When a perfect pre-treatment fit means nothing

A synthetic control that tracks the treated unit exactly before the intervention looks like the best possible outcome. Sometimes it carries less information than it appears to: the fit criterion may be satisfied by a whole family of donor weightings that disagree about the counterfactual, in which case the number you are about to report was settled by your solver rather than by your panel.

This page explains when that happens, how to check for it in a few lines, and what to do about it. It is written around a published example, so the failure is concrete rather than hypothetical.

The problem

The classical synthetic control picks donor weights by solving

\[\min_{w}\; \big\| y_1 - Y_0 w \big\|^2 \quad\text{subject to}\quad w_j \ge 0,\; \sum_j w_j = 1,\]

where \(y_1\) is the treated unit’s pre-treatment path over \(T_0\) periods and \(Y_0\) holds the \(J\) donors’ paths. This is a convex quadratic program, so the optimal value is unique. The optimal weights need not be.

Count the constraints. Matching the pre-treatment path exactly imposes \(T_0\) equations, and the weights must sum to one, so \(T_0 + 1\) equations in \(J\) unknowns. When \(J\) comfortably exceeds \(T_0 + 1\) and the treated unit lies inside the donors’ convex hull, the set of weight vectors achieving a perfect fit is not a point but a polytope of dimension \(J - T_0 - 1\). Every point in it reproduces the pre-treatment path exactly and none of them is preferred by the objective.

Those weight vectors do not agree after treatment. They generally imply different counterfactuals, and therefore different estimated effects. The optimiser returns one of them, determined by its starting point and its internal path — not by the data.

This is not an edge case in the wide-panel regime. It is the generic outcome whenever a large donor pool is matched on a short pre-period, and a perfect pre-treatment fit is its signature rather than its refutation.

A caveat worth stating immediately, because it changes what to conclude: none of this says a large donor pool is bad. See Adding donors is not the problem below. What it says is that the objective stops choosing for you, so something else must — and you should know what.

Diagnosing it

The check is direct. If the pre-treatment fit is (near) exact, ask what range of post-treatment effects is consistent with an exact fit. That is a linear program: maximise and minimise the synthetic post-treatment outcome over the same feasible set,

\[\max_{w} \;/\; \min_{w} \;\; c' w \quad\text{subject to}\quad Y_0^{\text{pre}} w = y_1^{\text{pre}},\; \textstyle\sum_j w_j = 1,\; w \ge 0,\]

where \(c\) holds each donor’s mean outcome over the post-treatment periods. The spread between the two solutions is the range of effects the fit criterion cannot distinguish. If the program is infeasible, the treated unit lies outside the donors’ hull, which is a different problem (see below).

import numpy as np
from scipy.optimize import linprog

def identified_interval(y1_pre, Y0_pre, y1_post, Y0_post):
    """Range of post-treatment effects consistent with an exact pre-fit.

    y1_pre : (T0,)      treated pre-treatment path
    Y0_pre : (T0, J)    donor pre-treatment paths
    y1_post, Y0_post    the same over the post-treatment periods

    Returns (low, high), or None if exact interpolation is infeasible
    (the treated unit is outside the donors' convex hull).
    """
    J = Y0_pre.shape[1]
    A_eq = np.vstack([Y0_pre, np.ones(J)])
    b_eq = np.append(y1_pre, 1.0)
    c = Y0_post.mean(axis=0)                 # synthetic post-treatment mean
    lo = linprog(c,  A_eq=A_eq, b_eq=b_eq, bounds=(0, 1), method="highs")
    hi = linprog(-c, A_eq=A_eq, b_eq=b_eq, bounds=(0, 1), method="highs")
    if not (lo.success and hi.success):
        return None
    observed = y1_post.mean()
    return observed + hi.fun, observed - lo.fun

Run it whenever pre_rmse is near zero and the donor pool is large relative to the pre-period. A narrow interval means the fit pins the counterfactual down; a wide one means it does not, and no amount of solver tuning will change that – only a stated rule for choosing among the tied solutions will.

Adding donors is not the problem

It would be easy to read the above as an argument for small donor pools. It is not, and the evidence points the other way.

Spiess, Imbens and Venugopal (2023) study exactly this regime and find that synthetic control exhibits single descent: average out-of-time imputation error falls monotonically as control units are added, with no deterioration at or past the point where the pre-treatment fit becomes perfect. Their Proposition 4 gives the mechanism – because the weights are convex, a synthetic control built from \(J\) donors is itself a convex combination of the fits built from \(J - 1\) of them, so a larger pool behaves like a model average over smaller ones. The result holds with or without interpolation, and they note it extends to penalized synthetic control at a fixed penalty.

Their conclusion is explicit that the conventional worry is misplaced – but so is its condition, and the condition is the whole point of this page: the result holds as long as ties are broken by a suitable regularisation procedure, the minimum-norm solution in their case. Non-uniqueness is not denied; it is assumed away by fixing a rule.

So the two readings fit together. The polytope is real, and which point you land on is not determined by fit. What follows is not “use fewer donors” but “decide the rule, and report it” – and given a rule, more donors can help rather than hurt.

How much does the rule matter? On the panel below, every one of these tracks the pre-treatment path to within about thirteen cents a month, on contributions averaging some $66,000 a month:

Tie-breaking rule	Donors used	Effect (four-month)
minimum norm (Spiess et al.)	47	$113,700
Abadie-L’Hour penalty, \(\lambda = 10^{-6}\)	10	$124,600
mlsynth’s interior-point default	98	$126,800
the original study’s general-purpose NLP solver	96	$130,500

A spread of about $17,000 across four defensible-looking routes, none of which is meaningfully distinguishable on pre-treatment fit. Note what the last row is not: an argument that its answer is wrong. It is that nothing in that analysis names the rule, so the number came from an optimiser’s path rather than from a modelling choice anyone made deliberately.

