RESEARCH DOSSIER
Spillovers and Equilibrium Effects in Field Experiments
Abstract. Field experiments intervene in economic systems whose participants share markets, institutions, resources, and information. Random assignment can identify the consequences of an allocation of treatment without identifying the consequences of universal implementation. This monograph studies that distinction through interference between experimental units, randomized treatment saturation, network exposure, market clearing, and the adjustment of institutions at scale. It reconstructs the principal causal estimands, derives their relationships under explicit allocation assumptions, and examines how experimental designs support or limit their identification. Evidence from labor markets in France and India, cash transfers and agricultural markets in Kenya, rural insurance in China, school organization in Kenya, and digital marketplace experimentation illustrates the diversity of spillover mechanisms. The analytical synthesis distinguishes individual gains from changes in aggregate resources, population coverage, and the incidence of equilibrium adjustment. Positive individual effects may redistribute a fixed opportunity; negative effects on untreated units may accompany a socially productive change; local income multipliers may depend on external funding and market boundaries. A policy interpretation therefore requires an explicit allocation counterfactual, a population and market boundary, a time horizon, and an account of resource costs. The monograph is a critical synthesis of primary research and formal illustrative reasoning; it presents no newly estimated field data or claim to a new named theory.
Keywords: Field experiments; treatment interference; spillover effects; randomized saturation; causal inference; general equilibrium; displacement; social networks; market clearing; external validity; policy evaluation; welfare economics
Research object and disciplinary boundaries
A field experiment is an intervention whose assignment is governed by a known experimental design and whose outcomes arise within the ordinary economic environment of the units under study. Its scientific object includes the intervention, the allocation of the intervention, the participants' responses, and the environment through which those responses acquire consequences. The distinction is fundamental because many outcomes recorded for one participant depend on economic choices made by others. A worker competes for vacancies; a farmer learns from neighbors; a trader reacts to suppliers' costs and competitors' prices; a household spends a transfer on goods produced by other households. Each action may become part of another participant's treatment environment.
Interference denotes dependence of a unit's potential outcome on the treatment assignment of other units. A spillover is a causal effect associated with a change in others' assignment or exposure, with the unit's own treatment condition specified. Equilibrium effects arise when behavior, prices, quantities, matching probabilities, institutional rules, or other endogenous variables adjust to the intervention. Interference is a property of the potential outcomes and assignment environment. Equilibrium adjustment is an economic mechanism capable of generating interference. The terms have overlapping but distinct domains. Information transmission can generate interference before prices adjust. Conversely, a policy may alter an economy-wide price level while leaving some individual outcomes insensitive to it.
An experiment estimates a contrast between assignment regimes represented in its design. The target of a policy decision is usually a contrast between feasible implementation regimes. The experimental and policy contrasts coincide when their populations, exposure distributions, mechanisms, and time horizons coincide, or when a defensible transport argument connects them. Changing any one of these elements changes the interpretation of a result. A citywide subsidy, for example, is an allocation of purchasing power across a market. A subsidy assigned to a few isolated purchasers is a different allocation and can have a different effect even when the payment and eligibility criteria are identical.
Three economic distinctions organize the investigation. First, the identity of beneficiaries differs from the creation of resources. An employment intervention may move a participant ahead of competitors in a queue without changing the number of jobs. Second, the scope of transmission differs from the boundary of observation. Customers and sellers outside the sampling frame may absorb part of an intervention's effect. Third, the time profile of adjustment differs from the time profile of treatment delivery. Information may diffuse rapidly, while capital formation, migration, entry, or fiscal adjustment can occur over a much longer period.
These distinctions locate the dossier at the intersection of microeconomics and economic methodology. The microeconomic problem is the dependence of feasible individual decisions and returns on others' decisions. The methodological problem is the identification of relevant causal contrasts when treatment changes that decision environment. General equilibrium theory and welfare economics supply interpretive instruments; the dossier's distinctive object is their connection to field-experimental evidence. A structural market model, a randomized experiment, and a welfare calculation answer related but different questions. The strength of the conclusions depends on keeping those questions visible throughout analysis.
The evidence reviewed here is purposive rather than a systematic meta-analysis. Selected primary studies represent contrasting mechanisms, not a probabilistic sample of all field experiments. Reported findings are attributed to the original researchers and kept within the populations and outcomes they studied. Formal derivations and worked examples are analytical illustrations, with assumed parameters explicitly distinguished from measured quantities.
Historical development of interference and equilibrium analysis
Economic analysis has long treated individual decisions as interdependent through prices, expectations, and social arrangements. Randomized experimentation adds a distinct problem: a known assignment mechanism makes causal comparisons possible, yet the set of potential outcomes may itself be indexed by the entire treatment allocation. The investigator must choose which features of this allocation are substantively relevant.
Manski's (1993) reflection problem establishes an important historical distinction between social behavior responding to peers' behavior, responses to peers' characteristics, and similarities produced by a shared environment. Consider a classroom in which achievement correlates with classmates' achievement. That association can arise through mutual learning, composition, teacher quality, neighborhood selection, or a combination of these. A regression of an individual's achievement on group achievement does not isolate an endogenous peer response without additional identifying structure. Randomizing peer exposure can identify an effect of the assignment, while decomposing that effect into behavioral and contextual channels requires further variation or assumptions.
The potential-outcomes approach extends this concern by defining treatment response over allocations. Manski's (2013) analysis of social interactions examines identification when outcomes depend on the treatment configuration, with the strength of inference depending on restrictions placed on that dependence. The unrestricted allocation-indexed outcome is a useful conceptual starting point: it reveals the number of counterfactuals before the researcher introduces simplifying exposure assumptions. The practical research question is which restrictions are plausible in a specified economic environment.
Hudgens and Halloran (2008) developed causal effects under interference for allocation strategies within groups, making distinct effects for treated and untreated people explicit under a partial-interference assumption. Their terminology provides a way to separate the outcome difference associated with own assignment from the difference associated with group-level assignment strategies. In economics this decomposition is especially valuable because effects on untreated individuals can be of equal policy significance to effects on participants.
Aronow and Samii (2017) formalized general interference estimation by distinguishing the assignment design, the mapping from assignments to exposures, and the causal effects defined over those exposures. A scientist can retain a complex randomized assignment while reducing a very large space of allocation vectors to a substantively interpretable set of exposure conditions. Such reduction entails assumptions about which configurations are equivalent for an outcome. The choice of exposure therefore belongs to substantive economic analysis as well as statistics.
