Synthetic control

An opinionated synthetic-control workflow grounded in a read canon (references/canon.md): Abadie's JEL survey, the practice manual by the method's originator, with the synthetic-DiD bridge and the DiD-vs-SC boundary supplied by the Arkhangelsky-Imbens panel survey (shared with the did skill). Deliverable: the recommendation with its citation, the R estimation and diagnostics code, and a methods paragraph. The skill stops at the four stop points in ../causal-design/references/shared-rules.md (section "Stop points") and puts each choice to the user.

Current as of 2026-10-09; refresh per shared-rules (../causal-design/references/shared-rules.md, section "Refresh path"). Nothing enters the canon without the user's approval.

Which precedent your design looks like

Design shape	Canonical case	Marketing analogue	What kills it
One treated region, outcome co-moves across regions	Basque terrorism (Abadie and Gardeazabal 2003)	a single-market launch	donors whose outcome does not co-move with the treated region
One treated unit, a regulation, other units running their own versions of it	California Prop 99 (Abadie, Diamond, and Hainmueller 2010)	a regulation hitting one state's category sales	already-treated donors left in the pool
One treated unit, pool restricted to genuine peers	German reunification (Abadie, Diamond, and Hainmueller 2015)	a platform policy change in one country	a pool wide enough that fit gets bought from dissimilar donors
Mid-pack treated unit, smooth series, long pre-period	Texas prison construction (Cunningham, The Mixtape, online ch. 11 sec. 11.1)	a geo rollout in one DMA	a treated unit at the top or the bottom of the donor range
Comparison units picked by hand and defended in a footnote	Mariel Boatlift (Card 1990; Peri and Yasenov 2019)	a hand-picked matched-market holdout	no test exists on the hand-picked choice. Synthetic control replaces it

references/canon.md (section "Exemplar rows") carries the sources behind each row.

The boundary: DiD, SC, or synthetic DiD

Settle this before the feasibility gate and the donor pool. One continuous decision path, not competing methods:

DiD is the special case of the SC factor model with constant factor loadings. If the treated unit's pre-trend parallels a plausible comparison average, use did, provided more than one unit is treated. With one treated cluster, the cluster-level methods fail: CV1, CV3, and the wild cluster bootstrap. Prefer this skill, after aggregating the micro units to the treated unit, or did's Fallback B, the cluster-level Fisher randomization test. When neither is feasible, use one of the two rescues on did's map: Ferman-Pinto, under its heteroskedasticity restriction, or the ordinary wild restricted bootstrap with observation-level weights. Long pre-periods are key for SC identification. DiD needs one pre-period to identify the ATT and more only for credibility, so the SC pre-period gate does not transfer to a DiD routing decision.
When the pre-period plot shows the donor average diverging from the treated unit before treatment, parallel trends has already failed and SC is the tool. The sharpest known routing result: under selection on lagged outcomes with autocorrelated errors, DiD is inconsistent even as the pre-period grows while SC is consistent (Arkhangelsky and Hirshberg 2023, arXiv 2311.13575). If units select into treatment on recent outcomes, that is the SC regime.
Synthetic DiD is SC with unit weights plus analogous time weights and a DiD-style adjustment: it does not require the pre-fit to be perfect, it differences the remaining gap out. The price is a stable-bias assumption on that gap. In simulations calibrated to real panels, SDID typically outperforms DiD, SC, and matrix completion. Practical default: run canonical SC when the gate passes cleanly; when level fit is the sticking point, move to SDID and say why. Reporting discipline: plot the time weights beside the trajectory figure so readers see which pre-years carry the counterfactual, and plot the unit weights so they see which donors do. The intercept weakens the visual pre-fit check (scripts/synth_template.R, section 7). The four assumptions SDID actually makes are in references/details.md.
Staggered adoption forecloses the standard SC estimator. With a few treated units, first try the staggered SC routes. One is scpi's prediction intervals for multiple treated units and staggered adoption (Cattaneo, Feng, Palomba, and Titiunik 2025, REStat, cattaneo2025uncertainty; the package is cattaneo2025scpi). The other is stagsynth, which implements Cao, Lu, and Wu (2026). With many treated units it is did territory, or multisynth (Ben-Michael, Feller, and Rothstein 2022) and the factor-model estimators below. Staggered SDID is the exception. Its sources are section 8 of arXiv v4 of Arkhangelsky et al. (2021) and section 2.3 of the Stata Journal SDID article (Clarke, Pailanir, Athey, and Imbens 2024). Porreca (2022) and the sequential SDID of Arkhangelsky and Samkov (2024) extend it. No CRAN package covers staggered SDID; the sources and code links are in references/details.md.

