Why Donor Contamination Matters
A synthetic control uses a weighted combination of untreated units to approximate the treated unit’s outcome in the absence of treatment. That counterfactual depends on the donor units remaining suitable comparisons after treatment begins. If a donor is indirectly affected by the intervention, its post-treatment outcome may no longer represent the untreated path it is meant to supply. The resulting gap can be biased even when the synthetic control matched the treated unit closely before treatment.
Spillovers can travel through trade, migration, commuting, shared infrastructure, policy imitation, or other links. A donor may also experience a related policy or shock at the same time. The central diagnostic question is not simply whether a donor changed after treatment, but whether the change plausibly reflects exposure that makes its observed post-treatment outcome a poor proxy for its untreated outcome.
How Contamination Enters the Synthetic-Control Gap
Let unit 1 be treated, and let \(j=2,\ldots,J+1\) index donor units. Suppose weights \(w_j\) are chosen using pre-treatment information and then held fixed for post-treatment comparisons, with \(w_j\geq 0\) and \(\sum_{j=2}^{J+1}w_j=1\). Write \(Y_{it}(0)\) for unit \(i\)’s outcome at time \(t\) without direct treatment or spillover exposure. For the treated unit, let \(\tau_{1t}\) denote its direct treatment effect. For donor \(j\), let \(\delta_{jt}\) denote the change in its outcome due to spillover or related contamination, relative to its outcome without that exposure. Then the observed outcomes can be written as
The observed treated-minus-synthetic gap is \(G_t=Y_{1t}-\sum_j w_jY_{jt}\). Substituting the outcome decompositions separates the direct effect, the untreated counterfactual fit error, and the weighted donor contamination:
This identity gives a useful sign check. If the donor-weighted spillover is positive, the synthetic control is raised by contamination and the estimated gap is reduced. If it is negative, the synthetic control is lowered and the gap is increased. When the untreated fit error is negligible, the contamination component of the gap’s bias is \(-\sum_jw_j\delta_{jt}\). A strong pre-treatment match does not, on its own, rule out this post-treatment problem.
Worked Example: A Positive Spillover Shrinks the Estimated Gap
Suppose two donors each receive weight \(0.5\). At a post-treatment date, the treated unit’s untreated outcome would be 100, and its direct treatment effect is 12, so its observed outcome is \(100+12=112\). Without spillover, each donor’s outcome would be 100. Donor A instead receives a positive spillover of 10, while donor B is unexposed. Assume the synthetic control had a perfect untreated fit at this date: its weighted untreated donor outcome is \((0.5)(100)+(0.5)(100)=100\).
The observed donor outcomes are 110 for A and 100 for B. The observed synthetic outcome and treatment-effect gap are
The direct effect is 12, but the gap is 7. The weighted spillover is \((0.5)(10)+(0.5)(0)=5\), so the decomposition gives \(G_t=12-5=7\). The positive exposure in donor A raises the synthetic counterfactual by 5 outcome units and reduces the estimated gap by the same amount.
Diagnosing Exposure Before Re-estimating
Contamination is a substantive question about what happened to the donors, not a label assigned solely from their outcomes. Begin by specifying plausible channels through which treatment or related events could affect them. For a place-based policy, for example, nearby jurisdictions might receive displaced activity, share a labor market, or adopt a linked policy. For a sectoral intervention, suppliers, customers, or competing firms might be exposed even if they are outside the treated jurisdiction.
A disciplined diagnosis combines design information with outcome evidence. Record which donors have a plausible exposure pathway, when exposure could begin, and whether its likely direction is positive or negative for the outcome. Check policy records, geographic and network relationships, and other contemporaneous events. Then inspect donor outcomes over time for changes consistent with those channels. A post-treatment change can support a concern, but it cannot by itself establish that treatment caused the change.
Distinguish spillovers from shocks that are part of the relevant untreated counterfactual. A shock shared by the treated unit and otherwise appropriate donors may be represented by their common movement. By contrast, a shock that affects selected donors differently from the treated unit can distort the weighted comparison. The key issue is whether the donor’s post-treatment outcome still tracks the treated unit’s outcome under no direct treatment.
Exposure may vary by donor and time. A useful summary for each post-treatment date is the donor-weighted exposure component \(\sum_j w_j\delta_{jt}\), if credible estimates or bounds for the \(\delta_{jt}\) are available. In practice, spillover effects are rarely known exactly. The expression is therefore often best used to organize the reasoning: highly weighted donors with credible, large exposures deserve particular attention, while a small exposure in a donor with negligible weight may matter little for the fitted counterfactual.
Worked Example: Combining Opposite-Signed Exposures
Consider four donors with weights \(0.4, 0.3, 0.2,\) and \(0.1\). At one post-treatment date, suppose their spillover effects are \(+6, 0, -4,\) and \(0\) outcome units, respectively. Assume the untreated treated outcome and the weighted untreated donor outcome are both 50, so untreated fit error is zero. The treated unit’s direct effect is 8, giving an observed treated outcome of 58.