Baird and colleagues (2018) studied the design of randomized saturation experiments, clarifying trade-offs in assigning differing treatment proportions across groups. The extension matters economically because institutions regularly choose coverage rates and because an estimate at one coverage rate may conceal effects arising at another. The theoretical emphasis shifts from identifying a single treatment coefficient to identifying contrasts across experimentally supported allocations.
A complementary strand makes the scale problem explicit. Acemoglu (2010) emphasizes the role of general equilibrium and political economy in interpreting development interventions. Muralidharan and Niehaus (2017) distinguish dimensions of experimentation at scale, including the sampling frame, the number receiving treatment, and the units of randomization. These considerations explain why an individually randomized intervention in a large representative sample may still be a small perturbation of each local market. Replication across many households can improve precision for the same low-saturation estimand without identifying the outcome at national coverage.
The historical development thus connects two intellectual tasks. Causal methodology characterizes the assignment-dependent counterfactual and the conditions needed to estimate it. Economic theory characterizes the transmission of an intervention through behavior and institutions. A field experiment becomes fully interpretable when the allocation contrast and the economic mechanism generating the contrast are brought into the same argument.
Formal premises and causal estimands
Allocation-indexed potential outcomes
Let a finite target population contain N units. For simplicity each unit has a binary assignment z, and the assignment vector is Z = (Z₁, …, Zₙ). Unit i has a potential outcome Yᵢ(z) for each feasible vector z. The consistency condition states that its observed outcome equals the potential outcome under the realized assignment, provided the treatment versions and the observation horizon are adequately specified. Assignment may differ from actual receipt, intensity, or duration.
Without interference Yᵢ(z) depends on zᵢ alone. With interference this compression requires justification. With N binary assignments the full vector has 2ᴺ possible configurations. One observed realization cannot reveal every response. Experimental design and economic restrictions are therefore jointly necessary to identify useful contrasts. Randomization supplies known probabilities over feasible configurations; it cannot create positive probability for configurations excluded by design.
Suppose groups g form a partition, with assignment in one group affecting only outcomes within that group. This is partial interference. It can be an approximation, for instance when locations are separated by high travel costs. Its validity depends on the outcome and horizon: administrative enrollment might be confined to districts, while wages respond to migration across those same districts. The relevant partition is economic rather than merely administrative.
Let p denote a group-level assignment strategy. Write μ₁(p) and μ₀(p) for average potential outcomes under the strategy, conditional on own assignment being one and zero, respectively. With independent Bernoulli assignment at probability p within a group, the distribution of other individuals' assignments is the same under either own status. With complete randomization of exactly k individuals, the number of treated peers differs by own assignment, and the conditional means describe a contrast within that particular allocation strategy. These two designs should not be treated as identical.
For an interior strategy p, define the direct comparison D(p) = μ₁(p) − μ₀(p). For two strategies p and q define the indirect comparison I(p,q) = μ₀(p) − μ₀(q), where the untreated outcome is supported in both regimes. Define T(p,q) = μ₁(p) − μ₀(q), a treated-to-untreated contrast across strategies. It follows by addition and subtraction that
T(p,q) = D(p) + I(p,q).
This identity is arithmetic; its causal interpretation comes from the specified allocation regimes and their identification. A positive D(p) and negative I(p,q) can yield a small total contrast. Equally, a modest direct contrast may coexist with a substantial indirect gain. The definitions are related to the allocation-based causal contrasts in Hudgens and Halloran (2008), with notation specialized here to the analytical examples.
For a population with common assignment probability p, the average outcome under strategy p is
M(p) = p μ₁(p) + (1 − p) μ₀(p).
The overall contrast O(p,q) = M(p) − M(q) satisfies
O(p,q) = pD(p) − qD(q) + I(p,q).
The equality holds when the relevant conditional means exist and the averaging weights describe the same target population. Boundary strategies p = 0 or p = 1 can be compared through their population outcomes without inventing conditional cells that the strategy makes impossible. At full coverage there is no contemporaneous untreated group within the strategy, and μ₀(1) is not identified by observations of that regime alone.
For heterogeneous probabilities pᵢ, group-specific strategies, unequal inclusion probabilities, and sampling weights, the overall effect must instead be defined through the appropriate weighted expectation for each unit. Treating a mean of community means as a population mean changes the target when community sizes differ. Equal weighting of markets is scientifically meaningful when the market is the target unit; weighting by persons is meaningful when the target is average individual welfare or outcome. The weighting decision must precede estimation.
Exposure mappings and identification
Let G describe a network measured before treatment, and let eᵢ = fᵢ(z,G) be an exposure assigned to unit i. Possible exposures include own assignment and the fraction of treated neighbors, the number of informed contacts, or the treatment intensity within an accessible market. The maintained exposure restriction is that allocations yielding the same eᵢ produce the same outcome for i, for the outcome and time considered.
This restriction makes the potential outcomes manageable but can omit relevant identity, distance, strength of ties, or routes of transmission. Two people with three treated neighbors may face different environments if one interacts daily with those neighbors while the other barely sees them. A weighted network exposure can address this difference, but the weights need substantive justification and preferably pretreatment measurement. A network formed after treatment may itself be an outcome of the intervention.
Let πᵢ(e) = Pr(Eᵢ = e) under the known assignment mechanism. For a target set in which πᵢ(e) is positive, the inverse-probability estimator of the mean exposure outcome is
HT(e) = (1/N) Σᵢ 1(Eᵢ = e)Yᵢ / πᵢ(e).
Under consistency and the maintained exposure mapping, the expectation of each indicator divided by its probability equals one. Taking expectations term by term yields E[HT(e)] = N⁻¹Σᵢ Yᵢ(e). Thus the estimator is design-unbiased for the target exposure mean. Subtracting two such estimators identifies their average contrast when both exposures have support for the target population.
Small exposure probabilities can produce highly variable estimates. A normalized Hájek-type estimator trades exact finite-sample unbiasedness for stabilization of realized weights; its use requires attention to the target and sampling behavior. Observations sharing exposure-generating assignments are dependent, and variance calculations require information about their joint inclusion probabilities or defensible approximations. Independent-unit standard errors cannot be justified merely because treatment assignments were generated randomly.
Leung's (2022) approximate neighborhood interference allows for the possibility that distant assignment effects decay instead of disappearing beyond a sharp network cutoff. This is relevant when a village boundary or first-degree connection is an imperfect representation of transmission. Decay is a substantive condition and must be supported by the economic setting; it is not a generic property of any recorded network.