Two things this comparison does not show. Spiess et al. measure average imputation risk over randomly chosen donor subsets, which is a different question from the spread of estimates at a fixed donor set – their result can hold while this interval stays wide. And mlsynth’s own outcome-only default is an interior-point solution: deterministic and reproducible, but a solver artifact rather than a rule anyone chose. If the identified interval is wide, choose the rule explicitly rather than inheriting that one.

A worked example

Van Parys (2026) studies whether the two Senate holdouts on the Build Back Better Act received more campaign contributions than they otherwise would have. The design is a synthetic control on monthly PAC contributions, matching on all nine pre-treatment months with no covariates — the Doudchenko-Imbens constrained regression, which is VanillaSC(backend="outcome-only") in mlsynth. The donor pool is the rest of the Senate, so \(J = 98\) against \(T_0 = 9\).

For Kyrsten Sinema the pre-treatment fit is essentially perfect, and the interpolation polytope has dimension \(98 - 10 = 88\). Applying the check above, weight vectors that fit the pre-treatment path to machine precision imply four-month effects anywhere from about $36,600 to $180,800. The published figure, near $130,000, sits inside that range — but so does an estimate a fifth its size.

The author anticipated the concern and ran the donor-trimming robustness check of Abadie and Vives-i-Bastida, which is the right instinct: restricting the pool shrinks the polytope. Re-running the diagnostic across his trim levels shows how sharply that bites.

Donor pool	Identified interval (four-month total)	Width
top 10 / 30 / 50	exact interpolation infeasible — an ordinary identified fit	–
top 70	$128,600 – $135,300	$6,700
top 90	$59,800 – $180,800	$121,000
all 98 (headline)	$36,600 – $180,800	$144,200

The trimmed specifications are identified and cluster tightly, and they agree with the headline. The substantive conclusion survives — but it survives on the robustness check rather than on the main specification, which by itself identifies the sign and not the magnitude. That distinction is worth making explicitly in any write-up, and it is exactly what the diagnostic surfaces.

What to do about it

Penalise. Abadie and L’Hour (2021) add a pairwise matching penalty to the same program,

\[\min_{w}\; \big\| y_1 - Y_0 w \big\|^2 \;+\; \lambda \sum_j w_j \big\| y_1 - Y_{0,j} \big\|^2 ,\]

and their Theorem 1 says that for any \(\lambda > 0\) the solution is unique, with at most \(T_0 + 1\) non-zero weights. Among the weight vectors that fit equally well, it selects the one built from donors individually close to the treated unit — the least interpolation bias. In mlsynth that is backend="penalized", and it needs no covariates: the pre-treatment outcome lags are the matching variables.

On the panel above, an essentially infinitesimal penalty is enough to restore uniqueness at no meaningful cost in fit:

Specification	Donors	Pre-treatment RMSE	Effect (four-month)
outcome-only	98	0.00	$126,800
penalized, \(\lambda = 10^{-6}\)	10	0.13	$124,600
penalized, \(\lambda = 10^{-2}\)	9	984	$122,700

Ten donors at \(\lambda = 10^{-6}\) is exactly the \(T_0 + 1\) bound, and the estimate is stable across four orders of magnitude of \(\lambda\).

Three other routes are worth knowing:

Trim the donor pool, as above, following Abadie and Vives-i-Bastida — the simplest fix and the one to reach for when a principled similarity ranking is available.

Shrink instead of interpolating. The high-dimensional estimators exist for this regime: see Cluster Synthetic Controls (CLUSTERSC), Sparse Synthetic Control (SparseSC), Relaxed / Penalized Synthetic Control (RESCM), Forward-Selected Synthetic Control (FSCM) and Bayesian Synthetic Control with a Soft Simplex Constraint (BVS-SS), and Q1.6 of A practitioner’s decision tree.

Do not reach for Matching and Synthetic Control (MASC) here. It trades extrapolation bias against interpolation bias and is the right tool when the hull condition fails. That is the opposite problem: too few fits rather than too many.

The other failure

The diagnostic returns None when exact interpolation is infeasible, which means the treated unit is outside the donors’ convex hull. Nothing is under-determined then — the fit is a genuine constrained least-squares problem with a well-defined solution — but the pre-treatment fit will be poor and the convex-hull condition that motivates synthetic control does not hold.

In the same study, the second treated senator is in exactly that position: exact interpolation is infeasible at every donor-pool size, and his pre-treatment RMSE is roughly $12,600 on an outcome of that order. A poor pre-treatment fit is easier to notice than a suspiciously perfect one, which is part of why the perfect-fit case deserves a deliberate check.

References

Abadie, A., and J. L’Hour (2021). “A Penalized Synthetic Control Estimator for Disaggregated Data.” Journal of the American Statistical Association 116(536), 1817-1834.

Abadie, A., and J. Vives-i-Bastida (2022). “Synthetic Controls in Action.” arXiv:2203.06279.

Spiess, J., G. Imbens, and A. Venugopal (2023). “Double and Single Descent in Causal Inference with an Application to High-Dimensional Synthetic Control.” Advances in Neural Information Processing Systems 36.

Doudchenko, N., and G. W. Imbens (2016). “Balancing, Regression, Difference-in-Differences and Synthetic Control Methods: A Synthesis.” NBER Working Paper 22791.

Van Parys, A. (2026). “Vote Buying and Negative Agenda Control: A Problem for the Study of Money in Politics.” American Journal of Political Science.