13 Spillover Effects
All evaluation methods introduced so far rely on a simple idea: each unit has two potential outcomes, one under treatment and one under no treatment. This is convenient because it allows us to write the causal effect for unit \(i\) as the comparison between \(Y_i(1)\) and \(Y_i(0)\).
This representation depends on the Stable Unit Treatment Value Assumption (SUTVA) (Rubin 1980). As discussed in Chapter 2, SUTVA has two main components. First, there should be no hidden versions of the treatment: units assigned to the same treatment status should receive the same treatment in the relevant sense. Second, there should be no interference between units: the potential outcome of one unit should depend only on that unit’s own treatment status, not on the treatment status of other units (Cox 1958).
This second part is the no-interference assumption. Spillover effects arise precisely when it fails.
Spillover effects occur when the treatment of one unit affects the outcomes of other units.
Spillovers are not a technical nuisance only. In many policy settings, they are part of the mechanism through which the policy is expected to work. A regional development program may aim to support treated firms, but also to stimulate local suppliers, competitors, workers, and neighboring areas. A vaccination campaign may directly protect vaccinated individuals, but also indirectly protect unvaccinated individuals by reducing disease transmission.
When these indirect effects exist, treatment effect estimates obtained by comparing treated and untreated units may be biased. They may also fail to capture the indirect effects of the treatment on untreated units.
Angelucci and Di Maro (2016) illustrate this problem using a hypothetical school deworming program. Suppose that, without the program, the infection rate would be 80%. After treating some pupils, the infection rate falls to 10% among treated pupils and to 60% among untreated pupils because reduced transmission also benefits them.
A naive comparison within the school estimates an effect of \(10\%-60\%=-50\) percentage points. However, relative to the no-program counterfactual, the effect on treated pupils is actually \(10\%-80\%=-70\) percentage points, while the spillover effect on untreated pupils is \(60\%-80\%=-20\) percentage points.
Ignoring spillovers therefore creates a double underestimation: it understates the benefit for treated pupils and completely overlooks the benefit received by untreated pupils. Treatment randomization within the same school does not solve this problem because the control group is exposed to the treatment indirectly.
13.1 Why Spillovers Matter
Suppose a training program improves the job prospects of treated workers. If treated workers obtain jobs that would otherwise have gone to untreated workers, the program generates a substitution effect. The treated group benefits, but part of the gain comes at the expense of the untreated group.
In this case, the untreated group no longer represents what would have happened to the treated group in the absence of the treatment.
Spillovers can also be positive. For example, providing medicine to some children may reduce disease transmission and benefit untreated children as well. If better health improves learning, both treated and untreated children may experience educational gains.
The same logic applies to local economic policies. A subsidy to some firms may increase demand for local suppliers and create positive spillovers. But it may also crowd out competitors, increase input prices, or reallocate workers across firms.
If untreated units are affected by the treatment received by other units, they are no longer valid controls because their outcomes no longer represent the untreated counterfactual. This contaminates the control group and biases the estimated treatment effect. Depending on the direction and magnitude of the spillovers, the resulting estimate may understate or overstate the treatment effect of interest.
13.2 Relaxing the no-interference assumption
Under the no-interference assumption, the potential outcome of unit \(i\) depends only on its own treatment status:
\[ Y_i = Y_i(D_i). \]
With spillovers, this is no longer enough. The potential outcome of unit \(i\) may depend on the entire vector of treatment assignments:
\[ Y_i = Y_i(D_1,D_2,\ldots,D_N). \]
This creates a severe dimensionality problem. With \(N\) units and a binary treatment, there are \(2^N\) possible treatment allocations, and unit \(i\) may in principle have a different potential outcome under each of them. The potential-outcomes framework therefore expands from two potential outcomes per unit to an exponentially growing set of possibilities. Without additional restrictions on how other units’ treatments affect unit \(i\), causal inference quickly becomes intractable, because only one treatment allocation is observed while an enormous number of counterfactual exposure configurations remain unobserved.
This is why causal inference with interference requires structure. We need assumptions that reduce the number of relevant potential outcomes and define which forms of exposure matter.
A common way to simplify the problem is to distinguish between a unit’s own treatment and its exposure to the treatment of others.
Let \(D_i\) denote whether unit \(i\) is directly treated. Let \(G_i\) summarize unit \(i\)’s exposure to the treatment status of other units. The rule that maps the full treatment allocation into this lower-dimensional exposure measure is known as the exposure mapping (Manski 2013; Aronow and Samii 2017). For example, \(G_i\) may indicate whether some neighboring units are treated, or it may measure the share of treated units in the same local area.
