# Predictor Selection for Synthetic Controls

Jaume Vives-i-Bastida Department of Economics, Massachusetts Institute of
Technology. Email<EMAIL_ADDRESS>I thank Alberto Abadie, Amy Finkelstein,
Anna Mikusheva, Stephen Morris, Brian Quistorff, Jason Thorpe and the
participants in the MIT Economics second year research seminar, the MIT
econometrics lunch, the Google statistics seminar, and the Meta economics
seminar for valuable comments and suggestions. An earlier version of the paper
was circulated under the title Sparse Synthetic Controls.

###### Abstract

Synthetic control methods often rely on matching pre-treatment characteristics
(called predictors) of the treated unit. The choice of predictors and how they
are weighted plays a key role in the performance and interpretability of
synthetic control estimators. This paper proposes the use of a sparse
synthetic control procedure that penalizes the number of predictors used in
generating the counterfactual to select the most important predictors. We
derive, in a linear factor model framework, a new model selection consistency
result and show that the penalized procedure has a faster mean squared error
convergence rate. Through a simulation study, we then show that the sparse
synthetic control achieves lower bias and has better post-treatment
performance than the un-penalized synthetic control. Finally, we apply the
method to revisit the study of the passage of Proposition 99 in California in
an augmented setting with a large number of predictors available.

keywords: synthetic controls, lasso, variable selection, linear factor models,
high-dimensional observational studies.

##  1 Introduction

Synthetic controls have become a popular method for making inferences on
causal effects of policy interventions. Its applications have ranged from
evaluating the effects of tax changes ([1], [17]) to more complex policy
changes such as guaranteed job programs ([16]). Beyond the social sciences
synthetic controls have also been used in other applied sciences, for example
in engineering and the health sciences, and in the private sector, for
instance to evaluate the effect of advertising promotions in large tech
companies.

In the classical synthetic control setting ([3]) a single aggregate unit (such
as a city or a state) is exposed to a policy treatment at period $T_{0}$, and
$J$ units that are never exposed to the policy (called the donor units) are
used to generate a counterfactual. The researcher builds the synthetic control
by finding the combination of donor units that best matches the pre-treatment
characteristics (called the predictors) of the treated unit. Predictors may
include both pre-treament outcomes as well as other covariates that are
informative of the outcome of interest. An open question in the literature
regards best practices and theory on how to choose the set of predictors and
how to weight the importance of each predictor in building the synthetic
control.

There are two main reasons why the choice of predictor weights matters for
computing synthetic controls. First, as noted by [2], [4], [18] and [19] among
others, the predictor weights are important for the performance of the
synthetic controls. Weighting the predictors naively can lead to bad pre-
intervention fit and synthetic controls with poor post-intervention
performance. This, in turn, means that the estimated treatment effects will be
biased. Second, the predictor weights may be of interest in their own right.
The researcher may be interested in interpreting them to explain how the
synthetic control was built. For example, in the California tobacco control
program application that we will re-visit in Section 5, the researcher may be
interested in explaining what predictors (alcohol consumption, income etc) are
used in generating the counterfactual. Hence, the choice of predictors is
important both for the performance and the interpretability of the synthetic
control.

Most of the literature relies on treating the predictor weights as a hyper-
parameter and choosing them through a cross-validation procedure. Different
implementations and best practices for choosing the weights have been
proposed, see for example [1], [2], [11], and [8]. A common thread throughout,
however, is that researchers should have a good prior on what predictors to
include to construct the synthetic control. Recently, [21] note that cross-
validation may not be amenable to many synthetic control settings and
insightfully propose an information criteria for model selection of the donor
weights based on estimating the degrees of freedom of the synthetic control
problem. Under a gaussianity assumption they show that using the information
criteria leads to the right selection of the combination of donor units.

In this paper our focus is slightly different. We are interested in the
selection of the predictors themselves as well as how they relate to the
performance of the synthetic control. Taking [2] as a starting point, we show
theoretically and empirically that a modified penalized procedure that
includes an $l_{1}$ penalty for the predictor weights can achieve consistent
predictor selection as well as better mean squared error performance than the
standard method. Our theoretical results for a linear factor model ensure
that, almost surely, predictors that do not contribute to the outcome of
interest in the model will not be used in the match to compute the synthetic
control. Under stronger assumptions, the result also holds the other way
around; predictors that are useful in generating the outcome of interest are
used with positive probability. In the same setting we also derive a synthetic
control bias bound akin to the one in [1] and [13], and show that the bias
depends on whether the useful predictors can be matched well. Finally, we show
that the proposed penalized procedure has a faster mean square error rate of
convergence for matching the predictors, suggesting it may have lower bias
than the standard method.