The feasibility gate: is SC usable here at all?

The method's originator is explicit that mechanical applications are risky and that there are situations where the honest answer is to walk away. Check before estimating:

One or a few treated AGGREGATE units (state, market, country, category), a donor pool of genuinely comparable untreated units, and outcomes that co-move across units.
A long pre-period. But a long T0 cannot repair a bad fit: the bias bound is derived under (near-)perfect predictor fit. When pre-period fit is poor, do not use canonical SC. Take the imperfect-fit routes instead: SDID (boundary section) or augmented SC (Extensions).
Enough post-intervention periods. Abadie (2021, sections 5 and 6) warns that effects can take time to emerge. His remedies are waiting for more post-period data or using surrogate outcomes, and he gives no count. This skill's judgment: a long pre-period with two post-periods does not pass this gate.
The converse trap: good pre-period fit with a short T0 or a noisy outcome can be spurious overfitting on transitory shocks, and a larger donor pool makes overfitting easier, so a bigger J is not automatically better. Abadie (2021, footnote 9) adds that a large J can help when T0 is also large (Ferman 2021). The rule targets dissimilar donors; a small pool is not safer by itself.
The expected effect must be large relative to unit-specific outcome volatility. Compare the effect you expect against the treated unit's pre-period residual volatility (for instance the pre-period RMSPE, or the outcome's detrended SD) and report that comparison. Sales and attention data are volatile, and when the effect is not clearly larger, pre-filter unit-specific noise (denoising a la robust SC) or concede the effect is undetectable. The judgment and its basis go in the writeup.
No anticipation, or shift T0 earlier than any plausible anticipation. Backdating does not mechanically bias the per-period effects, because the effect path is unrestricted (Abadie 2021, section 5). It has two costs. An averaged post-period effect now includes null periods, and the pre-period left for fitting and for the overfitting screen gets shorter. Forward-buying before an announced price change is the marketing version of the problem.
No interference: donors exposed to the treatment (neighboring markets, national campaign spillover) are handled in design (drop them, check the fit cost) or kept with the bias signed and the estimate reported as a bound.
The treated unit should be plausibly inside the donors' convex hull; weights are nonnegative and sum to one, so SC never extrapolates. Extreme treated units in levels need an outcome transformation (differences, growth rates, pre-mean deviations) or SDID, and differencing inflates the noise share of variance, which raises overfitting risk.
A treated unit that is the largest unit in the panel (a national market, the top platform) fails the convex-hull bullet by construction, and no donor mix reaches its level. First try the outcome transformation, SDID, or augmented DiD (the extensions map below). When the level itself is the estimand, use CausalImpact (its own series plus unaffected covariates), or HCW OLS (unconstrained regression weights) when donors are few relative to pre-periods. The price: both give up the no-extrapolation guarantee, so the counterfactual is an extrapolation the reader has to accept.

When the gate fails, first check the extensions map. Too short a pre-period points to forward DiD, a treated outcome outside the convex hull to augmented DiD, and few donors relative to pre-periods to HCW OLS. When none fits, say so, decline to estimate, and route back to causal-design.

Donor pool discipline

Exclude donors treated with similar interventions in the window, donors hit by large idiosyncratic shocks that would not have hit the treated unit, and donors dissimilar on observed or suspected unobserved attributes. The canon's line: including units the analyst regards as unsuitable controls "is a recipe for bias." The worked precedents: dropping US states with their own tobacco programs (Prop 99), restricting the reunification donor pool to OECD economies.

Estimator anatomy and researcher degrees of freedom

The counterfactual is a convex combination of donors chosen so the synthetic unit matches the treated unit's pre-intervention predictors, with predictor-importance weights V. The constraints buy transparency and sparsity. Suppose the treated unit lies outside the donors' convex hull and the donor columns are in general position. Then at most k donors get positive weight (Abadie 2021, section 5), and you can name them. Panel regression on the same data is implicitly a synthetic control whose weights sum to one but can be negative, so it extrapolates silently. In Abadie's (2021) reunification example with a 16-country pool, four donor countries get negative regression weights.