Endogenous equilibrium
Let x collect equilibrium variables, such as prices, wages, production, entry, or matching rates, and let s describe policy intensity. Suppose equilibrium is characterized locally by F(x,s) = 0. If F is differentiable and the Jacobian Fₓ is invertible at the equilibrium, the implicit-function theorem gives
dx/ds = −Fₓ⁻¹ Fₛ.
For an outcome yᵢ(s,x), its derivative along the equilibrium path is
dyᵢ/ds = ∂yᵢ/∂s + (∂yᵢ/∂x)(dx/ds).
The first term is the controlled direct response at fixed equilibrium variables; the second captures the endogenous environmental response. Neither is automatically the randomized direct comparison D(p). In particular, an experimental comparison can already incorporate price or institutional changes common to treated and untreated members of the same market. The distinction prevents substitution of a structural partial derivative for a design-based estimand.
Local differentiability does not guarantee a unique equilibrium globally. Entry thresholds, strategic complementarities, expectations, and institutional constraints can create discontinuities or multiple equilibria. An experiment at one intensity may identify a local equilibrium response without identifying the regime selected elsewhere. Extrapolation across such changes becomes model-dependent, even when the original randomized contrast is internally credible.
Mechanisms and counterexamples
Competition for fixed opportunities
Consider a population of job seekers in a labor market with a fixed supply of jobs, with baseline employment probability 0.4. Assume that the assignment gives a worker a relative advantage of 0.2, and that changes in employment probabilities sum to zero because the number of available jobs is fixed. An illustrative allocation response is
Y(z,s) = 0.4 + 0.2(z − s),
where s is the share treated. These are probabilities, not observations. At s = 0.25, treated workers have an expected employment probability of 0.55, while untreated workers have 0.35. At s = 0.75 the corresponding probabilities are 0.45 and 0.25. In both cases the treated-to-untreated direct difference is 0.20.
The aggregate expectation is sY(1,s) + (1−s)Y(0,s) = 0.4 at every saturation. At universal coverage it is 0.4. Relative to an untreated market the intervention redistributes employment opportunities without creating jobs. This counterexample is compatible with a large internally valid direct effect. The conclusion is derived from the assumption of fixed supply and the specified allocation response.
The welfare consequences remain a separate question. Reallocation can improve matching quality, correct discrimination, reduce unemployment duration for particularly vulnerable workers, or increase aggregate output through better matches. It can also waste resources if the only change is intensified competition for the same opportunity. Employment headcounts alone do not decide among these possibilities. The mechanism directs investigators toward job creation, retention, wage, productivity, displacement, and fiscal cost measures.
Positive complementarities
An equally transparent illustration is an information intervention in which own training improves productivity and others' training increases the value of interaction. Let
Y(z,s) = 10 + 2z + s.
At saturation 0.25, treated units produce 12.25 and untreated units 10.25. At saturation 0.75 the outcomes are 12.75 and 10.75. The direct difference is two in either market. The aggregate value is 10 + 3s, so full treatment raises average output by three relative to zero treatment. The same direct effect can therefore coexist with different aggregate gains when the spillover structure differs.
The illustrative comparison also separates a productivity relationship from a welfare judgment. The units of output must be valued, costs must be counted, and the distribution and opportunity cost of inputs must be established. If training diverts scarce productive labor for a substantial period, net value may differ from the change in observed output.
Price-mediated incidence
Consider a competitive local market with demand D(P,s) = a + δs − bP and supply S(P) = c + dP, where b and d are nonnegative slopes and b+d is positive. Here δ represents a policy-induced increase in demand at a fixed price, and s represents coverage intensity. Market clearing gives
P*(s) = (a−c+δs)/(b+d),
and differentiating yields
dP*/ds = δ/(b+d), dQ*/ds = dδ/(b+d).
With b = 4, d = 6 and δ = 20, a move from zero to full intensity increases the equilibrium price by two and quantity by twelve, provided the linear relationships continue to hold throughout the interval and equilibrium quantities remain feasible. If supply is locally fixed, d = 0, the quantity response is zero and the increase in price is five. These examples show how an identical demand shock produces different incidence depending on supply conditions.
A transfer can improve recipients' purchasing power and increase suppliers' revenues, yet a price increase can harm nonrecipients who purchase the goods. The equilibrium price response depends on import capacity, inventories, production technology, adjustment speed, competing demand, and market power. Price indices must represent the consumption baskets of the populations for whom real outcomes are being measured.
Market opening also changes the accounting boundary. Spending on imported goods may generate benefits outside the study area; a local supplier may source inputs from distant markets; a geographic region may receive income from an external funder. A smaller local multiplier in a highly integrated region could reflect leakage of spending to other regions rather than a smaller total benefit. Local and national multipliers answer different accounting questions.
Strategic and institutional response
Some spillovers arise through endogenous behavior of a party outside the randomized population. A school principal reallocates teachers, a firm changes prices, a platform retrains its recommendation system, a lender alters screening rules, or an employment bureau changes caseworker effort. These actors can amplify or attenuate treatment effects even when direct peer interactions are absent.
If program implementation increases the number of trained teachers but shifts experienced teachers out of untreated schools, a favorable participant effect and an unfavorable spillover can reflect resource reallocation. The mechanism cannot be inferred from the sign alone. Measuring staffing flows, wages, time allocation, and the decision rules of school authorities helps distinguish the channel from direct peer learning. Such measurement is also crucial for interpreting scale: universal coverage may exhaust a pool of experienced staff and induce new training or a decline in quality.
Multiple mechanisms can produce observationally similar results. Positive effects among untreated people may reflect knowledge diffusion, higher labor demand, higher household spending, selection into the observation sample, or altered outcome reporting. Mechanism identification requires a design or evidence capable of separating these pathways. A statistical association between an outcome and a measured mediator is insufficient when treatment changes the mediator and other unobserved determinants of the outcome.
Data and measurement
The population and the economic boundary
The fundamental data object of an interference study is an assignment-linked population embedded in a specified economic environment. A reproducible record identifies the sampling frame, all randomization units, the treatment eligibility rules, dates of assignment and delivery, the treatment status of units, the exposure mapping, the primary outcomes, and the observation windows. When market spillovers are central, data collection extends beyond recipients and follows the relevant prices, transactions, labor demand, and population movements.