We refer to our proposed procedure as the sparse synthetic control as it is
related to the class of penalized synthetic control models proposed by [22].
The focus of [22], however, is on showing consistency and inference for
penalized synthetic control estimators of the average treatment effect on the
treated using the theoretical framework of [12] and [9]. Our model consistency
results also apply to the estimators proposed by [22], therefore we see our
theoretical results and proposed methodology as complementary to [22] in the
analysis of the properties of penalized synthetic control methods.

To evaluate the usefulness of the theoretical results in practice we compare
in a simulation study the standard (un-penalized) synthetic control and our
proposed method and revisit the passage of Proposition 99 in California using
an extended data set with forty predictors. The simulation evidence confirms
that the penalized method is able to identify the useful from the nuissance
predictors and achieves better mean squared error in the post-treatment
period. The empirical application highlights that when the number of
predictors is large the standard un-penalized synthetic control may struggle
to provide a valid synthetic control. On the other hand, our procedure is
robust to increasing the number of predictors from the original seven used in
[1] to a higher dimensional setting with forty predictors. Furthermore, the
sparse synthetic control uses predominantly predictors included in the
original application, confirming the predictor choice of [1]. Finally, an
estimate of the placebo variance in the application suggests that the proposed
method has lower variance than the standard method, as predicted by the
theory.

The paper is structured as follows. Section 2 describes the proposed penalized
synthetic control method and a computation algorithm. Section 3 presents the
main theoretical results in a linear factor model. Section 4 explains the
simulation study results, and finally Section 5 discusses the empirical
application to the California tobacco control program.

##  2 Sparse Synthetic Controls

To define the sparse synthetic control method, consider a setting in which we
observe $J+1$ aggregate units for $T$ periods. The outcome of interest is
denoted by $Y_{it}$ and only unit 1 is exposed to the intervention during
periods $T_{0}+1,\dots,T$. We are interested in estimating the treatment
effect $\tau_{1t}=Y_{1t}^{I}-Y_{1t}^{N}$ for $t>T_{0}$, where $Y_{1t}^{I}$ and
$Y_{1t}^{N}$ denote the outcomes under the intervention and in absence of the
intervention respectively. Since we do not observe $Y_{1t}^{N}$ for $t>T_{0}$
we estimate $\tau_{1t}$ by building a counterfactual $\hat{Y}_{1t}^{N}$ of the
treated unit’s outcome in absence of the intervention.

As in the standard synthetic control our counterfactual outcome will be given
by a weighted average of the donor units’ outcomes, that is
$\hat{Y}_{1t}^{N}=\sum_{j=2}^{J+1}w_{j}Y_{jt}$ for a set of weights
$\mathbf{w}=(w_{2},\dots,w_{J+1})^{\prime}$. To choose the weight vector
$\mathbf{w}$ we use observed characteristics of the units and pre-intervention
measures of the outcome of interest. Formally, we let the $K\times 1$ design
matrix for the treated unit be
$\mathbf{X}_{1}=(Z_{1},\bar{Y}_{1}^{\mathbf{K}_{1}},\dots,\bar{Y}_{1}^{\mathbf{K}_{M}})^{\prime}$,
where $\\{\bar{Y}_{1}^{\mathbf{K}_{i}}\\}_{1}^{M}$ represent $M$ linear
combination of the outcome of interest for the pre-intervention period and
$Z_{1}$ are pre-treament characteristics of the treated unit. Similarly, for
the donor units, $\mathbf{X}_{0}$ is a $K\times J$ matrix constructed such
that its $j$th column is given by
$(Z_{j},\bar{Y}_{j}^{\mathbf{K}_{1}},\dots,\bar{Y}_{j}^{\mathbf{K}_{M}})^{\prime}$.
We call the $K$ rows of the design matrices $\mathbf{X}_{0}$ and
$\mathbf{X}_{1}$ the predictors of the outcome of interest. This can include,
for example, lags of the outcome variable and important context dependent
characteristics of the aggregate units averaged over the pre-treatment period.