The degrees of freedom, each with a discipline:

Predictors: pre-intervention outcomes PLUS substantive covariates. Pre-outcomes alone push excluded covariates into the unobserved loadings and raise the bias bound. Including the entire pre-treatment outcome path as predictors has become increasingly popular (Kaul, Klößner, Pfeifer, and Schieler 2022, JBES 40(3): 1362-1376). This skill rejects the drift because the excluded covariates are what inflate Abadie's bias bound. Kaul et al. also show that entering every pre-period outcome as a separate predictor makes all covariates irrelevant to the weights. Use a few pre-period outcome summaries (window means, selected years), never all lags as the main specification. Report the all-lags fit beside it as the benchmark that Ferman, Pinto, and Possebom (2020) recommend. The exception is an outcome series known to be driven by strongly co-moving common factors, which is why one pre-period average sufficed for reunification.
V: inverse-variance as the simple default; better, minimize pre-period MSPE or pick V by a training/validation split of the pre-period. Cross-validated V is not always unique, so show the estimate is stable across reasonable V choices.
Weights are computed from pre-intervention data only, so the design can be locked, even preregistered, before post-treatment outcomes are seen; the canon compares this to a pre-analysis plan. Use that: fix the specification before looking at effects.

Stop before fitting. Present the donor pool, the predictor set, and the V choice to the user, each with its reason. This is the "before estimation" stop point in shared-rules.md.

Inference

The primary mode is design-based permutation, honest about its limits:

In-space placebos: reassign treatment to each donor, refit, pool the gaps. The test statistic is the post/pre RMSPE ratio, which corrects for placebos that fit badly pre-period; p is the treated unit's rank among J+1 ratios. Report the spaghetti plot of placebo gaps, never only p; the plot carries the magnitude.
The smallest attainable p is 1/(J+1). A tiny donor pool cannot deliver conventional significance, and pretending otherwise is the error. One-sided versions of the statistic add real power in small pools.
Uniform permutation is a benchmark, not a model of assignment; sensitivity to non-uniform assignment and test-inversion confidence sets exist (Firpo-Possebom).
Model-based complements when intervals are wanted: conformal inference (Chernozhukov et al.) and prediction intervals (scpi). For SDID, placebo, jackknife, and bootstrap variance estimators ship with the estimator. The data-shape conditions for choosing among them are in references/details.md.

Diagnostics battery

Pre-period fit, the entry gate: table the treated unit's predictor values against the synthetic unit's and plot both trajectories over the whole pre-period. Visible gaps in either mean do not proceed (tighten the pool, change predictors or transformation, bias-correct, move to SDID, or abandon). The balance table has one value per variable per group, so it is a display, not a test. Li and Shankar (2024) give a formal test of the SC pretrends assumption, with a second step that picks the estimator. Report it beside the plot when a marketing referee will ask for a test.
Backdating (in-time placebo, the Heckman-Hotz preprogram test): move the intervention date back, re-estimate on pre-data only. Pass has two parts: no effect opens during the fake post-period, and the gap still opens at the true date with the same sign and shape. A pre-gap estimates the bias's direction and size. Caveat carried from the panel survey: backdating assumes strict exogeneity and backfires under selection on recent shocks (the AMA Marketing News routing source (Li, Luo, and Pattabhiramaiah 2024; AMA (causal-design canon)) states this exercise as one of two mandatory best practices; the strict-exogeneity caveat here governs when it is informative).
In-space placebos with the RMSPE ratio (above).
Leave-one-out on positive-weight donors: refit dropping each in turn; the conclusion must not hinge on one donor. When it does, check whether that donor had its own intervention or shock.
Robustness across predictor sets, V choices, and tightened donor pools; drift as the pool tightens signals interpolation bias from dissimilar donors. Searching over pre-treatment lag choices raises the false-positive rate (Ferman, Pinto, and Possebom 2020), so pre-commit the predictor set or report every specification tried, with the all-lags fit as the benchmark. A test across all specifications is valid only with a combined test statistic (Ferman, Pinto, and Possebom 2020, p. 522).
Outcome-transformation check when levels are hard to match (levels vs differences vs growth rates vs pre-mean deviations), remembering the noise-amplification tradeoff and that matching changes alone is not credible when the level itself drives dynamics.
Spillover accounting: with and without exposed donors; when kept, sign the bias and interpret the estimate as a bound.