A village roster can support randomized assignment at the household level. It cannot by itself establish market closure. Mapping trading partners, school catchment areas, labor commuting, mobile-phone information links, and migration histories can reveal transmission across the administrative boundaries. The relevance of each boundary depends on the mechanism under examination. Researchers should specify both the proposed economic boundary and the empirical information used to evaluate it.
Sampling outside the treatment eligibility frame is particularly important. In an employment experiment, ineligible job seekers may compete for the same vacancies. In a consumption experiment, nonrecipient households may sell goods, supply labor, or purchase goods whose prices rise. Data collection restricted to eligible people supports claims about eligible people; external population effects require an appropriate additional sample or a clearly stated model.
A study can estimate effects per eligible household, per resident, per worker, per firm, or per market. These denominators should never be interchanged casually. Changes in resident population due to migration mean that an average among current residents can differ from an average for the baseline population. A rise in a price index can affect purchasing power differently across income groups. Units of measurement and population definition are therefore integral to the estimand.
Treatment, exposure, and implementation
Assignment records establish the experimentally controlled intervention. Administrative receipt records establish whether and when participants accessed it. Intensity measures establish doses, service quality, treatment duration, and compliance. Network data and market geography establish exposure to other units' assignments. Keeping these classes of records separate preserves the distinction between intent-to-treat comparisons and the treatment actually received.
The study should document crossovers, administrative errors, and anticipatory responses. When implementation delays differ by market, outcomes measured at common calendar dates can combine effects at different durations. When announcements precede delivery, nominal baseline observations may already reflect changed behavior. A treatment-time record permits appropriate cohort comparisons and prevents false precision regarding exposure.
Network surveys present distinctive difficulties. Recall errors create missing or invented links, a cap on nominations removes weaker contacts, and respondents may report more socially salient links after receiving treatment. A baseline network can reduce endogeneity of exposure definition, but it remains a measured representation of relevant relationships. Robustness to alternative justified weightings and geographic buffers can reveal whether a conclusion depends on a fragile exposure definition.
Outcomes and real economic quantities
A program can change the number of transactions, total expenditure, product quality, prices, availability, and composition simultaneously. Nominal revenue is not equivalent to real output. In a cash-transfer study, nominal household consumption and business revenue should be interpreted with suitable prices and attention to inventories and imported goods. A transfer enters recipients' budgets immediately; it is not itself newly produced output. Counting both the transfer and its re-expenditure as production would duplicate accounting components.
For labor markets, earnings can be decomposed into wage rates, hours, days employed, occupational composition, and job duration. Changes in employment status may conceal reduced hours among continuously employed workers. Increased wages may benefit workers while lowering profits or affecting other employment. Wage data should distinguish nominal and real measures, contractual pay and actual receipts, and program wages and nonprogram earnings.
For insurance, enrollment is one outcome within a longer chain. Coverage renewal, claims payment, loss protection, borrowing, investment, and welfare under realizations of risk matter. Information received from a neighbor may affect take-up without improving contract value. For online markets, searches, bookings, listings, seller revenue, platform fees, cancellations, and consumer surplus differ in their exposure to algorithmic and strategic responses.
Statistical provenance
Each extracted quantitative result should retain the original study population, treatment, outcome, unit, denominator, comparison, estimation horizon, and edition. Reported percentages need explicit interpretation: percentage change, percentage-point difference, standard-deviation unit, elasticity, or a ratio. Where comparable uncertainty intervals are unavailable, a synthesis should avoid implying a formal ranking of estimates.
This dossier uses source-level claim verification from accessible original papers, author pages, and publisher or indexed journal abstracts. It does not include individual-level datasets or a replicated meta-analysis. The empirical comparisons consequently serve to distinguish mechanisms and interpretation conditions. They do not measure a pooled average spillover effect for the world economy.
Experimental design and statistical identification
Individual and cluster randomization
Individual randomization is powerful for detecting contrasts within a shared environment. If assignment affects other participants, the resulting estimate describes a comparison under the experimental allocation distribution. It may still answer an important question about eligibility or relative advantage. The limitation appears when the estimate is interpreted as a policy effect across different coverage rates or market equilibria.
Cluster randomization assigns shared treatment status to groups. If clusters are economically self-contained for the relevant outcome, a between-cluster comparison can identify the effect of changing the intervention at group scale. A cluster may contain treatment recipients, untreated residents and firms affected by the same economic environment. Outcomes collected across those groups enable population-level interpretation. Cluster treatment also combines direct and spillover effects unless there is independent variation enabling decomposition.
Design power depends on the number and sizes of randomized clusters and the correlation among their outcomes. For a simple balanced design with equal cluster size m and intracluster correlation ρ, the familiar variance-inflation approximation is 1+(m−1)ρ. With m = 40 and ρ = 0.1 this factor equals 4.9 relative to an independent-observation calculation under the corresponding simplifying assumptions. Saturation experiments with heterogeneous effects and complex network dependence require design-specific precision analysis rather than automatic use of this approximation.
Randomized saturation
A two-stage design first assigns groups to different coverage strategies and then randomizes individuals inside groups according to the assigned strategy. The between-strategy comparison among untreated people measures indirect effects under partial interference and the designated target. The within-strategy comparison among alternatively assigned people estimates direct contrasts at particular exposure levels. The between-strategy comparison of appropriately weighted group outcomes estimates overall effects.
The design requires enough groups at each intensity, sufficient within-group support, and an allocation that reflects scientifically relevant coverage ranges. If no group approaches full implementation, the design does not identify universal implementation directly. Including untreated groups provides a useful baseline, while including fully treated groups assists estimation of total group outcomes. Interior strategies provide the within-group comparisons that endpoints cannot supply.
The choice of allocation strategies reflects a trade-off among estimands. Many saturation levels may improve resolution of a response curve while reducing the number of clusters per level. Extreme intensities may be especially informative about aggregate policy, while intermediate intensities supply treated and untreated individuals for direct and indirect effects. Prespecifying the principal contrasts and simulating statistical power using plausible effect and dependence scenarios can align the experiment with its intended decision.
Network and geographic randomization
A network design can randomize strategically chosen nodes, complete network neighborhoods, or treatment at different graph-based distances. The design must take into account the resulting probabilities of exposure conditions. A unit cannot identify a contrast between high and low treated-neighbor exposure if its observed network and the assignment scheme make one of those conditions impossible. Support calculations reveal which units contribute to each contrast.