We partition the pre-intervention period into a training set
$(\mathbf{X}_{0}^{train},\mathbf{X}_{1}^{train},\mathbf{Y}_{0}^{train},\mathbf{Y}_{1}^{train})$
for $t\in\\{1,\dots,T_{v}\\}$ and a validation set
$(\mathbf{X}_{0}^{val},\mathbf{X}_{1}^{val},\mathbf{Y}_{0}^{val},\mathbf{Y}_{1}^{val})$
for $t\in\\{T_{v}+1,\dots,T_{0}$}. This allows for the training and validation
design matrices to differ, for example if predictors are averaged over
different time periods or different linear combinations of lagged outcome
variables are used.

The sparse synthetic control is defined by the tuple of weight vectors
$(\mathbf{V}^{*},\mathbf{w}^{*})$ computed by solving the following bi-level
optimization program:111I follow the notation of Malo, Eskelinen, Zhou and
Kuosmanen 2020, who propose a computational method to solve a similar problem.

  * •

Upper level problem:

$\displaystyle(\mathbf{V}^{*},\mathbf{w}^{*})\in\text{argmin}_{\mathbf{V},\mathbf{w}}$
$\displaystyle
L_{V}(\mathbf{V},\mathbf{w},\lambda)=\frac{1}{T_{val}}\|\mathbf{Y}_{1}^{val}-\mathbf{Y}_{0}^{val}\mathbf{w}(\mathbf{V})\|^{2}+\lambda\|\text{diag}(\mathbf{V})\|_{1},$
s.t.
$\displaystyle\mathbf{w}(\mathbf{V})\in\psi(\mathbf{V}),\bm{V}\in\mathbb{R}^{K}_{+}.$

  * •

Lower level problem:

$\psi(\mathbf{V})\equiv\text{argmin}_{\mathbf{w}\in\mathcal{W}}L_{W}(\mathbf{V},\mathbf{w})=\|\mathbf{X}^{train}_{1}-\mathbf{X}^{train}_{0}\mathbf{w}\|^{2}_{V},$

where,

$\displaystyle\mathbf{w}\in\mathcal{W}$
$\displaystyle\equiv\left\\{\mathbf{w}\in\mathbb{R}^{J}\text{ }|\text{
}\mathbf{1}^{\prime}\mathbf{w}=1,\text{ }w_{j}\geq 0,\text{
}j=2,\dots,J+1\right\\},$ $\displaystyle\mathbf{V}\in\mathcal{V}$
$\displaystyle\equiv\left\\{\mathbf{V}\text{ }|\text{
}\mathbf{V}\in\mathbb{R}^{K\times K},\text{ }trace(\mathbf{V})=1,\text{
}V_{kk}\geq 0,V_{kl}=0\text{ for }k\neq l\right\\},\text{ and}$
$\displaystyle\|\cdot\|_{V}$ $\displaystyle\text{ denotes the semi-norm
parameterized by $\mathbf{V}$ such that
}\|\bm{A}\|_{V}=(\mathbf{A}^{\prime}\mathbf{V}\mathbf{A})^{1/2}.$

The main idea of the sparse synthetic control is that the $l_{1}$ penalty in
the upper level problem induces some predictor weights (the diagonal elements
of the weight matrix $\mathbf{V}$) to be set to zero as the penalty term
$\lambda$ increases. A similar bi-level program is also considered in [22], in
which the authors also consider additional penalties for the lower level
problem. In practice, given the weight restriction $\mathbf{V}\in\mathcal{V}$,
we follow [1] in the use of ex-post weight normalization by initially setting
one predictor weight to one (i.e. $v_{k_{0}}=1$ for some
$k_{0}\in\\{1,\dots,K\\}$) and only restricting the $v_{k}$ weights to be
positive in the upper level program. In the appendix we describe why this ex-
post normalization is necessary for finding a unique solution for the $v$
weights. The following algorithm details the procedure used to choose the
hyper-parameter $\lambda$ and compute the sparse synthetic controls.

