternative distances, but focus on a preferred near/far comparison, 0--1 versus 1--2 miles, guided by atmospheric dispersion evidence currie2015toxicplants. donaldson2016railroads recompute market access under alternative trade elasticities as robustness checks donaldson2016railroads. In each case, variation across \(\theta\) is treated as specification analysis rather than propagated into sampling uncertainty.}
To address these challenges in choosing and calibrating exposure mappings, this paper develops a design-based framework for testing and estimating exposure mappings in settings with spillovers. A key difficulty in such settings is that correctly specifying the outcome model is especially challenging given the complex dependence induced by spillovers. We adopt a design-based approach that sidesteps this by treating potential outcomes as fixed for the experimental sample and letting all randomness come from the known assignment mechanism; this randomization serves as the key assumption needed to test and conduct inference on the exposure mapping. Starting from a proposed exposure map $g(W; X_i, \theta)$, we develop tools to (i) test whether the implications of this map are consistent with observed outcomes under the known assignment mechanism and (ii) estimate the tuning parameters $\theta$. To quantify uncertainty, we develop a design-based law of large numbers and central limit theorem for GMM estimators under spatial and network dependence, characterize an efficiency bound and optimal moments within the class of design-based estimators, and propagate the resulting exposure-map uncertainty into downstream policy estimands.
Formally, we work with a known randomized (or quasi-randomized) assignment design \(\mathcal{D}_n\) and a proposed exposure map \(g(W;X_i,\theta)\). A key observation is that a correctly specified exposure mapping implies an exposure sufficiency property: there exists a true parameter \(\theta_0\) such that potential outcomes depend on the full treatment assignment vector only through the exposure mapping \(g(W;X_i,\theta_0)\), so that conditional on \(g(W;X_i,\theta_0)\) the remaining details of \(W\) carry no additional outcome-relevant information. This property implies a large set of orthogonality conditions between outcomes and functions of \(W\), which we construct via what we call design-side residuals. Given any integrable outcome transformation \(\phi\) and design function \(\psi\), we orthogonalize \(\psi(W)\) with respect to the exposure mapping by subtracting its conditional expectation given \(g(W;X_i,\theta)\) BorusyakHull2023, and for each unit \(i\) define the design-side residual \( R_{i,\theta}{\psi}(W) := \psi(W) - \mathbb{E}\big[\psi(W)\mid g(W;X_i,\theta)\big], \) where the conditional expectation is taken with respect to \(\mathcal{D}_n\), and thus can be computed by repeatedly sampling from the known design. Under exposure sufficiency and (quasi-)random assignment, we show that at the true parameter these design-side residuals are orthogonal to any function of unit $i$'s outcome: \( \mathbb{E}\big[\phi(Y_i)\, R_{i,\theta_0}{\psi}(W)\big] = 0 \) for every \(\phi\) and \(\psi\). Varying \((\phi,\psi)\) generates a family of moment conditions that form the basis for GMM estimation; when the system is overidentified, the associated \(J\)-test assesses whether the proposed exposure mapping is consistent with the design. In this way, a single design-side residualization strategy supports both of our key objectives: evaluating the fit of a proposed exposure map and learning about the tuning parameter \(\theta_0\) from the data.
For inference, we establish consistency and asymptotic normality of the design-based GMM estimator under spatial and network dependence. We work in the affinity-set dependence framework of chandrasekhar2023general, which nests classical structures such as mixing random fields, m-dependence, and dependency graphs as special cases. Existing results in this framework are pointwise; to our knowledge we are the first to establish uniform consistency and asymptotic normality in it, and we give primitive conditions that cover both smooth exposure maps (gravity and market-access kernels) and non-smooth ones (the ring radius). We also characterize efficiency within this moment class: there is an asymptotic-variance lower bound for any moment the framework constructs, and a feasible sieve attains it.
Finally, we carry the resulting uncertainty about $g(W; X_i, \theta)$ into downstream policy estimands (e.g., average effects under counterfactual assignment rules) so that inference reflects both the experimental variation and uncertainty about the exposure specification itself.
We illustrate the framework in two applications to large-scale anti-poverty programs in development economics: the large-scale public-works reform in rural India analyzed by muralidharan2023generaleq, and the GiveDirectly cash-transfer experiment in rural Kenya studied by egger2022general together with the follow-up structural analysis of walker2024slack. Both study large interventions in low-income economies, are explicitly motivated by general-equilibrium spillovers, involve spatially linked local markets, and rely primarily on ring-based exposure mappings.
The two applications yield contrasting conclusions. In the muralidharan2023generaleq application, the design-based overidentification tests do not reject their ring specification, and the estimated radii broadly support the original 20 km labor-market scale for the main income outcomes. In the egger2022general application, by contrast, the ring specification is rejected for several core outcomes, and our support diagnostics reject the original 2 km radius for all outcomes, with the smallest non-rejected supports often being 4--6 km or larger. This pattern is consistent with the follow-up analysis of walker2024slack, which argues that very local rings can miss market-level ambient spillovers that are common to households within local markets. Consistent with this narrative, we obtain a local fiscal transfer multiplier of 1.57, which is smaller than egger2022general's original 2.5, and much closer to the model-predicted multiplier of 1.54 by walker2024slack.
Together, these applications illustrate the value of treating exposure mappings as objects of design-based inference rather than fixed researcher choices: the framework can support an economically motivated map, detect and guide revisions when it does not, and propagate the resulting uncertainty into policy-relevant estimates.
\paragraph{Design-based uncertainty.} We adopt a finite-population, design-based perspective in which $\{Y_i(\cdot),X_i\}_{i=1}^n$ are fixed and randomness arises only from the assignment mechanism. This tradition traces to Neyman1923 and motivates modern distinctions between design-based and superpopulation uncertainty in regression and experimental analyses AbadieAtheyImbensWooldridge2020. Beyond fully randomized designs, RambachanRoth2025 develop a design-based theory of uncertainty for canonical quasi-experimental estimators when treatment propensities can vary across units, and LiDing2017 provide finite-population central limit theorems yielding $\sqrt{n}$-Gaussian approximations under randomization-based dependence. Our contribution operates within this design-based framework but targets moment conditions implied by exposure-sufficiency restrictions for parameterized exposure mappings, under the cross-unit dependence induced by interference.