Potential outcomes can then be written as
\[ Y_i(d,g), \]
where \(d\) is the unit’s own treatment status and \(g\) is its exposure to others’ treatment.
Writing potential outcomes as \(Y_i(d,g)\) makes the interference problem more tractable. This simplification is useful, but it is also an assumption. It means that, once we know unit \(i\)’s own treatment status \(D_i\) and its exposure measure \(G_i\), the exact identity and configuration of treated units no longer matter for unit \(i\)’s potential outcome.
For example, if \(G_i\) is defined as the share of treated neighboring municipalities, we assume that two municipalities with the same own treatment status and the same treated-neighbor share have the same relevant exposure, even if the treated neighbors are located in different directions or have different sizes.
The credibility of the analysis therefore depends on whether the chosen exposure mapping captures the spillover channels that matter in the application.
Once potential outcomes are indexed by both own treatment status and exposure to others’ treatment, there is no longer a single treatment effect. Different causal questions correspond to changing different components of \((d,g)\). We can therefore distinguish between direct, indirect, total, and overall effects, depending on whether we vary the unit’s own treatment, its exposure to others’ treatment, or both.
To make these comparisons concrete, let \(g_0\) denote the baseline exposure level, corresponding to no exposure to others’ treatment, and let \(g_1\) denote a higher level of exposure.1
1 If exposure is measured as the share of treated neighbors, for example, \(g_0=0\) corresponds to having no treated neighbors, while \(g_1>0\) represents positive exposure.
The direct effect compares treated and untreated status while holding exposure fixed at a given level \(g\), where \(g\) can take any admissible exposure value, including the baseline level \(g_0\):
\[ DE(g)=E[Y_i(1,g)-Y_i(0,g)]. \]
This captures the effect of receiving the treatment directly for units exposed to the same level \(g\) of spillovers. In particular, \(DE(g_0)\) is the direct effect when units are unexposed to others’ treatment.
The indirect effect compares different exposure levels while holding the unit’s own treatment status fixed. For untreated units, it can be written as
\[ IE(0;g_1,g_0)=E[Y_i(0,g_1)-Y_i(0,g_0)]. \]
This captures the spillover effect of moving an untreated unit from no exposure, \(g_0\), to a higher exposure level, \(g_1\).
The total effect compares being treated and exposed to a treated environment with being untreated and unexposed:
\[ TE(g_1,g_0)=E[Y_i(1,g_1)-Y_i(0,g_0)]. \]
It therefore combines the effect of receiving the treatment directly with the effect of moving from no exposure, \(g_0\), to the higher exposure level \(g_1\).
The overall effect takes a population-wide perspective. Rather than focusing on a particular combination of own treatment and exposure, it compares average outcomes under the policy with average outcomes under a counterfactual scenario in which no unit is treated and, consequently, no unit is exposed to others’ treatment. If the policy generates treatment status \(d_i^1\) and exposure \(g_i^1\) for each unit \(i\), the overall effect can be written as
\[ OE= \frac{1}{N}\sum_{i=1}^{N} \left[ Y_i(d_i^1,g_i^1)-Y_i(0,g_0) \right]. \]
The overall effect therefore captures the total impact of the policy on the population, combining the direct effects on treated units with the spillover effects generated by their treatment on other units.2
2 Unlike the total effect, which compares two specific treatment-exposure states, the overall effect averages over the different treatment and exposure conditions generated by the policy across the population.
With spillovers, the direct effect is only part of the story. A complete evaluation may also need indirect, total, and overall effects.
13.3 Why Spillover Effects Are a Problem for Control-Based Designs
Suppose we are analyzing an RCT and we adopt a simple difference in means estimator:
\[ DIM = E[Y_i^{obs}\mid D_i=1] - E[Y_i^{obs}\mid D_i=0]. \]
Without spillovers, the average outcome of untreated units provides a reliable estimate of the missing counterfactual outcome for treated units.
With spillovers, however, untreated units may themselves be affected by the policy and therefore no longer provide a clean untreated counterfactual. If, for instance, untreated units benefit from positive spillovers, their observed outcomes are higher than they would have been in the absence of the policy. A treated-control comparison then subtracts part of the policy-induced benefit and may understate the total effect of the program.