Result: $\mathbf{w}^{*},\mathbf{V}^{*}$

Data:
$(\mathbf{X}_{0}^{train},\mathbf{X}_{1}^{train},\mathbf{Y}_{0}^{train},\mathbf{Y}_{1}^{train})$,
$(\mathbf{X}_{0}^{train},\mathbf{X}_{1}^{train},\mathbf{Y}_{0}^{val},\mathbf{Y}_{1}^{val})$

1 set $v_{k_{0}}$= 1;

2 initialize $v_{k}$ for $k\neq k_{0}$ to
$(\mathbf{X}_{0}^{train^{\prime}}\mathbf{X}_{0}^{train})^{-1}$;

3 for  _each $\lambda$ in a grid_ do

4 get $(\mathbf{V}_{\lambda},\mathbf{w}_{\lambda})$ by jointly minimizing
$L_{W}(\mathbf{V},\mathbf{w},\lambda)$ and $L_{V}(\mathbf{V},\mathbf{w})$ for
the training data;

5 s.t. $\mathbf{w}\in\mathcal{W}$, $v_{k}\geq 0$ $\forall k\neq k_{0}$ and
$v_{k_{0}}=1$;

6 scale $\mathbf{V_{\lambda}}$ to $[0,1]$;

7 get $\mathbf{w}^{*}_{\lambda}$ by minimizing
$L_{W}(\mathbf{V_{\lambda}},\mathbf{w},\lambda)$ for the training data;

8 store
$\text{MSE}(\mathbf{Y}_{1}^{val},\mathbf{Y}_{0}^{val}\mathbf{w}_{\lambda}^{*})$
and $\mathbf{V}_{\lambda}$;

9

10 end for

11choose $\lambda^{*}$ with minimum
$\text{MSE}(\mathbf{Y}_{1}^{val},\mathbf{Y}_{0}^{val}\mathbf{w}_{\lambda}^{*})$;

12 $\mathbf{V}^{*}=\mathbf{V}_{\lambda^{*}}$;

get $\mathbf{w}^{*}$ by minimizing
$L_{V}(\mathbf{V^{*}_{\lambda}},\mathbf{w})$ for the shifted training
data.222The shifted training data is the training data but with time dependent
variables shifted to the $T_{v}$ periods before $T_{0}$.

Algorithm 1 Sparse Synthetic Control

##  3 Theoretical Results for a Linear Factor Model

To motivate the model selection procedure for thesparse synthetic controls
theoretically, consider a standard setting in which the outcomes in absence of
the intervention are given by a linear factor model as in [1]

$Y_{it}^{N}=\delta_{t}+\bm{\theta}_{t}\mathbf{Z}_{i}+\bm{\lambda}_{t}\bm{\mu}_{i}+\epsilon_{it},$

where $\delta_{t}$ is a common factor with equal loadings, $Z_{i}$ is a
($k\times 1)$ vector of observed features, $\theta_{t}$ is a $(1\times k)$
vector of unknown parameters, $\lambda_{t}$ is a $(1\times F)$ vector of
unobserved common factors, $\mu_{i}$ is an $(F\times 1)$ vector of unknown
factor loadings, and $\epsilon_{it}$ is a unit-level transitory shock. Similar
models have been used to motivate synthetic control and diff-in-diff
estimators (see [6], [13] or [4]), as well as two-way fixed effect estimators
and interactive fixed effect estimators ([7], [14]). Assumption 1 imposes
restrictions on the model primitives common in the literature.

######  Assumption 1 (Model primitives)

Assumptions on the covariates, the factor structure and the error components.

  * •

The covariates are fixed and bounded such that
$\max_{j}\|\bm{Z}_{j}\|\leq\sqrt{k}$.

  * •

The common factor $\lambda_{t}$ are covariance stationary.

  * •

$\epsilon_{it}$ are mean independent of $\\{\bm{Z},\bm{\mu}\\}$.

To study under which conditions the sparse synthetic control algorithm selects
the most important predictors, I assume a sparse representation of the
predictors.

######  Assumption 2 (Sparse representation)

For all $t$, $\bm{\theta}_{t}$ is partitioned conformably into
$(\tilde{\bm{\theta}}_{t},\mathbf{0})^{\prime}$ where
$\tilde{\bm{\theta}}_{t}$ is a ($k_{1}\times 1$) vector of non-zero parameters
and $\mathbf{0}$ is a $k_{2}\times 1$ vector such that $k=k_{1}+k_{2}$.

Under Assumption 2 we partition the covariates comformably into a non-zero and
zero group such that $\bm{Z}_{i}=(\bm{Z}_{i}^{1},\bm{Z}_{i}^{2})$. Throughout
the paper I refer to the $\bm{Z}_{i}^{1}$ predictors as the ”useful”
predictors and the $\bm{Z}_{i}^{2}$ predictors as the nuisance predictors.
Intuitively, we say that the sparse synthetic control is interpretable if
given a large set of predictors the algorithm successfully recovers the useful
ones. That is, we would like to require the method to consistently select
which covariates are useful and give them positive weight, while giving zero
weight to the nuisance covariates. Without further assumptions, however, this
requirement is too strong. Indeed, if the nuissance covariates are highly
correlated with the useful covariates then there is little hope to achieve
model consistency. Assumption 3 gives a strong condition to avoid this
problem.

