Module 8: Matrix Completion and the Modern Panel Toolbox

The course closes where panel causal inference is heading: treat the whole problem as missing data. Athey, Bayati, Doudchenko, Imbens and Khosravi (2021) show that TWFE (Module 1), the heterogeneity-robust DiD estimators (Module 2), synthetic control (Module 4) and synthetic DiD (Module 5) are all, underneath, rules for filling in a matrix of untreated potential outcomes. Matrix completion (MC-NNM) is the member of that family that imposes the least structure: it works on any missingness pattern, including the irregular ones none of the earlier estimators can handle.

The imputation view

Every panel causal problem has a matrix of potential outcomes under control, $Y_{it}(0)$, for units $i = 1, \dots, N$ and periods $t = 1, \dots, T$. You observe $Y_{it}(0)$ for control cells; for treated cells it is missing, not caused by treatment, simply unobserved. Once you have an estimate $\hat Y_{it}(0)$ for every missing cell, the ATT falls out directly:

$$\widehat{ATT} = \frac{1}{|\mathcal{M}|}\sum_{(i,t) \in \mathcal{M}} \big(Y_{it} - \hat Y_{it}(0)\big)$$

where $\mathcal{M}$ is the set of treated (missing) cells. Every course estimator differs only in how it fills those cells:

• TWFE / DiD fills a missing cell with $\hat\alpha_i + \hat\beta_t$: a pure two-way fixed-effects imputation, no interactive structure at all.
• Synthetic control fills a treated unit's missing cells with a convex combination of donor units' outcomes at the same period.
• Synthetic DiD fills them with a weighted two-way FE fit, unit weights matching pre-period shape, time weights matching post-period relevance.
• gsynth / interactive fixed effects (IFE) fills them with a factor model of fixed rank $r$, chosen by cross-validation.
• Matrix completion (MC-NNM) fills them with a low-rank matrix whose effective rank is chosen continuously, by nuclear-norm shrinkage.

The missingness pattern itself varies by application: one unit going missing in a block at the end of the panel (single-market policy change), many units in one simultaneous block (a coordinated rollout), staggered absorbing missingness (a rollout ops schedule city by city), or genuinely irregular missingness (data gaps plus treatment, or treatment on-again off-again). Only matrix completion handles the last case; the others require some form of block or absorbing structure.

The MC-NNM estimator

Let $\mathcal{O}$ denote the observed (untreated) cells. The estimator solves for a low-rank matrix $L$ and unpenalized two-way fixed effects jointly:

$$\min_{L,\, \alpha,\, \beta}\; \frac{1}{|\mathcal{O}|} \sum_{(i,t) \in \mathcal{O}} \big(Y_{it} - L_{it} - \alpha_i - \beta_t\big)^2 + \lambda \lVert L \rVert_*$$

Two design choices matter as much as the objective itself:

1. The fixed effects are not penalized. $\alpha_i$ and $\beta_t$ absorb level and trend structure every unit or every period shares. Leaving them inside $L$ would force the nuclear-norm penalty to pay for that shared structure, wasting rank budget that should go to the genuinely interactive (unit-by-time) part of the residual.
2. $\lambda$ is chosen by cross-validation on the observed cells only. Hide a random subset of observed control cells, refit, and pick the $\lambda$ that best predicts the held-out subset. The treated cells are never part of this CV loop, which is exactly why the estimator can under-extrapolate into them (see below).

Given $\hat L, \hat\alpha, \hat\beta$, the counterfactual for every missing cell is $\hat Y_{it}(0) = \hat L_{it} + \hat\alpha_i + \hat\beta_t$, and the ATT is the average gap over the treated cells.

Why the nuclear norm

Minimizing the rank of $L$ directly is combinatorial and NP-hard in general. The nuclear norm

$$\lVert L \rVert_* = \sum_k \sigma_k(L)$$

(the sum of $L$'s singular values) is its convex relaxation, playing the same role for a matrix that the lasso's $\ell_1$ penalty plays for a vector: it shrinks every singular value toward zero and sets the smallest ones exactly to zero, choosing the effective rank of $L$ continuously rather than fixing it in advance.