Conversely, if untreated units are harmed by negative spillovers, their observed outcomes are lower than they would have been in the absence of the policy. The treated-control difference may then overstate the effect of the program, because part of the observed gap is generated by the negative spillover on the control group rather than by the direct effect of treatment.
The bias depends on the type, direction, and intensity of interference.
Randomization does not automatically solve the problem of spillovers. If treated units affect untreated units, then even a perfectly randomized experiment will not identify the treatment effects of interest.
For example, in an experiment on job training, assigning some workers to training may change the labor-market opportunities of untreated workers. In an experiment on vaccination, assigning some individuals to treatment may reduce infection risk for untreated individuals.
Randomization still simplifies identification, but the design must be adapted to the relevant estimand. In some cases, researchers may randomize treatment saturation across groups, so that some groups have many treated units while others have few. This makes it possible to study how outcomes vary with exposure to treatment (Hudgens and Halloran 2008).
13.3.1 Partial Interference
One common restriction is partial interference (Sobel 2006). Units are divided into groups, and interference is assumed to occur within groups but not between groups.
For example, firms may interact within local labor markets but not across distant markets. Students may interact within schools but not across schools. Households may interact within villages but not across villages.
Under partial interference, the potential outcome of unit \(i\) in group \(c\) may depend on the treatment assignments of units in the same group:
\[ Y_{ic}=Y_{ic}(D_{1c},D_{2c},\ldots,D_{n_c c}), \]
but not on treatment assignments in other groups.
This assumption greatly simplifies the problem. It allows the researcher to compare groups with different treatment intensities and to estimate direct and spillover effects within a structured framework.
Partial interference assumes that units can affect each other within groups, but not across groups.
The assumption is useful, but it may be unrealistic for some policies. Economic interactions often cross administrative boundaries. Firms trade with suppliers outside their municipality, workers commute across local labor markets, and households may respond to opportunities in nearby areas.
13.4 Spatial Econometric Models
In regional and urban policy, spillovers often depend on geography. The treatment assigned to one municipality, region, or firm may affect nearby units more than distant units.
Spatial econometric models formalize this idea by using a spatial weights matrix \(W\) (Halleck Vega and Elhorst 2015). The element \(w_{ij}\) measures the connection between units \(i\) and \(j\).
Common definitions include:
- binary contiguity, where \(w_{ij}=1\) if two areas share a border and \(w_{ij}=0\) otherwise;
- inverse distance, where closer units receive larger weights;
- network distance, where connections are based on commuting, trade, supply chains, or social links.
An exposure measure can then be written as
\[ G_i=\sum_{j\neq i}w_{ij}D_j. \]
This variable measures the extent to which unit \(i\) is exposed to treatment received by other connected units, with the weights \(w_{ij}\) determining how strongly the treatment status of each unit \(j\) contributes to \(i\)’s exposure.
A simple spatial lag of the treatment model can be written as
\[ Y_i=\alpha+\tau D_i+\theta \sum_{j\neq i}w_{ij}D_j+X_i'\beta+u_i. \]
The term \(\sum_{j\neq i}w_{ij}D_j\) is the spatial lag of treatment and summarizes unit \(i\)’s exposure to treatment received by other units, with the spatial weights \(w_{ij}\) determining which units are considered connected and how strongly each contributes to \(i\)’s exposure.3
3 The spatial weights matrix \(W\) must be specified by the researcher. For example, units may be defined as connected when they share a border or are located within a given distance. If the weights are row-standardized, the spatial lag can often be interpreted as a weighted share of connected units that are treated.
In this specification, \(\tau\) captures the effect associated with unit \(i\)’s own treatment, holding its exposure to other treated units fixed, while \(\theta\) captures how the outcome changes with spillover exposure to treatment received by connected units, holding own treatment status fixed. A positive \(\theta\), for example, indicates that greater exposure to treated neighbors is associated with higher outcomes.
13.4.1 A Caution on Spatial Econometrics
Spatial econometric models can be useful, but their estimates do not have a causal interpretation by default. For causal interpretation, the spatial weights matrix \(W\) must provide a credible representation of the true structure of interactions.
If the researcher uses geographic distance but the relevant interactions occur through commuting networks, the spatial weights matrix may be misspecified. If spillovers operate through suppliers, competitors, or social networks, a simple border-contiguity matrix may be misleading.
This is one reason why the use of spatial econometrics for causal policy evaluation has been criticized (Gibbons and Overman 2012). Spatial methods can be informative, but spatial correlation alone is not enough for causal interpretation. What is needed is a credible identification strategy that defines the relevant potential outcomes and clarifies the assumptions under which they can be identified.