######  Assumption 3 (Oracle covariate match)

For fixed $J$, let the oracle weights be defined by

$\bm{w}^{*}\in\text{argmin}_{w\in\Delta^{J}}\mathbb{E}\|\bm{Y}_{1}-\bm{Y}_{0}\bm{w}\|^{2}.$

We consider two assumptions:

  1. 1.

For all $k\in S=\\{k\mid\theta_{tk}=0\text{ for all }t\\}$,
$|Z_{1k}-Z_{Jk}^{\prime}\bm{w}^{*}|>0$.

  2. 2.

(1) holds true and for $l\in S^{c}$, $|Z_{1l}-Z_{Jl}^{\prime}\bm{w}^{*}|=0$.

Assumption 3 is different to the irrepresentability condition and the
restricted eigenvalue condition common in compressed sensing and model
selection consistency for penalized estimators (see [24] and [10] for
applications to lasso estimators). It says that the weights that minimize the
statistical risk can not lead to a perfect match for a nuisance covariate.
This assumption rules out data generating processes for which matching
nuisance covariates improves the overall fit. For example, this could happen
if the nuisance covariates are correlated with the factor loadings and contain
useful information for matching them. Without this assumption, there could be
cases in which a nuisance covariate is actually useful in improving the
outcome fit and also can be matched at no cost to the lower level program,
making it desirable for our algorithm to use it with positive probability.

The main result, Theorem 1, states that the sparse synthetic control algorithm
is model consistent when the number of pre-treatment periods grows and $J$,
$k$ and $F$ are fixed.

######  Theorem 1 (Model Selection)

Under A1-A3.1 if $\psi$ is an injective function and $\hat{\lambda}\to 0$ as
$T_{0}\to\infty$, for a fixed $k$ and $J$, as $T_{0}\to\infty$ the following
holds333Here, $\hat{\lambda}$ is the cross-validated hyper-parameter of the
penalty function denoted by $\lambda^{*}$ in Algorithm 1.

  1. 1.

If $k\in S=\\{k\mid\theta_{tk}=0\text{ for all }t\\}$, then $P(v_{k}=0)\to 1$.

  2. 2.

If A3.2 holds and $l\in S^{c}$ then $P(v_{l}=0)\to 0$.

where $v_{k}$ is the predictor weight for predictor $m$ assigned by the sparse
synthetic control algorithm.

In words Theorem 1 states that the sparse synthetic control algorithm will not
use the nuisance predictors with probability going to one as the number of
pre-treatment periods increases. The two main assumptions to derive the result
are the oracle selection assumption and the assumption that the bi-level
program has a unique optimum such that $\psi$ is injective. This will be the
case when the data points are in general position, that is, when every subset
of the columns of $\bm{X}$ are linearly independent. These two assumptions are
hard to test in practice.

It is important to note that the implication does not go the other way in
general. The method could set a useful predictor weight to zero, but it will
not assign a nuisance predictor a non-negative weight with high probability.
Only if the useful predictors can be matched perfectly in the population, then
the method is sign consistent. This result is important because it justifies
the use of sparse synthetic controls to identify important predictors. A
researcher that is unsure about what predictors to use to generate the
synthetic control can use the sparse synthetic control with many predictors
and be confident that it will use the ”useful” predictors if the oracle
separation assumption is satisfied. This suggests using the method as an
alternative to manual predictor search by researchers and possibly as a way to
prevent specification search.

Next, we show that the sparse synthetic control also has desirable performance
properties when compared to the standard (un-penalized) method. In particular,
it has a faster convergence rate the for bias and mean-squared-error of the
treatment effect estimator. To show this, recall that the treatment effect of
interest is $\tau_{1t}=Y_{1t}^{I}-Y_{1t}^{N}$ for $t>T_{0}$. To estimate it we
generate a counterfactual $\hat{Y}^{N}_{1t}=\sum_{j=2}^{J+1}w_{j}Y_{jt}^{N}$
for a synthetic control $\mathbf{w}=(w_{2},\dots,w_{J+1})^{\prime}$.
Therefore, the estimated treatment effect indexed by a synthetic control
$\bm{w}$ is given by