\paragraph{Interference and exposure mappings.}
Foundational potential-outcomes treatments of interference include Sobel2006 and HudgensHalloran2008. Building on this tradition, AronowSamii2017 formalize exposure mappings and develop randomization-based estimators for causal effects under general (but specified) interference structures, while SavjeAronowHudgens2021 clarify large-sample behavior of conventional estimators under unknown interference and show that standard variance formulas can fail. Leung2022ANI allows treatments assigned to increasingly distant units to have smaller but nonzero effects under approximate neighborhood interference. Recent work also studies what can and cannot be learned about interference structure from the design itself: GaoHarshawSavjeWang2026 show that no specification test can have uniform power against any richer exposure-mapping alternative to an exposure-mapping model\footnote{See Remark (ref) for detailed discussion.}, while Zhong2025Unconditional develops finite-sample randomization tests for the existence and extent of interference (for example, whether spillovers vanish beyond a given distance) under minimal assumptions on the network. Complementary work emphasizes robustness to unknown spillover mechanisms within broad classes and studies estimators (and sometimes designs) with minimax or neighborhood-adaptive guarantees; see belloni2022neighborhood and faridani2024linear. Our approach is complementary to these robust and testing-based methods: rather than remaining fully agnostic about structure or testing a partially sharp no-spillover null, we take the parametric exposure maps used in applied work (e.g.,\ ring, gravity, market-access) as maintained and use the known design to (i) estimate the tuning parameter $\theta_0$ and (ii) test the associated exposure-sufficiency restrictions via overidentifying, design-implied orthogonality conditions.\footnote{A further complementary literature asks how exposure-based estimands should be interpreted when the researcher's chosen exposure mapping is misspecified. Savje2024Misspecified separates the use of an exposure mapping to define an estimand from the assumption that the mapping captures the complete causal structure, and establishes conditions under which exposure effects remain estimable under misspecification. ParkYang2026 instead take the marginal policy effect as primitive and show that a researcher-chosen exposure mapping induces a pseudo-true outcome model and a corresponding decomposition into direct and spillover components.}
\paragraph{Testing models with trusted shocks.} A line of work going back to Lucas1980 views structural models as objects to be disciplined by their responses to shocks with well-understood sources and exogeneity properties. In quantitative trade, AdaoCostinotDonaldson2023 propose IV-based goodness-of-fit statistics that compare a model's predicted response to quasi-experimental tariff shocks with the observed response. We bring this “trusted shocks” logic to spillovers and exposure mappings: the parametric exposure family $g(W;X_i,\theta)$ plays the role of the structured model, a structural restriction on how treatments propagate even in otherwise reduced-form designs, the (quasi-)experimental assignment $W\sim\mathcal{D}_n$ (or $W\sim G_n(\cdot\mid X)$) provides the trusted shock, and the design-implied orthogonality conditions deliver both specification tests for the maintained exposure class and design-based estimators of the exposure parameter $\theta_0$.
\paragraph{Orthogonalization and recentering.} Our design-side residualization builds on a long tradition of orthogonalization in semiparametric and GMM settings, including the partially linear model of robinson1988root and the construction of “orthogonal instruments” in IO AckerbergCrawford2009,AckerbergCrawfordHahn2011,AndrewsBarahonaGentzkowRambachanShapiro2025. Closest in spirit is the recentering approach of BorusyakHull2023 and borusyak2025estimating, who study settings where a known shock design generates a constructed regressor (a formula instrument) and recenter it by subtracting its conditional mean given covariates to obtain orthogonal moments for a downstream causal or structural parameter. Extensions to optimality are provided by BorusyakHull2026Optimal. Whereas that work uses recentering to identify and estimate a downstream parameter given a fixed formula or exposure, we apply the same orthogonalization logic upstream to discipline and test the exposure map itself: we treat $g(W;X_i,\theta)$ as the object of interest and use the known (quasi-)experimental design to identify, estimate, and test $\theta_0$. Relatedly, Ritzwoller2025Spillovers develops reweighting procedures for proximity-exposure regressions using residualized proximity measures to isolate variation orthogonal to alternative mediating channels.
The rest of the paper is organized as follows. Sections (ref)--(ref) develop the framework: identification via design-based orthogonality (Section (ref)), a large-sample theory under spatial and network dependence (Section (ref)), and the efficient choice of moments (Section (ref)). Section (ref) propagates the estimated map into downstream estimands, and Section (ref) presents the two applications.
We observe units $i=1,\dots,n$ (regions, households, or network nodes) and a treatment assignment vector $W = (W_1,\dots,W_n)^\top$ drawn from a known experimental (or quasi-experimental) design $\mathcal{D}_n$ (e.g., complete, Bernoulli, stratified, cluster-randomized, shock-based, etc.).
The assignment takes values in a known support $\mathcal{W}$. Binary treatment, $\mathcal{W}=\{0,1\}^n$, is the leading case, but nothing in what follows requires it: the individual assignment $W_i$ may be multivalued or continuous, as with the per-village transfer amounts in our second application. For each assignment $w \in \mathcal{W}$, unit $i$ has a potential outcome $Y_i(w)$, a function of the entire assignment vector $w$ rather than unit $i$'s own assignment $w_i$ alone; this is what allows unit $i$'s outcome to depend on other units' treatments. The realized outcome is $Y_i = Y_i(W)$.
Let $X_i$ denote observed unit-level information, taking values in a set $\mathcal{X}$, that may be relevant for how assignment affects unit $i$, such as location, network links, strata, or baseline covariates. An exposure map is a function \[ g : \mathcal{W} \times \mathcal{X} \times \Theta \to \mathbb{R}^k, \] with parameter $\theta \in \Theta \subset \mathbb{R}^p$ and $k \ll n$, intended to summarize the aspects of the assignment that are relevant for $Y_i$ through \[ g(W;X_i,\theta). \] When there is no risk of confusion, we use the shorthand notation \[ g_i(W;\theta) := g(W;X_i,\theta), \] and write $g_i(w;\theta)$ for the exposure induced by a nonrandom assignment $w \in \mathcal{W}$.
Throughout, we adopt a finite-population, design-based perspective: the potential-outcome schedule $\{Y_i(\cdot)\}_{i=1}^n$ and covariates $\{X_i\}_{i=1}^n$ for the experimental (or quasi-experimental) sample are treated as fixed (or, equivalently, conditioned upon), and all randomness comes from $W \sim \mathcal{D}_n$.
