Synthetic Control

---
name: synthetic-control
description: Design, estimate, validate, and write up a synthetic control analysis, including synthetic difference-in-differences, augmented and penalized variants, and factor-model/matrix-completion relatives for panel counterfactuals. TRIGGER on "synthetic control", "synthetic DiD", "SDID", "donor pool", "comparative case study", "geo holdout", "CausalImpact", "matrix completion", "interactive fixed effects", "gsynth", or any setting where one or a few aggregate units (a state, market, DMA, category, platform region) got treated and untreated units must form the counterfactual. Many treated units with staggered timing belong to did; choosing treatment markets prospectively to field-experiment.
---

# Synthetic control

An opinionated synthetic-control workflow grounded in a read canon (references/canon.md,
current as of 2026-07-28): 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.

Refresh path: run litreview on the method since the canon date, then propose additions to
references/canon.md as flagged addenda.

## 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 (the Mixtape's data exercise) | 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/details.md carries what each case is the precedent for.

## 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, and when pre-period fit is poor the recommendation is to not
  use synthetic control, full stop.
- Enough post-intervention periods. Abadie, Diamond, and Hainmueller (2015) also require a
  sizable number of them when the effect emerges gradually after the intervention or changes
  over time, so 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.
- 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 (harmless if too
  early, because the effect path is unrestricted). 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.

When the gate fails, say so and decline to estimate; route back to causal-design. When the
gate fails on pre-period length or convex-hull grounds, check the extensions map (forward
DiD, augmented DiD, HCW) before declining and routing back.

## 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: at most k donors get positive weight, 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 (four donor countries get negative
regression weights in the reunification example).

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. The Mixtape
  (Cunningham, Causal Inference: The Remix, synthetic-control chapter) reports that
  researchers increasingly rely solely on lagged outcomes as covariates (Ben-Michael, Feller,
  and Rothstein 2021); this skill rejects the drift because the excluded covariates are what
  inflate Abadie's bias bound. 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.

## The boundary: DiD, SC, or synthetic DiD

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. 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-Hirshberg,
  via the panel survey). 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 means the treated and synthetic series will not overlay,
  so the visual pre-fit check canonical SC leans on is weaker here. No accepted substitute
  exists yet. The four assumptions SDID actually makes are in references/details.md.
- Staggered adoption with many treated units forecloses the standard SC estimator; that is
  did territory (or multisynth / the factor-model estimators, below). Staggered SDID is the
  exception: the appendix of Arkhangelsky et al. (2021), section 2.3 of the
  Stata Journal SDID article (Clarke, Pailanir, Athey, and Imbens 2024), and Porreca (2022).
  No CRAN package covers it. Porreca ships code at
  github.com/zachporreca/staggered_adoption_synthdid.

## 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

1. 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.
2. 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' hereafter)
   states this exercise as one of two mandatory best practices; the strict-exogeneity caveat
   here governs when it is informative).
3. In-space placebos with the RMSPE ratio (above).
4. 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.
5. 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.
6. 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.
7. 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,
  the tool marketing analytics teams usually already run for geo tests; the canon situates
  it among SC relatives, so treat its output with this skill's diagnostics, and note 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),
  a different method from Ben-Michael's ridge-augmented SC in augsynth despite the
  near-identical name. 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.

## 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:

```r
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

> [Treatment] hit [treated unit] at [date]; no comparable unit did, so we 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]. We 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 design, not the method: statistical significance in the
> conventional sense is out of reach and we lean on magnitude and the placebo distribution].
> We 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, we 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].

Every claim traces to references/canon.md; keys live in ../causal-design/references/causal.bib.

## Handoffs

- did: parallel pre-trends hold, 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: prospective geo experiments (choosing treatment markets by design rather
  than analyzing one after the fact).
- preregister: locking weights and specification before post-period outcomes exist.