Geographic designs use distances or travel patterns to define potential transmission. Geographic buffer zones may reduce contamination but alter the sampled population if residents near edges differ systematically from residents in central locations. Randomization of larger economic areas can improve alignment with market equilibrium while reducing the number of independent assignment units. A design should explain how the gain in mechanism coverage balances the loss in replication.
Online experiments pose related questions because users and sellers can compete even when geographically dispersed. Clustering by substitution patterns, shared listings, or buyer-seller interactions may reduce interference. A design using time blocks may estimate market-wide outcomes when simultaneous assignment would create severe interference. Such switchback designs require adequate treatment switching, randomized scheduling, and credible treatment of carryover, trend, anticipation, and serial dependence.
Noncompliance, estimation, and inference
Randomized assignment identifies assignment effects within the experiment's supported contrasts. Receipt-based estimation introduces an additional endogenous variable. A participant may be induced to enroll by assigned outreach; a nonparticipant may receive information through peers. Instrumental-variable analysis requires exclusion, monotonicity where applicable, and an explicit treatment/exposure structure. Under interference, a person's assignment may alter others' behavior and then feed back into that person's outcome. A conventional own-receipt exclusion restriction can therefore fail.
Inference should reflect the actual probability law of assignment and the exposure mapping. Randomization tests can evaluate sharp null hypotheses when outcomes under relevant assignments are known under the null. A sharp null of no effect of any assignment is stronger than a null excluding one specified spillover channel. Testing a particular interference mechanism may require restricting assignments or conditioning on aspects of assignment that preserve imputability. Rejection of a global null does not identify which transmission route caused the difference.
Standard errors should account for randomization units, joint exposure, and any maintained residual dependence assumptions. Under finite-population designs, cross-unit dependence can arise from assignment even without correlated outcome disturbances. Spatial or network dependence can remain after statistical adjustment for observed exposure. Precision calculations, robustness checks, and uncertainty reporting should correspond to the design rather than to the appearance of the regression table.
Repeated analyses across outcomes, saturation levels, demographic groups, network distances, and time periods generate multiplicity. Prespecified outcome families, transparent exploratory labels, and suitable adjustment or interpretation reduce the risk of selecting a favorable pattern after inspecting results. Mechanism analyses require particular care because proposed mediators often respond endogenously to treatment.
Structural modeling is a complementary identification strategy when experiments support limited policy regimes. Randomized price or cost changes can discipline demand or competition parameters. The model then links those parameters to equilibrium counterfactuals outside the observed range. Parameter identification, model fit, equilibrium selection, sensitivity, and external validation are distinct tasks. A structurally projected effect is best reported alongside the experimental contrasts that support it, with explicit assumptions governing extrapolation.
Comparative international field evidence
France: job placement and displacement
Crépon and colleagues (2013) studied labor market displacement in France using clustered randomization across 235 labor markets and differing assignment intensities, including zero and full assignment. The authors report that assistance offered to eligible job seekers improved their relative prospects of stable employment in the short run, while some of that advantage came at the expense of other eligible job seekers. Displacement was more pronounced in weak labor markets, and aggregate employment gains were limited. The reported advantage was not a persistent universal effect at all horizons.
The design is scientifically important because both competition and market-level coverage enter the evaluation. The policy problem is the extent to which assistance creates opportunities, accelerates matching, or reallocates existing openings among applicants. Workers who receive more effective help compete with workers who do not. In a market with little job creation, a comparison within a partially treated market is naturally sensitive to this competition.
This study does not establish that every job-search program is socially wasteful. A program designed to improve match quality may influence productivity or reduce hiring costs, and a different labor market may respond with additional vacancies. The evidence instead establishes that displacement can be large enough to change the interpretation of an individual advantage in the institutional environment examined. It justifies measuring nonparticipants and aggregate labor-market outcomes in relevant policy evaluations.
Kenya: cash transfers and local production
Egger and colleagues (2022) examined general equilibrium effects of cash transfers in rural Kenya. Their intervention delivered large one-time transfers of about US$1,000 to more than 10,500 poor households across 653 randomized villages. The authors report positive economic effects on nonrecipient households and firms, limited local price inflation, and an estimated local transfer multiplier of approximately 2.5.
The intervention is a demand and income shock at a scale capable of affecting the surrounding economy. Its expansionary spillovers contrast with the competition around a relatively fixed resource. If firms have unused capacity, additional spending can increase production and earnings without producing proportionate inflation. If local production and trading networks meet part of the demand, some benefits extend to households outside the eligibility frame.
The empirical finding is tied to this setting, scale, funding source, definition of local economic activity, and estimation horizon. The multiplier is not a national balanced-budget fiscal multiplier. National financing arrangements may change taxation, borrowing, prices, interest rates, imports, and expenditure elsewhere. The study's local estimate provides evidence about regional economic transmission under the studied intervention. A national policy comparison requires additional evidence about these omitted adjustments.
Nor should the estimated multiplier be read as a benefit-cost ratio. A multiplier describes a change in economic activity relative to the transfer measure used by the study. Welfare accounting additionally requires resource costs, distributional valuations, financing opportunity costs, and the treatment of external effects. A positive activity response matters, but it is not a complete policy valuation.
India: public employment and labor market power
Muralidharan, Niehaus, and Sukhtankar (2023) report general equilibrium effects of public employment from experimental evidence on improved implementation in India. In the final published abstract, the authors report beneficiary households' earnings rising by 14% and poverty falling by 26%; about 86% of the income gains came from nonprogram earnings. They report increased real private wages and employment, with their interpretation emphasizing imperfectly competitive labor markets.
The case illustrates how the quality and accessibility of a public employment opportunity may alter the private employment environment. A credible outside option changes the willingness of workers to accept existing terms. If employers have market power, the resulting wage and employment responses need not match the predictions of a simple competitive labor market with perfectly elastic alternatives. The observed combination of outcomes motivates examination of labor supply, bargaining, employer concentration, and the actual reliability of public work.
The result is conditional on an intervention improving program implementation in the studied regions; it is not an estimate for every public employment program or for unrestricted expansion of public work. The monograph uses final journal abstract results rather than substituting earlier working-paper estimates. Because final full-text access was unavailable, detailed secondary mechanism coefficients and subgroup estimates are not used as independent evidence here.