We write $\mathbb{E}$ and $\mathbb{P}$ for expectation and probability with respect to $\mathcal{D}_n$, conditioning implicitly on this fixed schedule of potential outcomes and covariates. This perspective, as in Neyman1923,AbadieAtheyImbensWooldridge2020,LiDing2017, anchors inference to the specific network, market, or spatial environment actually exposed to the policy, rather than positing a hypothetical superpopulation experiment in which entire economies, including their equilibrium prices, networks, and cross-unit dependence, are repeatedly resampled and subjected to new assignments $W$. Such an experiment is least credible exactly when spillovers are system-wide, since it would then require strong assumptions about how the joint distribution of $\{Y_i(w)\}_{i,w}$ and the broader equilibrium environment vary coherently across draws. The design-based framework is correspondingly most appealing here: taking the realized economy as fixed and the known randomization or shock design as the sole source of uncertainty, it delivers a transparent basis for inference without additional assumptions on the population-generating process.
As a concrete illustration, we document three families of exposure maps that recur in applied work. Let \(d(i,j)\) denote a fixed, nonstochastic distance between units \(i\) and \(j\), where distance may be geographic, travel-time, or network distance.
Across these examples, the role of \(\theta\) is always the same: it indexes how far spillovers reach or how quickly they decay. Table (ref) illustrates the three families.
We now state the two primitive conditions that generate the design-based moment restrictions. The first condition is the usual finite-population randomization condition: the potential-outcome schedule is fixed, and all randomness comes from the known assignment law.
The second condition is the exposure-map hypothesis. It states that, at the correct value $\theta_0$, the candidate exposure map contains all information in the assignment vector that is relevant for unit $i$'s outcome.
Thus Hypothesis (ref) makes the exposure \(g(W;X_i,\theta_0)\) a summary of the assignment for unit $i$: the map is well specified when the exposure captures everything in $W$ relevant to $Y_i$. The goal is to test this restriction and learn $\theta_0$ using the known design \(\mathcal{D}_n\).
Our main result is that, combined with the known design, well specification has an observable consequence. Because the assignment law is known and does not depend on the potential outcomes, conditioning on the exposure removes all dependence between $Y_i$ and the residual variation in $W$. We call this consequence exposure sufficiency. It is what makes the map testable: the design leaves assignment variation that a well-specified exposure must render irrelevant to $Y_i$, and any leftover dependence is evidence against the map.
To see what the theorem requires, and why it can be tested, consider the ring map of Example (ref), where $g(W;X_i,\theta)$ is the treated share of units within radius $\theta$ of unit $i$. Applied researchers already probe this choice informally: one draws rings of half a mile, a mile, two miles, and looks for the radius at which estimated spillovers level off. The design-based restriction makes that intuition precise. Well specification at radius $\theta_0$ says unit $i$'s outcome depends on the assignment only through the within-$\theta_0$ treated share: two assignments with the same share produce the same outcome for $i$, no matter which of those neighbors are treated and regardless of the treatment of any unit beyond $\theta_0$. This is a substantive economic restriction, and it can fail in two ways: a treated unit just outside the radius still affects $i$, or the identity rather than the count of treated neighbors matters. The known randomization turns each failure into something observable. If the ring is correct, then under the design the treatments of units outside radius $\theta_0$ are uncorrelated with $Y_i$ once we condition on the within-ring share; leftover correlation is evidence that spillovers reach past $\theta_0$. This is exactly the equal-to-zero condition that the moments of the following subsection formalize, both to test a candidate radius and to select $\theta_0$.
The ring discussion tested one exposure map with one natural statistic, the treatments of units outside the radius. The conditional independence in Theorem (ref) says much more: any function of the assignment, once purged of what the candidate exposure explains, must be unrelated to any function of the outcome. We encode this with a residual that strips from a design function the part predictable from the exposure. To construct the moments, let \(\psi:\mathcal{W}\times\mathcal{X}\to\mathbb R\) be any integrable design function, possibly depending on the unit's covariates \(X_i\).\footnote{The design residual \(R_{i,\theta}\) below evaluates the design function at the unit's covariates \(X_i\), so the unit-centering enters through the same index \(i\) that \(R_{i,\theta}\) already carries. This covers the leading applied case, in which \(\psi\) aggregates the assignment in a neighborhood of \(X_i\) (for example, population-weighted treatment averages over distance bands around unit \(i\)). To avoid clutter we continue to write \(\psi(W)\), and \(\psi_m(W)\) for dictionary elements, each understood to be evaluated at the relevant unit's covariates inside \(R_{i,\theta}\).} For each unit \(i\) and candidate parameter \(\theta\), define the design residual
where the conditional expectation is taken under the known design \(\mathcal{D}_n\). This residual removes from \(\psi(W)\) the component explained by the candidate exposure \(g(W;X_i,\theta)\).
Two features of the corollary matter for what follows. First, it is agnostic about the map: nothing in (ref) is special to the ring, so the same construction disciplines gravity, market-access, or network exposures, with only $g(W;X_i,\theta)$ changing. Second, the equalities hold at $\theta_0$ for every admissible $(\phi,\psi)$, which is what lets a single strategy serve two ends: matching them identifies and estimates $\theta_0$, while a candidate map that violates them is detectable through the resulting overidentification.
For estimation, fix a finite dictionary of moment-generating pairs \[ \{(\phi_m,\psi_m):m=1,\dots,M\}, \] where each \(\phi_m:\mathbb R\to\mathbb R\) is an outcome transformation and each \(\psi_m:\mathcal{W}\times\mathcal{X}\to\mathbb R\) is a design function. Define the $i$-specific moment contribution
and the corresponding sample moment \[ \eta_{m,n}(\theta) := \frac{1}{n}\sum_{i=1}^n\eta_{m,i,n}(\theta). \] Stacking the \(M\) moments gives \[ \eta_n(\theta) := \bigl( \eta_{1,n}(\theta),\dots,\eta_{M,n}(\theta) \bigr)^\top . \] A design-based GMM estimator is then
where \(\Lambda_n\) is a positive semidefinite weight matrix.
Section (ref) derived design-based moment restrictions implied by exposure sufficiency. We now study the large-sample behavior of GMM estimators and tests constructed from those moments. Our goal is to establish design-based consistency and asymptotic normality of the GMM estimator, and to develop the associated overidentification tests of the exposure-map specification. See Remark (ref) for discussion of exact randomization tests.