Extensions, and when to reach for them

Imperfect fit on a unit that must stay in: bias-corrected/augmented SC (ridge outcome model on the residuals; augsynth), or penalized SC.
Many treated or disaggregated units: one SC per treated unit, aggregated; the penalized estimator (pensynth) restores uniqueness and sparsity for inside-the-hull units and spans pure SC to one-to-one matching; multisynth handles staggered timing.
Both N and T modestly large: interactive fixed effects and matrix completion (gsynth, fect, MC-NNM) relax the convex-combination restriction entirely; the panel survey's unified view is that DiD, SC, unconfoundedness, and matrix completion are one imputation objective under different restrictions, so divergence across them is diagnostic.
Volatile single-market outcomes with a Bayesian time-series counterfactual: CausalImpact (Brodersen et al. 2015). Abadie (2021) lists it among related work he does not cover. Treat its output with this skill's diagnostics, and note that its counterfactual leans on one unit's own time series plus covariates.
SC-type weights with many controls and few pre-periods need regularization; unregularized in-sample fit can be perfect and meaningless.
Treated outcome outside the donor convex hull: augmented DiD (Li and Van den Bulte 2023). Too few pre-periods: forward DiD (Li 2024); controls far fewer than pre-periods: HCW OLS (Hsiao, Ching, and Wan 2012). Fuller map in references/details.md.

Choosing treated markets before a geo test

When the treated markets are not yet chosen and only one or a few can be treated, the synthetic control design picks treated and comparison markets jointly (Abadie and Zhao 2026). They show that with aggregate units this design can reduce bias substantially relative to randomizing treatment. GeoLift (github.com/facebookincubator/GeoLift, built on augsynth) is the practitioner tool for this step, with market selection and power calculators. It does not implement Abadie and Zhao's estimator. This skill owns that design step. Randomized geo experiments belong to field-experiment.

R implementation

The complete runnable pipeline is scripts/synth_template.R (canonical SC with the full diagnostics battery, SDID, augmented and penalized variants, factor-model robustness, conformal and prediction intervals), with every call verified against package documentation. The core:

library(tidysynth)                       # canonical ADH workflow with built-in placebos
out <- df |>
  synthetic_control(outcome = y, unit = unit, time = year,
                    i_unit = "TREATED", i_time = T0, generate_placebos = TRUE) |>
  generate_predictor(time_window = pre_window, ...) |>
  generate_weights(optimization_window = pre_window) |>
  generate_control()
plot_trends(out); plot_placebos(out); grab_significance(out)   # RMSPE-ratio table

library(synthdid)                        # the SDID branch
setup <- panel.matrices(panel, unit = "unit", time = "year",
                        outcome = "y", treatment = "treated")
tau <- synthdid_estimate(setup$Y, setup$N0, setup$T0)
sqrt(vcov(tau, method = "placebo"))

Package index with versions, links, and traps in references/details.md.

Methods paragraph template

Report each effect with the results sentence in ../causal-design/references/shared-rules.md (section "Results sentence"): magnitude, direction, a benchmark, and the calibration vocabulary.

[Treatment] hit [treated unit] at [date]; no comparable unit did, so I construct a synthetic control from [J] donors, excluding [units] for [own interventions / shocks / spillovers] (Abadie 2021). Predictors are [pre-period outcomes and covariates]; predictor weights are chosen by [cross-validation on the pre-period], and the resulting synthetic unit puts weight on [named donors]. Pre-period fit is [shown in table/figure]. The estimated effect of [effect] compares with a pre-period [RMSPE / detrended SD] of [value] for [treated unit]. I report permutation inference with the post/pre RMSPE ratio over in-space placebos (Abadie, Diamond, and Hainmueller 2010); with [J] donors the smallest attainable p is 1/(J+1), [which is a limitation of the donor count: statistical significance in the conventional sense is out of reach, and I lean on magnitude and the placebo distribution]. I validate with backdating, leave-one-out donor exclusion, and robustness across predictor sets and donor pools. [If fit is imperfect: because the synthetic unit cannot match pre-period levels exactly, I use synthetic difference-in-differences (Arkhangelsky et al. 2021), which differences out the remaining gap; I note this trades the perfect-fit requirement for the assumption that the gap would have been stable, which I cannot test directly.] The estimand is the effect on [treated unit] alone, and I generalize to [other units] only [not at all / under the stated assumption].

Most claims trace to references/canon.md; keys live in ../causal-design/references/causal.bib.

Handoffs

did: parallel pre-trends hold with two or more treated units, or staggered adoption with many treated units; synthetic DiD lives HERE, did points back for it.
causal-design: whether any panel counterfactual is credible; the taxonomy that routes between did, SC, and factor models.
rdd: policy-date designs masquerading as RD in time arrive here when one or a few aggregate units switch at a date; treat the date as the event, not a cutoff.
field-experiment: randomized geo experiments and customer-level experiments. Choosing treated markets by synthetic control before a geo test stays here (section "Choosing treated markets before a geo test").
Preregistration: the user writes it themselves; this skill supplies the fields to lock (donor pool, weights, specification) before post-period outcomes exist.

synthetic-control

Files4

SKILL.mdskills/synthetic-control/SKILL.md