Nearby units often look similar for many reasons. To interpret spatial dependence as a causal spillover, the researcher must explain why the spatial exposure measure captures the relevant causal channel.
13.5 A Commonly Adopted Empirical Strategy with Control-Based Methods
A credible spillover analysis usually starts from theory. The researcher should ask:
- Which units can plausibly affect each other?
- Through which channel does interference operate?
- Is the spillover expected to be positive or negative?
- Does exposure depend on geography, networks, markets, or institutions?
- Are there units that are untreated and plausibly unexposed?
If some untreated units are plausibly unaffected by the treatment, they can be used as a clean comparison group. In that case, the average total effect on the treated can be estimated by comparing treated units with unexposed untreated units, using familiar methods such as matching, DiD, RD, or SCM.
If some untreated units are exposed to spillovers, they can be compared with unexposed untreated units to estimate indirect effects. This is the logic of applications that explicitly distinguish between treated units, neighboring exposed units, and untreated unexposed units (see Cerqua and Pellegrini 2017).
The general empirical design should therefore classify units into meaningful exposure categories:
- directly treated units;
- untreated units exposed to spillovers;
- untreated units not exposed to spillovers.
In spatial applications, a common extension of the DiD strategy is to define distance rings around treated units. For example, untreated units may be classified as being within 0-10 km, 10-20 km, or more than 20 km from the nearest treated unit. Units far enough away from treatment are treated as “pure controls”, while untreated units in closer rings are interpreted as exposed to different spillover intensities. The DiD model can then compare changes in outcomes for each exposed ring with changes among far-away unexposed controls. This provides a transparent way to study whether spillovers decay with distance. However, the strategy remains assumption-based: the researcher must justify the distance cutoffs, the definition of the pure control group, and the parallel-trends assumption between each ring and the unexposed control units.
The direct effect compares the outcome of a treated unit with the counterfactual outcome it would have had without treatment, holding its exposure to other treated units fixed. The indirect effect captures the effect of exposure to the treatment of others and can be identified by comparing untreated units that are exposed to treated units with otherwise comparable untreated units that are not exposed. The total effect combines the unit’s own treatment effect with the effect of exposure to other treated units. The overall effect summarizes the policy’s effect at the population level, averaging the consequences of both direct treatment and spillovers across all affected units.
Di Tella and Schargrodsky’s study of police and crime in Buenos Aires (Di Tella and Schargrodsky 2004) provides an application of this logic. After the 1994 terrorist attack on the main Jewish center, Jewish institutions received visible police protection. The authors use this sudden change to compare car thefts before and after the attack across blocks with different exposure to police protection.
The key idea is similar to a DiD rings strategy. Blocks with protected institutions are directly treated. Nearby unprotected blocks are useful for checking whether crime was displaced just around the corner. Farther blocks provide a comparison group that is less likely to be affected by the extra police presence.
This example shows why distance bands can be informative: they do not only estimate whether the intervention worked where it was implemented, but also whether its effects faded, spilled over, or displaced outcomes across nearby locations.
13.6 Application: German reunification and the inclusive SCM
Di Stefano and Mellace (2024) revisit the effect of German reunification on West Germany’s GDP per capita. In the original SCM application, Austria receives 42% of the weight used to construct synthetic West Germany. This large weight substantially improves the pre-treatment fit, reflecting the close historical and economic relationship between the two countries.
However, Austria may itself have been affected by reunification. West Germany may have diverted demand and investment toward East Germany and away from Austria. Including Austria in the donor pool may therefore contaminate the estimated counterfactual. Excluding it is not an easy solution either: the pre-treatment RMSPE increases from 119.07 to 270.74, substantially weakening the quality of the synthetic control.
The inclusive Synthetic Control Method (iSCM) addresses this trade-off by allowing potentially affected units to remain in the donor pool. It constructs synthetic controls for both West Germany and Austria and uses the resulting system of relationships to separate the direct effect on West Germany from the possible spillover effect on Austria.
The results confirm a negative effect of reunification on West Germany’s GDP per capita. After accounting for spillovers, the estimated loss is up to 1.5% larger than the conventional SCM estimate. For Austria, iSCM estimates a small negative spillover, reaching at most approximately USD 708 per capita, although this effect is not statistically significant.
This application illustrates a central difficulty in spillover analysis: the units most useful for constructing a credible counterfactual may also be those most likely to be indirectly affected by the intervention.