To separate the asymptotic argument from any particular choice of moments, we work with a generic finite-dimensional moment contribution \[ \Psi_i(\theta)\in\mathbb R^q . \] In the exposure-mapping application, this vector is obtained by stacking finitely many residualized design moments, \[ \Psi_i(\theta) = \bigl( \eta_{1,i,n}(\theta),\dots,\eta_{q,i,n}(\theta) \bigr)^\top, \qquad \eta_{m,i,n}(\theta) = \phi_m(Y_i)R_{i,\theta}{\psi_m}(W). \] The generic notation lets us state the LLN, consistency, CLT, and asymptotic-normality results once, in terms of the dependence structure induced by the assignment design. These results are then used directly for exposure-map estimation here and for the optimal-moment analysis in Section (ref).
Following the design-based literature (e.g.,\ freedman2008regression,AronowSamii2017), we work with a triangular array of experiments $\{(\mathcal{U}_n,\mathcal{D}_n)\}_{n\geq 1}$, where both the population size $N_n:=|\mathcal{U}_n|$ and the assignment design $\mathcal{D}_n$ are allowed to change with $n$.
For each $n$, let $\mathcal{U}_n=\{1,\dots,N_n\}$ denote the finite experimental population. For each unit $i\in\mathcal{U}_n$ and parameter $\theta\in\Theta\subset\mathbb{R}^p$, let $\Psi_i(\theta)\in\mathbb{R}^q$ be a $q$-dimensional moment vector, with true parameter value $\theta_0$. The array $\{\Psi_i(\theta)\}_{i\in\mathcal{U}_n}$ is generated by the known assignment design $\mathcal{D}_n$, while the potential outcomes and baseline attributes are treated as fixed. The design fixes the distribution of these moments in any given population; the large-sample results below require, in addition, regularity conditions on the dependence the design induces across units, which we impose through the affinity-set structure introduced next.
The sample moment is the normalized finite-population average \[ \bar\Psi_n(\theta) := \frac{1}{N_n}\sum_{i=1}^{N_n}\Psi_i(\theta), \qquad \mu_n(\theta) := \frac{1}{N_n}\sum_{i=1}^{N_n}\mathbb{E}[\Psi_i(\theta)]. \] Let $\Lambda_n$ be a symmetric positive semidefinite $q\times q$ weight matrix with $\Lambda_n\stackrel{p}{\to} \Lambda\succeq 0$, and define the quadratic GMM criterion \[ Q_n(\theta) := \bar\Psi_n(\theta)^\top \Lambda_n\,\bar\Psi_n(\theta), \qquad \hat\theta_n \in \arg\min_{\theta\in\Theta} Q_n(\theta). \]
In the limit, write
whenever the limit exists. In particular, we assume that the limit is centered at the true parameter, $ \mu(\theta_0)=0$.\footnote{ This centering follows directly from the design-based orthogonality result in Corollary (ref).}
To accommodate design-induced spatial or network dependence, for each $i\in\mathcal{U}_n$ we fix an affinity set $A_i\subseteq\mathcal{U}_n$ with $i\in A_i$ collecting units whose assignments may have non-negligible covariance with that of unit $i$. We write $|A_i|$ for its cardinality and allow arbitrary dependence within $A_i$. In the spatial examples, $A_i$ can be read as a growing geographic or travel-time ball around unit $i$; in the market-access and gravity examples, it collects locations whose assignment shocks receive non-negligible kernel weight for $i$; and in the network examples, it corresponds to a local graph neighborhood whose radius may grow slowly with $N_n$. Outside $A_i$ we do not impose conditional independence; instead, we only assume that the aggregate covariance contribution from $\{j\notin A_i\}$ is asymptotically negligible relative to the contribution from within $A_i$.
Define centered variables \[ Z_{i,n}(\theta) := \Psi_i(\theta) - \mathbb{E}[\Psi_i(\theta)], \qquad \bar Z_n(\theta) := \frac{1}{N_n} \sum_{i=1}^{N_n} Z_{i,n}(\theta) = \bar\Psi_n(\theta)-\mu_n(\theta), \] and the within-affinity covariance matrix\footnote{We take the affinity relation to be symmetric ($j\in A_i\Leftrightarrow i\in A_j$), so that $\Omega_n(\theta)$ is symmetric; this holds in all our examples (metric or travel-time balls, symmetric kernels, undirected graph neighborhoods), and any directed relation may be replaced by its symmetrization $\{j:j\in A_i\ \text{or}\ i\in A_j\}$.} \[ \Omega_n(\theta) := \sum_{i=1}^{N_n} \ \sum_{j \in A_i} \ \operatorname{Cov}\!\big(Z_{i,n}(\theta),\, Z_{j,n}(\theta)\big) \in \mathbb{R}^{q \times q}. \]
We first state the high-level ULLN and identification requirements. The following subsection then explains how the ULLN is verified under primitive conditions in the two leading cases.
Assumption (ref) is stated at a high level in terms of the population map $\mu(\theta)$ and the sample map $\bar\Psi_n(\theta)$. The next result shows that these high-level conditions are sufficient for consistency.\footnote{Genuinely discrete exposure parameters (for example, an integer hop-count) are handled by a separate finite-grid selection argument in Appendix (ref).}
Consistency was established above under the high-level uniform law of large numbers assumed in (ref), \[ \sup_{\theta\in\Theta}\bigl\|\bar\Psi_n(\theta)-\mu_n(\theta)\bigr\|\stackrel{p}{\to} 0 . \] This subsection gives primitive conditions under which that uniform law holds. The smooth case follows from a standard argument; the ring needs care, because its sample path is a step function of the radius $\theta$ and the smooth-GMM argument does not apply. We verify it for the two exposure maps used in the applications, continuing Examples (ref) and (ref); Appendix (ref) states the primitive conditions more formally and gives the proofs.
\noindentExample (ref) (smooth spatial decay), continued.\ \ignorespaces When the weights $a_{ij}(\theta)$ vary smoothly with $\theta$, as in the gravity and market-access kernels, the moment vector is Lipschitz in $\theta$ and a standard covering argument applies. The condition that is not automatic concerns the design projection $m_{i,m,\theta}(s):=\mathbb{E}[\psi_m(W)\mid g_i(W;\theta)=s]$, which must itself vary regularly in both arguments, \[ \bigl|m_{i,m,\theta}(s)-m_{i,m,\theta'}(s')\bigr| \le M_{i,n}\bigl(\|\theta-\theta'\|+\|s-s'\|\bigr), \qquad \frac1{N_n}\sum_{i=1}^{N_n}\mathbb{E}\,M_{i,n}=O(1). \] Smoothness of the exposure map does not by itself deliver this, so we impose the displayed regularity condition directly as a primitive assumption in Appendix (ref).
