git:20261009.cbae15b to git:20261009.2e28914

---

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", "augmented synthetic control", "augsynth", "synthdid", "scpi", "generalized synthetic control", "fect", "penalized synthetic control", "augmented DiD", "forward DiD", "GeoLift", 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, including picking treated markets by synthetic control before a geo test. Many treated units with staggered timing belong to did; randomized geo experiments to field-experiment.

---

# Synthetic control

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.

## 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 |

## 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

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. 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.

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

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, 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).

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

(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.

## 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:

```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

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.