Kenya: classroom organization and teacher response
Duflo, Dupas, and Kremer (2011) investigated peer effects and tracking through a randomized evaluation in 121 schools in Kenya. Their results indicate benefits from achievement-based grouping, including for lower-achieving students, while their analysis recognizes the potential contribution of higher-achieving peers. The adjustment of instruction to students' preparation is central to interpreting the pattern.
Classroom composition changes several components of an educational environment at once. A student's peers can change motivation, learning opportunities, and classroom interactions; a teacher can change instructional pace and effort in response to the distribution of achievement. A grouping policy can therefore produce outcomes inconsistent with extrapolation from a fixed-teacher peer coefficient alone.
The case informs economic experiments because providers often respond to the composition of recipients. If an intervention changes the distribution of needs facing a teacher, clinician, caseworker, or loan officer, provider adaptation becomes part of the treatment mechanism. A research design intended to distinguish direct peer learning from provider response needs separate variation or measurements that support the distinction. The aggregate desirability of a grouping policy also requires attention to long-term outcomes, distribution, and institutional feasibility.
China: rural insurance and information networks
Cai, de Janvry, and Sadoulet (2015) studied social networks and insurance decisions using randomized information provision in rural China. The authors report that the effect of an additional informed friend on untreated farmers' insurance take-up was equivalent to a 13% reduction in the insurance premium. This is their reported premium-equivalent effect, not a thirteen-percentage-point increase in enrollment.
Insurance demand depends on knowledge of contractual contingencies, perceived risk, trust, and the availability of alternatives. A person who receives an explanation can transmit information through ordinary social relationships. An individually targeted educational intervention may consequently affect people who were never directly approached by its implementers.
Information exposure is not equivalent to a generic measure of social conformity. Identification of the message transmitted, and its distinction from friends' purchase choices or common environmental shocks, matters for policy. If information is the principal channel, diffusion may change how an organization should allocate educational effort. If cooperative risk sharing or imitation dominates instead, the appropriate policy and ethical analysis differ.
Enrollment effects alone cannot establish insurance welfare. A complete evaluation considers the risk actually covered, premium and subsidy, contract comprehension, claims settlement, liquidity constraints, and substitution away from informal protection. Informational spillovers may reduce distribution costs, but their value depends on whether additional coverage improves the insured population's feasible choices.
Kenya: competition among agricultural traders
Bergquist and Dinerstein (2020) used experimental shocks in agricultural markets to study competition and entry among traders in Kenya. They report a median markup estimate of 39% and find limited effects on prices from an intervention subsidizing entry that elicited low uptake. Their interpretation of competition relies on the economic structure used to connect randomized shocks and observed market behavior.
This setting illustrates the difference between experimental variation in a market primitive and a complete empirical identification of an unobserved market structure. A cost shock can reveal how prices respond; a demand shock can supply complementary information. Inferring strategic interaction requires a model of decisions, costs, demand, and equilibrium behavior. Market conduct may vary across products, locations, and time.
The limited price response to subsidized entry illustrates a further scale problem. The intended change in market structure and the actual change achieved by implementation need not coincide. Low entry uptake may leave incumbent conduct substantially unchanged. An assignment effect of the entry offer answers a different question from the effect of a sustained exogenous increase in the number of competing sellers. A policy assessment needs both implementation evidence and an economic counterfactual grounded in observed behavior.
Digital marketplaces: interference and experimental architecture
Holtz and colleagues (2025) report evidence from an online marketplace pricing meta-experiment comparing individual and cluster randomization. In the studied fee intervention, the authors attribute at least one fifth of the individual-randomized estimate of the total average treatment effect to interference bias, which their cluster design addresses. The fraction refers to the estimate of the treatment effect, not to a percentage-point change in sales or booking probability.
Digital platforms mediate demand across competing listings. A fee, ranking change, promotion, or seller incentive can redirect customers from untreated to treated sellers. The revenue of favored listings may rise while aggregate transactions rise by much less. When substitution is strong, a randomized treatment distributed among individual listings can modify the competitive position of each listing without replicating the conditions of platform-wide adoption.
Cluster randomization based on economically meaningful substitution patterns helps align the experiment with the scope of competition. It remains necessary to examine cross-cluster transactions and temporal adjustment. The cited study supports the relevance of design-induced differences in an actual pricing experiment; it does not demonstrate that a single clustering procedure eliminates every form of marketplace interference.
Comparative interpretation
France identifies competition for employment as a mechanism that can reduce aggregate gains relative to individual gains. Kenya's transfer experiment demonstrates the relevance of demand expansion and positive spillovers in a local economy. The Indian public employment experiment links implementation and outside options with private labor-market responses. The education and insurance studies underscore provider adjustment and information transmission, while the agricultural and digital-market studies show why prices, competition, and substitution require experiment-specific interpretation.
These are heterogeneous interventions rather than estimates of a homogeneous parameter. Differences in sector, country, treatment, baseline institutions, follow-up, and target population prevent a direct numerical ranking. Their comparative value is mechanistic. The findings show why a positive treated-unit effect can be produced by fundamentally different changes in the economic system, and why measurement of resource creation and incidence must accompany the explanation.
Institutions, policy scaling, and welfare
From experimental intensity to a policy regime
Scaling a field experiment can change several dimensions simultaneously. Geographic coverage expands; eligibility rules alter the population receiving treatment; implementation institutions move from dedicated experimental staff to ordinary agencies; suppliers and workers adjust to larger demand; fiscal resources are raised differently. A policy that preserves the intervention's formal description may change all these elements.
A useful policy counterfactual describes the allocation strategy, eligible population, implementation resources, funding source, economic environment, and time horizon. The relevant comparison might be full coverage versus existing policy, or high coverage versus an established partial program. A comparison to hypothetical absence of intervention may be less relevant than a feasible alternative if the institution already supplies similar services.
Transporting experimental evidence requires an explicit argument. Statistical reweighting can adjust measured differences in population composition when the relevant support and invariance assumptions hold. It cannot independently adjust a change in the mechanism of equilibrium response. A regional experiment on an externally funded transfer may be representative of household behavior while lacking variation in national funding arrangements. A model of financing or additional evidence from fiscal reforms is needed for the national counterfactual.
Collaboration with implementing agencies can improve relevance by revealing service capacity, budget costs, staffing requirements, take-up, and administrative constraints. It introduces a need for transparent independence of evaluation and protection from selective interpretation. Ethical safeguards must account for untreated individuals who may experience adverse effects. Where exposure creates risks for people outside the direct participant sample, the design's ethical assessment should consider these external populations within the applicable consent, legal, and data-protection framework.