\noindentExample (ref) (ring exposure), continued.\ \ignorespaces Raising the radius $\theta$ changes exposure only through the units whose distance to $i$ crosses $\theta$, so the sample path $\theta\mapsto\bar\Psi_n(\theta)$ moves in steps and is not differentiable; in place of a smoothness argument, the uniform law rests on a condition on the distances. That condition is the spatial counterpart of the bounded-density requirement familiar from regression-discontinuity and threshold-regression designs, with pairwise distance $d_{ij}$ playing the role of the running variable and the radius $\theta$ that of the cutoff: as a band of radii shrinks, the weighted mass of distances inside it must vanish. Formally, for an interval $I\subset\mathbb{R}_{+}$ of length $|I|$, \[ \lim_{\delta\downarrow0}\ \limsup_{n\to\infty}\ \sup_{|I|\le\delta}\ \frac1{N_n}\sum_{i=1}^{N_n}\sum_{j\ne i} a_{ij}\,\mathbbm{1}\{d(i,j)\in I\}=0, \] with $a_{ij}$ the exposure weights of Example (ref). Moving the radius then shifts only a vanishing share of the moment, so the empirical criterion converges uniformly and its population limit is continuous in $\theta$ even though every sample path jumps.
We now strengthen the LLN conditions above to obtain a CLT and a GMM asymptotic normality result. We retain the finite-population, design-based setup and notation introduced above, and assume Assumption (ref) holds so that $\hat\theta_n\stackrel{p}{\to}\theta_0$ by Theorem (ref).
Asymptotic normality rests on two further ingredients, both imposed at the population level. We state them formally as Assumption (ref) in Appendix (ref) and describe their roles here. The first delivers a pointwise central limit theorem for the moment vector at the truth. Because the design-based moments are dependent across units through the affinity sets of Section (ref), we invoke the affinity-set central limit theorem of chandrasekhar2023general: under bounded fourth moments, decay of the within-affinity covariances, and a stabilizing aggregate covariance $\Omega_n/N_n\to\Omega$ with $\Omega$ positive definite, the centered moments satisfy $\sqrt{N_n}\,\bar\Psi_n(\theta_0)\Rightarrow\mathcal{N}(0,\Omega)$.
The second ingredient carries this pointwise statement to asymptotic normality of the GMM estimator $\hat\theta_n$. It has two parts: mean differentiability of the population moment map $\mu(\theta)$ at $\theta_0$, with full-rank Jacobian $G$, and stochastic equicontinuity of the centered empirical process $\mathbb G_n(\theta)=\sqrt{N_n}\big(\bar\Psi_n(\theta)-\mu(\theta)\big)$ near $\theta_0$. Both are restrictions on the population map and on the empirical process, not on the individual sample paths $\Psi_i(\theta)$. This is what lets the argument, a Z-estimator application of vaart1996weak to the projected map $\theta\mapsto G^\top\Lambda_n\bar\Psi_n(\theta)$, cover the non-differentiable ring path alongside the smooth gravity and market-access kernels; the affinity-set conditions enter only through the pointwise CLT and the equicontinuity of $\mathbb G_n$.
The statistic $N_n Q_n(\hat\theta_n)$ therefore provides a formal test of the maintained exposure map, as anticipated in Remark (ref): rejection is evidence that residualized assignment variation left over after conditioning on $g(W;X_i,\theta)$ remains predictive of outcomes through the chosen moments. Different finite moment collections yield different $J$-statistics; Section (ref) studies how to choose moments efficiently.
It remains to estimate the asymptotic design covariance matrix \(\Omega\). In our setting $\Omega$ captures spatial and network dependence through the affinity sets, so a natural object is a spatial/graph HAC estimator built from $\{Z_{i,n}\}_{i\le N_n}$. Rather than spell out primitive conditions for a particular estimator, we impose a high-level consistency requirement in the spirit of spatial and network HAC methods, and refer to the existing literature for sufficient conditions. For spatial dependence, see Conley1999,KimSun2011. For general network dependence and $\psi$-dependent processes on graphs, KojevnikovMarmerSong2021,sasaki2025gmm provide LLN, CLT, and consistency results for a closely related network HAC estimator. We formalize our requirement as follows.
Sections (ref)--(ref) introduced a class of design-based moments parameterized by an outcome transformation $\phi$ and a design function $\psi$, \[ \eta_{\phi,\psi,n}(\theta) := \frac1{N_n}\sum_{i\in\mathcal{U}_n} \phi(Y_i)\,R_{i,\theta}\psi(W). \] Two facts delimit what optimality within this class means. First, the class is exhaustive at the unit level: Appendix (ref) shows that the collection of these moments over all bounded measurable $(\phi,\psi)$ is equivalent to the exposure sufficiency $Y_i \perp\!\!\!\perp W \mid g(W;X_i,\theta_0)$. Second, a correctly-specified exposure map also implies cross-unit restrictions, involving pairs or larger sets of units (Remark (ref)), which lie outside this class and are not exploited. The bound below is therefore an efficiency bound within the unit-level moment class, the class containing the moments used in applied work and in our applications, not a semiparametric bound over all implications of an exposure map hypothesis.
For empirical work the implication is that fixing a finite dictionary and running two-step GMM with an estimated covariance matrix is both standard and, as the dictionary grows, asymptotically efficient within the class.
Stage 1 learns the exposure map $g(W;X_i,\hat\theta_n)$. In most applications, the object of ultimate interest is a downstream exposure--response or policy parameter, such as the coefficient from an outcome regression on the learned exposure index. This section states the main implication for such second-step inference.
The main case is a regular exposure-map parameter $\theta\in\Theta\subset\mathbb{R}^p$ estimated in Stage 1. Since $\hat\theta_n$ is an input into the downstream exposure--response equation, the sampling uncertainty in $\hat\theta_n$ must be propagated into second-step inference.
For concreteness, consider the linear exposure--response projection. Define \[ Z_i(\theta):=
. \] The target $(\alpha_0,\beta_0)$ is the design-based projection coefficient satisfying
A correctly specified linear conditional mean is sufficient for (ref), but the projection interpretation does not require it.