13.7 Worked Example
Suppose the government subsidizes a subset of firms in a disadvantaged region. The goal is to increase investment and employment among beneficiary firms, but the policy may also affect other firms.
Positive spillovers may arise if beneficiary firms strengthen local input–output linkages, increase demand for local services, or expand the local pool of skilled workers available to other firms.
There may also be negative spillovers if subsidized firms compete more aggressively, hire workers away from non-beneficiary firms, or increase local wages and rents.
A simple evaluation comparing subsidized and non-subsidized firms may therefore be misleading, because some non-subsidized firms may still be indirectly affected by the policy through spillovers. The evaluation should instead distinguish between:
- subsidized firms;
- non-subsidized firms located near subsidized firms or connected to them through supply chains;
- non-subsidized firms that are plausibly unexposed.
The policy may have a positive direct effect on subsidized firms, a positive or negative indirect effect on nearby non-subsidized firms, and an overall effect that depends on the balance between the two.
If no units can be considered plausibly unexposed, however, constructing a credible counterfactual from observed control units may no longer be feasible. In such settings, FBCMs may provide an alternative by using pre-treatment information to forecast how outcomes would have evolved in the absence of the policy.
Celli, Cerqua, and Pellegrini show that the presence of spillovers creates an important trade-off between control-based and forecast-based counterfactual methods (Celli et al. 2026).
CBCMs require untreated units that can credibly represent the no-treatment, no-exposure counterfactual. When spillovers are pervasive, or when the researcher cannot reliably determine which untreated units are exposed, such clean controls may not exist or may not be identifiable. In these settings, cross-unit comparisons can become severely contaminated.
FBCMs shift the identifying strategy. Rather than using post-treatment outcomes from other units, they forecast the no-treatment, no-exposure outcome from pre-treatment dynamics. This makes it possible to estimate aggregate policy effects even when all units are directly or indirectly affected by the intervention. The advantage, however, comes with a different identifying burden, as discussed in Chapter 11: the credibility of the analysis now depends on the stability and predictability of untreated outcomes. Moreover, exposure-specific direct and spillover effects still require information about the relevant exposure structure.
The practical lesson is therefore not that one class of methods is always preferable. When credible clean controls exist, CBCMs can use them to construct the counterfactual; when spillovers make clean controls unavailable or difficult to identify, FBCMs may provide a more credible alternative, particularly for aggregate and short-run policy effects.
13.8 Diagnostics and Validity Checks
Several checks are useful in applications with spillovers.
Report the exposure rule clearly. Readers should understand why a unit is classified as exposed or unexposed.
Test sensitivity to alternative exposure definitions. For example, if exposure is defined using geographic distance, researchers can assess whether the results change substantially when using thresholds of 10, 20, or 30 kilometers. Strong sensitivity to these alternative definitions should lead to a more cautious interpretation.
Examine pre-treatment balance and outcome trends across treatment and exposure groups. In particular, exposed untreated units may differ systematically from unexposed untreated units in both their pre-treatment characteristics and outcome trajectories.
Check whether exposure intensity is correlated with pre-existing trends or other confounding factors. For example, treated areas may be located in places that were already growing faster.
Report direct, indirect, total, and overall effects separately when possible. A policy may look successful for treated units while harming untreated units nearby.
13.9 Common Mistakes
Ignoring spillovers when they are substantively plausible. This can contaminate the control group and distort the estimated treatment effect.
Treating spillovers as a minor robustness issue. In some policies, spillovers are central to the policy logic.
Defining exposure mechanically without a theory of interaction. Distance, borders, and networks are not interchangeable measures of exposure.
Reporting only the direct effect. If the policy also affects untreated units, the direct effect may not capture the overall social value of the policy.
Assuming that randomization eliminates interference. Randomization balances treatment assignment, but it does not prevent treated units from affecting untreated units.
13.10 Summary
Spillover effects occur when the treatment of one unit affects the outcomes of other units. They violate the no-interference part of SUTVA and can make standard treated-control comparisons misleading.
The presence of spillovers changes the evaluation question. The researcher should not ask only whether directly treated units benefited. The broader question is how the policy affected the entire system of treated, indirectly exposed, and unexposed units.
Credible spillover analysis requires a theory of interaction, a clear exposure mapping, and an empirical design that can distinguish direct and indirect effects. Without these ingredients, what looks like a treatment effect may simply be a mixture of direct impacts, spillovers, and spatially correlated confounding.