The soft-impute algorithm

Mazumder, Hastie and Tibshirani (2010) give a simple fixed-point algorithm. Starting from $L = 0$: fill the missing cells of the (FE-residualized) outcome matrix with the current $L$, take an SVD of the filled matrix, soft-threshold every singular value by $\lambda$ (subtract $\lambda$, floor at zero), reassemble $L$ from the thresholded SVD, and repeat to a fixed point. Each step is an exact solution to a proximal problem, $\min_L \tfrac12 \lVert Z - L \rVert_F^2 + \lambda \lVert L \rVert_*$, so the iteration is a majorize-minimize scheme that provably converges to the minimizer of the nuclear-norm objective over the observed cells. The exercise hand-codes this loop and checks it against gsynth(estimator = "mc").

One family: SC, SDID, gsynth, MC-NNM

Athey et al.'s own framing is useful for interviews: SC-style estimators run "horizontal" regressions, exploiting similarity across units at a given time; DiD-style estimators run "vertical" regressions, exploiting similarity across time for a given unit. Matrix completion is the member of the family that uses both directions simultaneously, through the two-way fixed effects plus a shared low-rank residual structure.

What the demos show

Demo A (a staggered launch with selection on growth). 60 cities, 40 weeks, two latent factors (a mildly trending, persistent market factor and a seasonal factor) with city-specific loadings. Ops launch the fastest-growing (highest-loading) cities first, so launch timing correlates with the trending factor by construction; parallel trends is false. 25 treated cities across 12 distinct launch weeks, 35 never-treated. True effect 2.0.

TWFE and CS both inherit the launch-timing selection bias. Fixed-rank IFE, because the true factor structure is exactly rank 2 and CV finds it, recovers the truth almost exactly. Matrix completion, whether via gsynth's own mc estimator or the hand-coded soft-impute (the two agree to within 0.01), lands close to the TWFE answer, not the truth.

Why. Cross-validation for $\lambda$ only ever sees observed control cells; it never sees the treated corner it is asked to predict. Shrinking singular values flattens exactly the growth-factor divergence that needs to be extrapolated into that corner. A noiseless version of the same DGP (zero noise, no treatment effect, so any imputation error is pure extrapolation bias) makes the point starkly: FE-only imputation has corner RMSE about 1.96 against a corner scale (SD) of about 6.3; nuclear-norm shrinkage at several values of $\lambda$ gets RMSE 1.85-1.93, barely better than ignoring the factor structure entirely; a rank-2 gsynth/IFE fit recovers the corner to machine precision (RMSE 0). This is structural, not a tuning failure: shrinkage is a conservative extrapolation policy, and the corner is precisely where it is most conservative.

Demo B (the placebo-imputation tournament). Athey et al.'s own validation recipe, applied here to a 40-city, no-treatment version of the same factor panel (noise floor 0.5). Hide cells you actually observe under four patterns, impute with each method, score RMSE against ground truth you happen to know.

Two robust conclusions. First, FE-only imputation (exactly the Borusyak-Jaravel-Spiess counterfactual of Module 2) is dominated by every factor-aware method on every pattern: parallel-trends imputation pays for ignoring the factor structure everywhere, not just under selection. Second, fixed-rank IFE wins whenever it can run (it exploits the exact rank), but gsynth requires an absorbing treatment pattern (once missing, always missing within a unit), so it cannot even attempt the random-holes case. Matrix completion is the only method in the table that runs on every pattern, and on the one pattern that rules out everything else, it clearly beats FE-only imputation.

Shrinkage is an extrapolation policy you choose

The two demos together are the module's central lesson. Regularization choice is not a technical footnote, it is a bet about how far you are willing to extrapolate:

• Fixed-rank factor estimation (gsynth/IFE) extrapolates aggressively once it commits to a rank: no shrinkage inside that rank, so a well-specified low-rank structure is recovered almost exactly, even deep into a treated corner far from any observed cell.
• Nuclear-norm shrinkage (MC-NNM) extrapolates conservatively: it never fully trusts a factor structure it cannot validate on observed data, so it degrades gracefully when the rank is unknown, the pattern is irregular, or the panel is thin, at the cost of under-correcting a confound that a correctly-specified fixed-rank model would catch.