Collect the regular parameters as \[ \zeta=(\theta^\top,\alpha,\beta^\top)^\top . \] The two-step estimator is characterized by stacking the projected Stage 1 GMM equation with the Stage 2 exposure--response equation: \[ G_1^\top\Lambda_{1,n}\bar\Psi_{1,n}(\hat\theta_n)=o_p(N_n^{-1/2}), \qquad \bar\Psi_{2,n}(\hat\theta_n,\hat\alpha_n,\hat\beta_n)=o_p(N_n^{-1/2}). \] Under a joint affinity-set CLT, mean differentiability of the stacked population map, and stochastic equicontinuity, Appendix (ref) shows that \[ \sqrt{N_n}(\hat\zeta_n-\zeta_0) \Rightarrow \mathcal{N}(0,V_\zeta), \] where $V_\zeta$ is the corresponding design-based sandwich covariance matrix. Inference for the exposure--response coefficient $\beta_0$ uses the $(\beta,\beta)$ block of $V_\zeta$. More general low-dimensional Stage 2 moments, including nonlinear regressions or policy-functional estimating equations, are handled by the same stacked-system argument.
This section applies the framework to two large-scale anti-poverty programs in development economics that explicitly study general-equilibrium (GE) effects: (i) the Smartcards reform of India's National Rural Employment Guarantee Scheme analyzed by muralidharan2023generaleq; and (ii) the GiveDirectly cash-transfer experiment in rural Kenya studied by egger2022general, together with the follow-up structural analysis of walker2024slack.
The two settings are chosen to be similar ex ante, but we find that they yield contrasting conclusions. Both applications follow the same two-stage structure: Stage 1 estimates the exposure map from the design-based moments and tests it against the randomization; Stage 2 re-estimates the authors' original outcome equations with the estimated map in place of their fixed one, propagating the Stage-1 uncertainty.
We begin with the general-equilibrium effects of India's National Rural Employment Guarantee Scheme (NREGS) studied by muralidharan2023generaleq. The program guarantees up to 100 days of public employment per year to rural households. muralidharan2023generaleq exploit a large randomized rollout of biometric “Smartcards” that improved the implementation of NREGS at the mandal level, and combine direct effects on treated mandals with spillovers to nearby untreated areas.\footnote{Administrative units nest as district $\supset$ mandal $\supset$ Gram Panchayat (GP): a mandal is a sub-district (average population roughly 62,500 in the study sample), and a GP is a village-cluster government comprising one or more census villages. Treatment was randomized at the mandal level, outcomes are measured at the GP (or household) level, and spatial exposure is computed from geocoded 2001 Census village locations muralidharan2023generaleq. Our Stage 1 below implements the exposure measure at the census-village level; see Appendix (ref).}
\paragraph{Ring-based exposure measure.} In their main specification (their equation (1)), muralidharan2023generaleq estimate regressions of the form
where $Y_{pmd}$ is an outcome such as NREGS earnings, wage-labor income, or total income for Gram Panchayat (GP) $p$ in mandal $m$ and district $d$, $T_m$ is the Smartcard treatment indicator for mandal $m$, and $X_{pmd}$ are controls. The key spillover variable $\mathrm{NR}_{pmd}^{20}$ is the share of GPs in other mandals within 20 km of $p$ that were assigned to treatment; it is a ring-based neighborhood-treatment measure constructed at the GP level using geographic distance, an instance of the ring exposure map of Example (ref) with radius $\theta = 20$ km.
The headline finding of muralidharan2023generaleq is that 86% of beneficiary income gains came from non-program earnings: from higher private-sector wages and employment rather than from NREGS payments themselves, with statistically significant spatial spillovers of wages and employment onto nearby areas.
The authors fix the radius defining $\mathrm{NR}^{20}_{pmd}$ a priori at 20 km, motivated by commuting distances and the geographic scale of local labor markets, rather than estimate it or test it against the design.
\paragraph{Stage 1: letting the data choose the radius.} We apply the Stage 1 design-based GMM procedure of Sections (ref) and (ref), taking the ring radius as the tuning parameter $\theta$. The exposure measure follows muralidharan2023generaleq's construction: for each GP we compute the population-weighted fraction of non-same-mandal treated census villages within radius $\theta$, using the same 6,662-village geometry as the original paper. The design functions are population-weighted annulus averages of the mandal treatment indicator in distance bands around GP $i$, built from the same village-level distance structure as the exposure. Because physical interaction distances vary continuously in space, we treat the radius as a continuous parameter and search over a fine 0.1 km grid. We report Wald confidence intervals justified by the asymptotic normality result and the design-based overidentification ($J$) test of Section (ref). Full technical details (the two-step criterion, Wald interval construction, and overidentification test) are in Appendix (ref).
Table (ref) reports the Stage-1 estimates: the selected radii are 23.7 km for total income, 14.1 km for NREGS earnings, and 25.8 km for wage-labor income. For each outcome the table also gives the Wald standard error and 95% confidence interval for $\hat\theta$, and the overidentification statistic $J(\hat\theta)$ with its $p$-value. The $J$ statistics are small and none is significant at conventional levels ($p = 0.42$, $0.54$, and $0.40$), so at the selected radii the design-based moments give no evidence against the ring specification.
NREGS earnings and wage-labor income decompose total income into a more local and a broader-reaching component (rows two and three of Table (ref)), and they separate in the direction the authors' own mechanism predicts: NREGS earnings, the direct public-employment margin, localize to 14.1 km, whereas wage-labor income, which operates through private labor markets, reaches farther, to 25.8 km.\footnote{muralidharan2023generaleq emphasize that jobcard holders “could only do NREGS work in their own villages,” so the public-employment margin should track local program access; the 14.1 km estimate has a tight 95% confidence interval of [12.8, 15.4] km. In their mechanism for wage-labor income, better NREGS implementation raises reservation wages and propagates through markets they describe as “spatially integrated beyond individual GPs or even mandals.”} The total-income radius, 23.7 km, falls between them.
Figure (ref) plots the Stage-1 criterion against the candidate radius for each outcome, with the dashed vertical line marking the selected radius $\hat\theta$; the criterion is small where the ring's implied design-based moments are close to zero. In all three panels the criterion is high at short radii, falls to a clear interior minimum at the selected radius, and rises beyond it, so the design identifies a finite interaction radius for every outcome. The total-income criterion also has local minima near the two component radii, consistent with total income aggregating a more local and a broader-reaching margin.