Welfare beyond the treated unit
Let an allocation strategy a generate consumption, income, leisure, risk, and other relevant outcomes for the target population. A social welfare assessment specifies the individual welfare objects and a rule for aggregation, together with resource costs and relevant effects outside that population. For a differentiable monetary approximation, welfare changes may be represented through changes in consumer and producer surplus, distributional weights where justified, and net resource costs relative to the counterfactual.
Transfers should be handled consistently. A payment from a government to a household is simultaneously expenditure for the government and income for the household. Its value to the household and opportunity cost to the funder matter; the payment itself should not be counted twice as newly produced resources. Administrative labor, real inputs, distortionary financing, and displaced alternative public spending may contribute to the resource cost of the policy. If distributional objectives justify valuing gains to poor households differently from losses borne elsewhere, the valuation should be explicit.
In a competitive model, a price-mediated pecuniary externality can redistribute surplus without creating an independent resource loss in the relevant benchmark. In settings with market power, missing markets, risk, taxes, or binding constraints, the same price change may also affect efficiency. A distinction between pecuniary incidence and technological or informational externalities can organize the analysis, but the welfare implications depend on the surrounding institutions.
Employment displacement presents a similar problem. A transfer of a job opportunity from one worker to another is a distributional change, potentially accompanied by productivity differences and matching improvements. Counting only recipients' earnings omits displaced workers. Conversely, treating every lost opportunity as identical to every gained opportunity may conceal heterogeneous wage, productivity, and welfare effects. A policy decision depends on both aggregate resource allocation and the distribution of access to scarce opportunities.
Local price effects require careful valuation. Rising producer prices may improve sellers' returns while raising consumers' cost of living. The identity of buyers and sellers can overlap; net market positions are relevant. Household-level welfare estimates should incorporate heterogeneous consumption and production baskets, and a market-level estimate should avoid aggregating inconsistent nominal measures.
Time and endogenous adaptation
An intervention may generate an immediate relative gain followed by attenuation, diffusion, or reversal. Hiring responds at a different pace from job search. Teachers change instructional methods, and firms decide whether persistent demand justifies investment. An announced durable policy can induce expectations and strategic reactions before funding is disbursed.
A longitudinal design distinguishes measured outcomes at different horizons from a forecast of eventual equilibrium. A short-run effect may be a valid estimate of a short-run policy objective. Its long-run interpretation requires observations or a model of adjustment. Follow-up should consider attrition, changes in population composition, migration, treatment renewal, and persistence of the exposure network.
Policy evaluation also requires a distinction between temporary local shocks and recurring commitments. A one-time transfer financed externally changes demand and household balance sheets in a manner different from a permanent entitlement financed by recurring taxes. A temporary public employment improvement can affect outside options during the intervention; a credible permanent program may alter long-run labor bargaining, investment, and land use. Program duration is part of the treatment definition, not merely a detail of data collection.
Analytical synthesis
The original contribution of this monograph is a comparative analytical synthesis linking design-based estimands to economic mechanisms and policy accounting. Its conclusions derive from the formal reasoning and source comparisons developed above. They constitute an interpretation of established research and explicitly constructed examples; no independent empirical discovery or new named theoretical system is asserted.
First, causal identification and policy relevance operate at distinct levels. The assignment design determines the causal contrast, and the economic system determines the response to alternative allocations. Randomization addresses selection into supported assignment regimes. It does not imply invariance of behavior, prices, or institutions across unsupported coverage levels. The two levels become connected when the experiment varies a policy-relevant allocation, records the resulting economic environment, and supplies a defensible argument for transport to the target regime.
An immediate implication is that estimation precision cannot compensate for an incorrectly specified target. A study of one hundred thousand individually assigned workers in a market with a fixed supply of vacancies may deliver a very precise estimate of relative advantage. The fixed-opportunity example demonstrates that the population effect can be zero regardless of that precision. Enlarging the number of workers improves information about the contrast represented in the experiment, not about a counterfactual beyond its support.
Second, the decomposition of mean outcomes under coverage strategies provides a transparent bridge from participant outcomes to population effects. Consider two interior intensities p = 0.25 and q = 0.75 in the fixed-opportunity example, and compute M(q) − M(p). The direct contrast remains 0.20 at each intensity. The weighted change in the direct term is 0.75×0.20 − 0.25×0.20 = 0.10, while μ₀(q) − μ₀(p) = 0.25 − 0.35 = −0.10. Their sum is zero. The calculation shows exactly how an expansion in the share receiving an advantage can be offset by deterioration of the untreated reference outcome. The offset is a feature of the fixed-resource example, not a universal empirical law.
In the complementary productivity example the analogous weighted direct term is one, and the indirect term is 0.50; the population average increases by 1.50. Identical experimental coverage changes and unchanged within-intensity direct comparisons produce different aggregate results when the transmission environment differs. Thus a direct effect by itself contains insufficient information for classifying a policy as predominantly redistributive or productive.
Third, economic effects cross the observational boundary through several channels. A labor-market program can affect ineligible applicants, a transfer can affect traders outside the recipient villages, and a digital intervention can affect listings competing for the same users. A research population defined only by eligibility becomes incomplete for an aggregate policy question when a substantial share of effects falls elsewhere. Extending data collection to relevant outsiders and recording cross-boundary flows improves the credibility of the interpretation. It also makes the remaining uncertainty explicit: effects beyond any finite observation boundary may still require modeling or bounds.
Fourth, the sign of an observed spillover is an unreliable substitute for mechanism identification and welfare analysis. A negative untreated effect may reflect displacement from a fixed opportunity, an increase in the price of a consumption good, or an efficient shift of labor toward more productive firms. A positive spillover may reflect creation of output, redistribution to suppliers, improved information, or a fiscal transfer from an unobserved population. The appropriate evaluative response depends on the mechanism, the identity of beneficiaries and losers, and the economic resources involved.
Fifth, the studies reviewed here imply that policy-scale evidence is most informative when experimental architecture and institutional architecture are aligned. A labor market, school system, trading network, or digital platform defines a domain of interaction. Assignment within that domain identifies contrasts in relative treatment exposure; assignment across domains can identify changes in the broader environment. The correct unit for randomization is governed by the economic question and attainable precision, not by a presumption that larger clusters are always preferable.