Neither dominates. The practical rule: a strongly trending confound plus a long extrapolation horizon, with enough pre-periods per treated unit, favors gsynth/IFE. An irregular missingness pattern, a panel with real data gaps, or genuine uncertainty about the rank favors matrix completion. Either way, validate with Demo B's recipe on your own panel before trusting the answer: hide cells you actually observe, impute, and see which method's errors you can live with.

Staggered adoption across the toolbox

How the block-treatment tools of Modules 4-5 extend, or fail to, under staggered timing:

The imputation view unifies the entire course. Borusyak-Jaravel-Spiess imputation (Module 2) is exactly the FE-only imputer in the tournament above, MC-NNM with $L$ constrained to zero: no low-rank term, pure additive fixed effects. gsynth is MC-NNM with a hard, CV-selected rank in place of continuous nuclear-norm shrinkage. Every difference-in-differences estimator in this course sits on the same regularization dial, from "no low-rank term at all" (BJS) through "hard-cutoff rank" (gsynth) to "continuous shrinkage" (MC-NNM).

When to reach for matrix completion

• Irregular adoption or genuinely missing panel cells. gsynth, SC, and SDID all require a structured, absorbing pattern. MC-NNM is the only estimator here that runs on arbitrary missingness, and Demo B shows it wins there.
• You are not confident in the rank. Continuous shrinkage degrades gracefully if the true factor count is misjudged; a hard-rank model can be badly mis-specified with the wrong $r$.
• Many treated units, a thin control pool. This is the paper's own motivating case (a hard-rank factor model is harder to estimate with few controls), but treat it as a reason to test, not a guarantee: in a single check on the tournament DGP with 35 of 40 units treated, fixed-rank IFE still beat soft-impute (RMSE 0.72 vs 1.15). Run Demo B's recipe on your own panel rather than assuming.

Caveat. A strongly trending confound plus a long extrapolation horizon, with enough pre-periods per treated unit, favors gsynth/IFE (Demo A). Nuclear-norm shrinkage is the safer default when the pattern rules out fixed-rank methods entirely, or when you are unsure the rank is right. Always validate with the placebo-imputation exercise before trusting either estimator on a new panel.

Long-run outcomes from short panels: the surrogate index

A different problem entirely, but one that shares the "the data you have is not the data you need" theme: the experimental panel runs 8 weeks, but the decision depends on 12-month retention. Waiting a year to evaluate every launch is not viable.

Athey, Chetty, Imbens and Kang (2019) combine two data sources:

1. The experiment itself, which records treatment and short-run surrogates $S$ (trips, active days, cancellation rate) but not the long-run outcome $Y_{\text{long}}$.
2. Historical data, from units observed for the full horizon, linking those same surrogates to $Y_{\text{long}}$.

Fit the surrogate index $\hat h(S, X) = \hat E[Y_{\text{long}} \mid S, X]$ on the historical sample, then use $\hat h(S_i, X_i)$ as the outcome inside the experiment. The resulting treatment-effect estimate targets the long-run effect without ever observing the long-run panel for the experimental units.

Assumptions. Surrogacy: treatment affects the long-run outcome only through the observed surrogates, $Y_i(\text{long}) \perp W_i \mid S_i, X_i$. Comparability: the surrogate-to-long-run relationship estimated historically also holds in the experimental sample. Overlap: the historical sample covers the surrogate values the experiment actually produces. A useful bonus when the assumptions hold: the index also reduces noise, since it averages away idiosyncratic long-run variation the surrogates do not explain, so the experiment's effective sample size for the long-run question is larger than running the full panel would give directly.

Failure modes. A treatment channel that bypasses the surrogates entirely, for example a fee change that leaves short-run usage flat but slowly erodes trust and long-run retention, breaks surrogacy silently: the index would report no effect while the true long-run effect is nonzero. Distribution shift between the historical and experimental samples (a changed product, a changed market) breaks comparability. Neither failure is directly testable from the experiment alone; both need domain judgment about the mechanism connecting treatment to the long-run outcome.