Taken together, the exhibits broadly support the exposure choice that muralidharan2023generaleq make on institutional grounds: the ring specification is not rejected for any outcome, and the estimated radius for total income, the headline outcome, is 23.7 km, close to the 20 km they adopt a priori (first row of Table (ref)). The 20 km choice also lies inside the range spanned by the two component radii, 14.1 to 25.8 km.
\paragraph{Stage 2: the income-source decomposition.} Re-estimating muralidharan2023generaleq's outcome equations at the outcome-specific radii leaves their conclusions essentially intact (Table (ref)). Total income ($9344.2$) and wage-labor income ($7627.9$) are approximately unchanged from the 20 km specification; only NREGS earnings move materially, falling from $1294.6$ to $758.7$. muralidharan2023generaleq attribute 14% of the income gain to program earnings and 86% to non-program earnings; the corresponding share computed from the 20 km column of Table (ref) is 13.5%. At the design-based radii the program share falls to 8.1% ($758.7$ of $9344$), so non-program earnings account for roughly 91.9% of the gain (bottom panel of Table (ref)).\footnote{Estimating sources at different radii need not yield shares that sum to one. As an alternative accounting exercise, restricting to the two sources with outcome-specific radii (NREGS and wage labor) gives a program share of 9.0%, of the same small magnitude as the 8.1% in the text.} Their central finding, that the income gains come predominantly from non-program (general-equilibrium) earnings rather than direct program payments, is thus robust to estimating the radius.
The design-based standard errors are close to their fixed-radius counterparts despite additionally propagating the sampling uncertainty in $\hat\theta$, so treating the radius as estimated rather than known does not materially inflate the uncertainty around the decomposition.
egger2022general study the GiveDirectly cash-transfer experiment in rural Kenya, in which treatment was randomized both across villages and, through a second-tier saturation design, across sublocations. The two-tier design generates experimental variation in indirect exposure to transfers at the village and local-market level; this is the variation our Stage 1 exploits below.\footnote{See egger2022general for details on the experimental design and data collection.}
Their main specification relates household outcomes to the amount transferred to the household's own village and to the amount transferred to other villages within 2 km. The 2 km outer radius, the distance beyond which transfers are assumed to have no effect, is selected by a Bayesian information criterion over concentric 2 km distance bands.
The headline finding of egger2022general is a local transfer multiplier of roughly 2.5 (their Table V), together with large positive spillovers onto non-recipient households. The spillover component of that accounting is estimated from the $0$--$2$ km exposure, so the multiplier inherits the support choice; and the support is selected by in-sample predictive fit rather than estimated from, or tested against, the experimental design.
\paragraph{Stage 1: estimating the weights and selecting the support.}
Stage 1 here estimates a richer object than the scalar radius of the previous application: the annulus weights of a linear spillover index, together with its support. Let \[ A_v(W) = \left( T_{v,0-2}^{\neg v}(W), T_{v,2-4}^{\neg v}(W), \ldots, T_{v,18-20}^{\neg v}(W) \right)' \] denote neighboring-village transfer amounts in the ten annuli up to 20 km.
The first of these, $T_{v,0-2}^{\neg v}(W)$, is egger2022general's own $0$--$2$ km spillover variable. For a candidate support $R_m=2m$, the radius beyond which transfers are assumed to have no causal effect on a household, Stage 1 forms the linear spillover exposure index \[ g_v^{(m)}(W;\theta_m) = \sum_{j=1}^{m} \theta_{m,j}T_{v,2(j-1)-2j}^{\neg v}(W), \qquad \mathbf 1'\theta_m=1, \] and estimates $\theta_m$ from the design-based exposure-sufficiency moments.\footnote{The scale of $\theta_m$ is immaterial for exposure sufficiency: replacing $\theta_m$ by $c\theta_m$, with $c\neq0$, only rescales the downstream coefficient on the index. We impose $\mathbf 1'\theta_m=1$ and let the Stage 2 coefficient absorb scale. When $m=1$, this normalization implies $\theta_{1,1}=1$. Thus the 2 km case coincides with the original Egger et al.\ one-ring exposure measure, and Stage 1 has no nontrivial shape parameter to estimate.} In this notation, the exposure map used in Stage 1 is \[ \left( T_v^{\mathrm{own}}(W), g_v^{(m)}(W;\theta_m) \right). \]
The support $R_m$ itself is also selected by the design. The 2 km support is an untested restriction, and the fully flexible 20 km index turns out to estimate the pure-spillover effects too imprecisely to be informative (Figure (ref)); we therefore select the smallest support the design does not reject. Exposure sufficiency makes the support a testable restriction: if the annuli beyond $R_m$ carry no outcome-relevant assignment variation, zeroing their coefficients leaves the design-based moments satisfied, which is the restriction the overidentification test of Section (ref) (Corollary (ref)) evaluates. We test the unrestricted 20 km index against the restricted index that zeroes all annuli beyond $R_m$,
implemented as a likelihood-ratio statistic at each candidate support (reported in the lower panels of Figure (ref)), and select the smallest non-rejected support.\footnote{As a check on post-selection and spatial-dependence concerns, the diamonds in Figure (ref) report a sublocation-level sample-splitting exercise. We split at the level of sublocations (the higher administrative tier at which the saturation design randomizes treatment intensity, each containing many villages and a local market) rather than at the village or household level: because cash-transfer spillovers operate through the local market walker2024slack, dependence is contained within a sublocation and is approximately negligible across them, so assigning whole sublocations to the selection and estimation subsamples makes the two approximately independent while leaving the within-sublocation spillovers the exposure map captures intact. We aggregate across repeated splits following the median procedure of chernozhukov2025fisher: we report the median point estimate across splits and form the band from the median lower and median upper confidence limits, yielding an approximately $90\%$ interval. The split estimates are noisier but point the same way: $2$ km is too local and the selected supports are modestly larger.} This is the same parsimony goal behind the Bayesian information criterion egger2022general use to set their outer radius; the difference is that the BIC scores cross-sectional predictive fit, whereas the design-based test scores consistency with the randomization, the identifying assumption the downstream estimates rely on.\footnote{egger2022general choose the radius $r$ by minimizing $\mathrm{BIC}(r)=N\log\hat\sigma_r^2+k(r)\log N$, where $\hat\sigma_r^2$ is the residual variance from regressing $Y_i$ on the radius-$r$ ring exposures and controls, $k(r)$ is the number of parameters, and $N$ is the number of villages: the radius is scored by how much the rings reduce residual variance, traded off against the penalty.} The two criteria can disagree: a spillover component that is approximately common to households within a local market is largely absorbed by the intercept and controls, so outer annuli that mainly carry such a component barely reduce residual variance, and a fit criterion prefers short supports even when the beyond-2 km transfers generating that component move the total response.