Sixth, an equilibrium result should retain its funding and time boundary. The Kenya transfer study concerns a substantial economic intervention into a particular local economy. The Indian case concerns implementation improvements affecting workers' feasible employment options. Their results demonstrate channels through which nonrecipient or nonprogram outcomes can change. They cannot, without further assumptions, supply national fiscal or permanent-program welfare estimates.
Finally, integrating formal inference with policy interpretation requires preserving the chain from intervention to assignment, actual receipt, exposure, behavioral response, endogenous adjustment, measured outcome, and welfare target. Every link has its own empirical or analytical requirements. A failure at one link does not invalidate the entire study; it limits the conclusions that can be drawn from it. A clear account of the chain allows valuable internally valid findings to survive a critical assessment of their external relevance.
A reproducible interpretation exercise
Consider an illustrative experiment in forty economically separate markets, with ten markets assigned to each of four strategies: zero coverage, 25% coverage, 75% coverage, and full coverage. Assume forty eligible individuals per market, plus a sample of thirty ineligible residents or firms observed for outcomes relevant to the mechanism. The example is a design sketch and power has not been established.
The first-stage assignment law determines the probability of each market strategy. At the interior strategies, exactly ten or thirty eligible persons are assigned. The own-status contrast is therefore a contrast under the complete-randomization strategy: treated and untreated workers face peer counts that differ by one. A policy-focused analysis would prespecify the overall eligible-population contrast between the full and zero strategies, the indirect contrasts among untreated individuals at supported strategies, and selected total-market outcomes including the sample of outsiders.
To interpret the result, suppose the primary eligible employment outcome follows the fixed-opportunity probabilities derived earlier. Expected employment in each market is sixteen individuals at every strategy. At 25% coverage the expected number of treated employees is 10×0.55 = 5.5 and the expected number of untreated employees is 30×0.35 = 10.5. At 75% coverage they are 30×0.45 = 13.5 and 10×0.25 = 2.5. The fractional values are expectations over repeated realizations, not observed counts. The direct contrast is positive, while the expected eligible total remains sixteen.
The additional observations matter because an unchanged eligible total may conceal shifts between eligible and ineligible workers or changes in hours, wages, and vacancy duration. If the market includes many noneligible applicants, the fixed-opportunity calculation of the eligible population is itself conditional on their outcomes. A claim of unchanged total market employment would require observing or accounting for that wider population. The exercise makes the choice of denominator explicit.
A data release for this hypothetical design would include the assignment probabilities, roster definitions, eligibility date, implementation records, outcome definitions, geographic or market links, and missingness handling. The analysis would report randomization-based uncertainty at the market and individual assignment levels as appropriate, supported exposure comparisons, and a distinct discussion of welfare. No empirical p-values or confidence intervals are imputed to this illustrative numerical exercise.
Open questions and research agenda
The most substantial open problems concern the relationship between feasible experimental variation and the scale of the economic systems under evaluation. National policy may affect macroeconomic conditions and public budgets that local experiments hold approximately fixed. Randomizing whole national economies is rarely feasible. Combining regional experimentation with credible structural restrictions, institutional comparisons, historical variation, and explicit uncertainty about general equilibrium becomes necessary.
Network boundaries require further methodological development. Many economic interactions are intermittent, directional, and endogenous. An observed social network may differ from the network through which employment, knowledge, credit, or prices respond. Research should examine how sensitive exposure effects are to measurement error, dynamic links, and omitted interactions, while retaining a clear target population for inference.
Long-run adjustment presents another challenge. Markets can respond gradually to changes in demand, skills, outside options, and expectations. Evaluations with short follow-up periods can establish immediate impacts without observing investments, entry, cohort replacement, and migration. Follow-up across different horizons can distinguish persistence of individual treatment effects from adaptation of the system itself.
Implementation at scale requires study of cost functions and institutional capacity. Small pilots often rely on dedicated personnel and close supervision. Expansion may change input quality, participation rates, administrative load, and opportunities for strategic behavior. Designs that experimentally vary implementer support, staff capacity, or treatment intensity can help separate these mechanisms, subject to feasibility and ethical constraints.
An important research direction is the collection of outcomes for populations outside eligibility criteria. The social benefit or harm of an intervention can be invisible when survey instruments cover only participants. Researchers should identify affected market actors in advance, then measure outcomes appropriate to their roles. This extension requires a balance between scientific value, participant burden, privacy, and legal obligations.
Methodological work should also focus on transparent transport. A policy assessment should state which quantities are experimentally estimated, which are calculated from accounting identities, which are borrowed from other populations, and which depend on equilibrium models. Sensitivity analyses should vary assumptions that materially influence policy estimates, including supply elasticities, market boundaries, funding, interference decay, and institutional response.
A final agenda concerns cumulative evidence. Heterogeneous field experiments can support common mechanistic comparisons without being forced into a single pooled coefficient. Future reviews should publish structured evidence records containing intervention, allocation contrast, market boundary, time horizon, estimand, outcome units, uncertainty, and institutional conditions. A quantitative synthesis would then be possible for sufficiently comparable subsets, with explicit treatment of study selection and dependence. This dossier establishes the interpretive rationale for such work but does not perform a systematic search or pooled estimation.
Conclusion
Spillovers and equilibrium effects belong to the economic substance of field experiments. They arise because interventions alter environments shared by economic actors and because the returns to individual choices depend on the decisions of others. The scientific task is to determine which allocation contrast an experiment identifies, how the intervention changes the surrounding system, and which population-level consequences follow from that change.
Potential outcomes indexed by treatment allocations provide a general causal representation. Partial interference, exposure mappings, and randomized saturation strategies yield tractable contrasts when their assumptions are appropriate. Randomization identifies effects supported by its probability law, while statistical inference must respect assignment dependence and exposure support. Equilibrium models explain how treatment changes prices, opportunities, production, and institutional responses, and their extrapolations require independently justified premises.
The empirical literature illustrates the range of mechanisms. Competition for jobs can redistribute employment opportunities; local cash injections can generate demand and nonrecipient income; public employment can affect private earnings and bargaining; information can diffuse through social networks; provider behavior can change with participant composition; market interventions can redirect competitive activity. No single sign or magnitude summarizes these processes.
The central analytical conclusion is that the individual treatment effect, the aggregate outcome effect, and the welfare effect are distinct objects. A complete economic interpretation connects them through explicit allocation regimes, mechanisms, resource constraints, population boundaries, time horizons, and distributional accounting. This approach preserves the causal value of field experiments while establishing the conditions under which their findings can inform decisions at scale.
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