The observed donor outcomes are \(56, 50, 46,\) and \(50\). The observed synthetic outcome is
The observed gap is \(58-51.6=6.4\) outcome units. Directly applying the decomposition, the weighted exposure is
The negative spillover in the third donor partly offsets the positive spillover in the first. Looking only at whether any donor is exposed, or only at the sign of one exposure, would miss the net effect on the synthetic outcome. These calculations rely on the stipulated exposure effects and exact untreated fit; in an applied analysis, both are generally uncertain and must be treated as assumptions or sensitivity inputs.
Excluding Exposed Donors and Comparing Alternative Pools
When a donor has a credible exposure pathway, one response is to remove it and re-estimate the synthetic control using a donor pool defined to exclude that exposure. The weights should be re-estimated using pre-treatment data; simply setting an exposed donor’s weight to zero while leaving the other weights unchanged does not generally produce the best-fitting control for the revised pool. The resulting estimate is informative only if the remaining donors still offer a plausible comparison and achieve acceptable pre-treatment fit.
An alternative-pool analysis asks whether conclusions depend on defensible choices about donor eligibility. For example, compare a broad pool with a restricted pool that excludes jurisdictions connected to the treated unit. Apply the same outcome definition, treatment date, post-treatment window, and fitting procedure to each pool. Report the estimated gaps and their units, and assess pre-treatment fit for every specification. Material changes in the estimated effect indicate sensitivity to pool composition; they do not, by themselves, identify which estimate is correct.
The following sequence keeps the exercise focused on exposure rather than on arbitrary model variation:
List donor connections, policies, and shocks that could transmit treatment effects or create differential post-treatment changes.
State in advance which exposure criteria motivate exclusion or restriction, and apply them consistently rather than selecting a pool because it yields a preferred estimate.
Recalculate weights for each pool and examine whether the resulting synthetic control tracks the treated unit before treatment.
Report how the estimated gaps change across pools, alongside fit diagnostics and the reasons each pool is substantively defensible.
Worked Example: Sensitivity to an Exposure-Based Pool Restriction
Suppose a treated region has an observed outcome of 94 in a particular post-treatment year. A broad donor pool assigns weight \(0.6\) to a connected donor with outcome 90 and weight \(0.4\) to an unconnected donor with outcome 80. A restricted pool excludes the connected donor and uses two unconnected donors, with weights \(0.5\) and \(0.5\), and outcomes 80 and 84.
Under the broad pool, the synthetic outcome and gap are
Under the restricted pool, they are
The estimated gap is 4 outcome units larger under the restricted pool. This difference is evidence that the result depends on the pool choice, not proof that 12 is the true treatment effect. Before interpreting it, the analyst must check that the restricted pool fits the treated region comparably well before treatment and that the exclusions follow a credible exposure rule. The calculation alone cannot establish which donor pool gives the correct untreated counterfactual.
Interpretation, Limitations, and a Common Pitfall
A donor-exclusion or alternative-pool analysis is a sensitivity analysis, not a cure for weak identification. Excluding exposed donors can reduce a particular contamination risk, but may also remove the units that best reproduce the treated unit’s pre-treatment trajectory. Conversely, retaining a donor with excellent pre-treatment fit can be problematic if a post-treatment exposure makes its outcome diverge for reasons that would not have affected the treated unit in the absence of treatment.
Report both the substantive exposure rationale and the fit consequences of each pool. If an estimate changes substantially, describe that dependence plainly and consider whether the differences are consistent with the expected direction of contamination. If plausible exposure effects or outcomes are uncertain, avoid presenting a single adjusted number as if contamination had been measured and removed exactly. The uncertainty concerns the counterfactual construction as well as the estimated post-treatment gap.
- Common mistake: “Donor A had a large post-treatment increase, so it must be contaminated; removing it proves the larger estimate is the causal effect.”
- Correction: A change alone does not establish exposure or its cause. Use design and contextual evidence to justify exclusion, refit weights from pre-treatment data, check fit after exclusion, and interpret differences across plausible pools as sensitivity rather than proof.
Another mistake is to treat a small pre-treatment prediction error as a guarantee against spillovers. Pre-treatment fit describes how well the weighted donors reproduce the treated unit before intervention; it does not show that those donors remain unexposed afterward. The donor pool must be assessed on both dimensions.
Check Your Understanding
Use the decomposition and examples above to answer the following questions.
- If the donor-weighted spillover is \(-3\) outcome units and untreated fit error is zero, how does the observed gap compare with the direct treatment effect?
- Why does excellent pre-treatment fit fail to rule out donor contamination after treatment begins?
- Name two kinds of evidence, other than a donor’s post-treatment outcome change alone, that could support an exposure concern.
- Why should weights be re-estimated after restricting the donor pool?
- If alternative defensible donor pools yield different post-treatment gaps, what conclusion is warranted, and what conclusion is not warranted?