Figure (ref) traces egger2022general's recipient and non-recipient effects, re-estimated at each candidate support from their 2 km to the fully flexible 20 km: the recipient point estimates are stable across the entire path, while the non-recipient effects attenuate and lose precision until, by 20 km, they are generally no longer distinguishable from zero. The two endpoints anchor the comparison. At $R=2$ km the normalized index collapses to their single $0$--$2$ km ring ($\theta_{1,1}=1$), so the leftmost point replicates the original egger2022general specification; at $R=20$ km the index imposes no support restriction across the ten annuli; each interior point imposes, ex ante, that transfers beyond $R$ km do not affect the household. The contrast between the two paths is what one would expect: recipients respond mainly to the direct, own-village transfer, which does not depend on the support, whereas non-recipients respond only through spillovers, which do. The confidence intervals do not shrink monotonically as the support widens; Appendix (ref), part D, takes up this feature separately.
The lower panel of each plot reports the $p$-value of the support test described above at each candidate support.
The design-based support test rejects the original 2 km support for all three outcomes: in every lower panel of Figure (ref), the $p$-value lies below $0.05$ at 2 km and crosses above it by 4 km. The smallest non-rejected support is $4$ km for household expenditure, assets, and household income; across the broader set of outcomes in Appendix (ref) the selected supports are $4$--$6$ km, occasionally larger. The $2$ km exposure is thus statistically inconsistent with the design. At the selected supports, the overidentification ($J$) test of the estimated linear-index specification (last column of Table (ref)) rejects for expenditure and assets ($p = 0.002$ and $0.001$) and does not reject for income ($p = 0.129$); the rejection is consistent with a spillover component that no annular index spans at any support, a point we return to below.
\paragraph{Stage 2.}
We next estimate egger2022general's original IV specification, given by \[ Y_{iv} = \alpha + \beta_{\mathrm{own},m}T_v^{\mathrm{own}}(W) + \gamma_m g_v^{(m)}(W;\widehat\theta_m) + X_{iv}'\delta + \varepsilon_{iv}, \] replacing their $0$--$2$ km spillover measure with the estimated index $g_v^{(m)}(W;\widehat\theta_m)$ at the selected support, and keeping the same controls and instrumenting logic as the original.\footnote{Standard errors account for the generated weights $\widehat\theta_m$ by the delta method.}
Table (ref) compares egger2022general's original estimates with the design-based estimates at the selected supports. The exposure measure is the only difference between the two columns. The change matters only for the non-recipient effects. The recipient total effects survive the change of exposure map: all three point estimates move by less than half of egger2022general's own standard error. Every pooled spillover, by contrast, attenuates by about one to one and a half of egger2022general's standard errors. Expenditure falls from $334.7$ to $128.9$ and remains significant; income falls from $225.0$ to $81.4$ and is no longer distinguishable from zero at the $5\%$ level; assets, not significant in the original specification, falls from $135.4$ to $41.9$.\footnote{The “Egger IV” column re-estimates the original 2 km specification on our replication sample; the estimates closely match the published Table 1 values (see the table notes).} Relative to the muralidharan2023generaleq application, then, the exposure-map choice does matter here, and it matters for the spillovers rather than for the direct effects.
Recomputing egger2022general's Table V multiplier accounting with the design-selected indexes gives a mean local transfer multiplier of about $1.57$, well below the original headline value near $2.5$ and close to the $1.54$ implied by walker2024slack's calibrated general-equilibrium model (Table (ref)). The expenditure and income components are about $1.60$ and $1.54$. With only $84$ sublocation clusters these multipliers are imprecisely estimated, with standard errors comparable to egger2022general's own; the mean multiplier carries a standard error of $1.12$, so although its point estimate lies well below $2.5$, it is not statistically distinguishable from one.\footnote{Standard errors are delta-method values that propagate both the Stage-1 uncertainty in the index weights and the Table V coefficient uncertainty; Appendix (ref), part E details the reparameterization and the inference.} The walker2024slack benchmark is on the same real (deflated) basis as egger2022general's Table V.
The economics of the setting supports spillovers that reach beyond 2 km. walker2024slack argue that local general-equilibrium responses to the transfers include a market-level “slack” component: part of the response is common to all households trading in the same local market, rather than declining smoothly with distance from the transferred villages. Such a component is consistent with both Stage-1 findings. It gives beyond-2 km transfers real effects on a household's outcomes, which is why the support test extends the support past 2 km; and it is not spanned by an annular index at any support, which is why the $J$ test still rejects at the selected supports.
The second application thus illustrates the revision use of the framework: when the design rejects the original exposure map, both the map and the headline policy estimate change materially.
Estimates of spillover effects depend on an exposure map that turns the realized assignment into an index of each unit's exposure. Both the functional form of that map (e.g., a ring) and its parameter (e.g., the radius) are usually fixed before estimation, with little guidance for either choice. This paper shows that the same randomization that identifies treatment effects can guide both choices. Specifically, a correctly specified exposure map implies orthogonality conditions that can be used for both estimation and testing: design-based GMM can estimate the mapping parameter, and the same conditions, when overidentified, can test the map itself.
We establish consistency and asymptotic normality of the resulting estimator for the maps used in applied work, with all randomness arising from the assignment, and we characterize the efficient moments. Finally, we carry the resulting uncertainty about $g(W;X_i,\theta)$ into downstream policy estimands (e.g., average effects under alternative assignment rules), so that inference reflects both the experimental variation and the uncertainty about the exposure specification itself.
We apply the method to two large-scale anti-poverty experiments. For the NREGS reform studied by muralidharan2023generaleq, the 20 km radius chosen on institutional grounds is not rejected by the design, and the program's headline decomposition is robust: even at the data-chosen radius, the income gains come predominantly from non-program earnings. For the cash-transfer experiment of egger2022general, the 2 km support is rejected for every core outcome, and replacing it with the smallest support the design does not reject lowers the estimated local transfer multiplier (mean) from about $2.5$ to $1.57$, close to the value implied by the independent structural model of walker2024slack.