Choosing the method: the course's capstone

• Can you randomize? Then randomize. Everything below answers "what do you do when the experiment you wanted is not available": a platform-wide launch, one treated market, a legal or PR constraint, or a retroactive question.
• Staggered rollout with clean never- or late-treated controls → Callaway-Sant'Anna or BJS imputation (Module 2), audited with a Goodman-Bacon decomposition (Module 1) and stress-tested with HonestDiD sensitivity (Module 3).
• One treated market with a good donor pool → synthetic control, augmented SC, or synthetic DiD (Modules 4-5), with placebo or conformal inference.
• Irregular adoption, holes in the panel, or many treated units → matrix completion or gsynth (this module), validated by hiding observed cells before trusting either.
• Need to know who benefits → causal forest (Module 6), with calibration, best-linear-projection, and RATE diagnostics before any subgroup claim.
• Need to decide who gets the treatment → policy tree with cross-fitted off-policy evaluation (Module 7).
• Long-run outcome, short panel → the surrogate index, layered on top of whichever design above supplies the experiment or quasi-experiment.

Practitioner guidance

• Start from the pattern, not the method. Draw the missingness pattern first (one block, many blocks, staggered, irregular); it rules out most of the toolbox before you touch an estimator.
• Cross-validate $\lambda$ (or $r$, for gsynth) only against cells you actually observe, never against treated cells, and report sensitivity to the tuning choice rather than a single point.
• Validate any panel estimator, before trusting its ATT, by hiding cells you already know and scoring the imputation. This is cheap, requires no new data, and directly answers whether the estimator's extrapolation policy fits your setting.
• Treat "irregular pattern" and "thin control pool" as two different reasons to consider matrix completion, and check the second empirically: it does not always favor MC over a fixed-rank alternative.
• For long-horizon outcomes, reach for the surrogate index only when you can defend surrogacy and comparability qualitatively; neither is testable from the experiment alone.

The same problem at an online retailer

The metro-week orders panel with a staggered block of treated cells is the natural matrix-completion setting from the delivery rollout. The treated cells, metro-upgrade-week combinations where the metro has already received next-day delivery, have missing untreated potential outcomes; matrix completion imputes those missing entries using the panel's low-rank structure without requiring a clean donor pool or homogeneous trends across metros. The nuclear-norm penalty shrinks the completed matrix toward a low-rank factorization, treating each metro's order trajectory as a noisy draw from a small number of latent demand factors shared across the metro network. This relaxes both the convex-hull requirement of synthetic control and the parallel-trends requirement of DiD, making it attractive when neither assumption is defensible.

In the capstone decision tree, the two running examples point to different branches of the method-choice diagram. Many staggered treated metros points to Callaway-Sant'Anna or BJS imputation; a single treated metro points to synthetic control or SDID; questions about which customers benefit from the signup discount point to causal forest and then to policy learning. Matrix completion covers the staggered-panel branch when the panel is large and the low-rank structure is plausible. Both examples have now appeared across every module of this course, illustrating that the choice of method depends on the data structure and identification strategy, not on which application is more familiar.

References

• Athey, S., Bayati, M., Doudchenko, N., Imbens, G. and Khosravi, K. (2021). Matrix completion methods for causal panel data models. Journal of the American Statistical Association, 116(536), 1716-1730.
• Athey, S., Chetty, R., Imbens, G. W. and Kang, H. (2019). The surrogate index: combining short-term proxies to estimate long-term treatment effects more rapidly and precisely. NBER Working Paper 26463.
• Xu, Y. (2017). Generalized synthetic control method: causal inference with interactive fixed effects models. Political Analysis, 25(1), 57-76.
• Arkhangelsky, D., Athey, S., Hirshberg, D. A., Imbens, G. W. and Wager, S. (2021). Synthetic difference-in-differences. American Economic Review, 111(12), 4088-4118.
• Borusyak, K., Jaravel, X. and Spiess, J. (2024). Revisiting event-study designs: robust and efficient estimation. Review of Economic Studies.
• Mazumder, R., Hastie, T. and Tibshirani, R. (2010). Spectral regularization algorithms for learning large incomplete matrices. Journal of Machine Learning Research, 11, 2287-2322.
• Rambachan, A. and Roth, J. (2023). A more credible approach to parallel trends. Review of Economic Studies, 90(5), 2555-2591.
• Liu, L., Wang, Y. and Xu, Y. (2024). A practical guide to counterfactual estimators for causal inference with time-series cross-sectional data. American Journal of Political Science, 68(1), 160-176.