$\hat{\tau}^{\bm{w}}_{1t}=\bm{\theta}_{t}^{\prime}\left(\bm{Z}_{1}-\sum_{j=2}^{J+1}w_{j}\bm{Z}_{j}\right)+\bm{\lambda}_{t}^{\prime}\left(\bm{\mu}_{1}-\sum_{j=2}^{J+1}w_{j}\bm{\mu}_{j}\right)+\sum_{j=2}^{J+1}w_{j}(\epsilon_{1t}-\epsilon_{jt}).$

It is well known that when the synthetic control does not have perfect pre-
treatment fit it is biased. The following lemma gives an upper bound on the
bias that depends on two terms that do not vanish asymptotically.

######  Lemma 1 (Bias Bound)

Under A1-A2 and assuming that there exists a $\bar{\lambda}$ such that
$|\lambda_{ft}|\leq\bar{\lambda}$ for all $t$ and $f$, and that the smallest
eigenvalue of $\sum_{t=1}^{T_{0}}\bm{\lambda}_{t}^{\prime}\bm{\lambda}_{t}$ is
bounded below by $\underline{\xi}$. Then, for a synthetic control $\bm{w}$,

$\mathbb{E}|\hat{\tau}^{\bm{w}}_{1t}|\leq\frac{\gamma}{T_{0}}\sum_{m=1}^{T_{0}}\mathbb{E}|Y_{1m}-\sum_{j=2}^{J+1}w_{j}Y_{jm}|+\left|\bar{\theta}\left(1-\frac{\gamma}{T_{0}}\right)\right|\sum_{k=1}^{k_{1}}\mathbb{E}|Z^{1}_{1k}-\sum_{j=2}^{J+1}w_{j}Z^{1}_{jk}|+\text{O}\left(T_{0}^{-1}\right).$

where $\gamma=\left(\frac{\bar{\lambda}^{2}F}{\underline{\xi}}\right)$,
$\bar{\theta}$ is the maximum value of $\tilde{\bm{\theta}}_{t}$, $F$ is the
number of unobserved common factors and $k_{1}$ is the number of ”useful”
predictors.

The bias bound in Lemma 1 provides three insights. First, if we don’t have
perfect pre-treatment fit the bias does not vanish asymptotically as $T_{0}$
increases. This means that our treatment effect estimate will be biased even
if we have many pre-treatment periods. Second, the bias depends on the mean
absolute deviation of the pre-treatment outcomes. Pre-treatment fit is,
therefore, very important for controlling the bias. This leads to the
suggestion of not using synthetic controls when the pre-treatment fit is bad.
Third, and most relevant for the sparse synthetic controls, the bias depends
on the fit of the ”useful” predictors $\bm{Z}_{i}^{1}$ and linearly in
$k_{1}$. Therefore, even if we have a large number of pre-treatment periods
and the pre-treatment fit is good (the first term in the bound is small), the
bias could be large if the predictor fit is bad. Hence, a synthetic control
that minimizes bias should attempt to perfectly match the useful predictors
and disregard the nuisance predictors. This Lemma reinforces the result in
[13] that synthetic controls with imperfect pre-treatment fit may in general
be biased.

To formalize the improvement in terms of bias and mean-square-error of the
sparse synthetic control over the standard synthetic control, we derive a
finite sample rate for $\text{MSE}(\bm{Z}_{0}\bm{w})$ in the case in which the

######  Theorem 2 (MSE Rate)

Let $\bm{Z}_{1}=\bm{Z}_{0}w^{*}+\bm{u}$ for
$u_{i}\sim_{ind}\text{subG}(\sigma_{z}^{2})$. Then, under $A1-A3.1$ as
$T_{0}\to\infty$, almost surely for the sparse synthetic control
$\hat{\bm{w}}$,

$MSE(\bm{Z}_{1},\bm{Z}_{0}\hat{\bm{w}})=\frac{1}{k}\|\bm{Z}_{1}-\bm{Z}_{0}\hat{\bm{w}}\|^{2}\lesssim\frac{\sigma_{z}\sqrt{k_{1}}}{k}\sqrt{2\log
J}.$

For the standard synthetic control $\tilde{\bm{w}}$,

$MSE(\bm{Z}_{1},\bm{Z}_{0}\tilde{\bm{w}})=\frac{1}{k}\|\bm{Z}_{1}-\bm{Z}_{0}\tilde{\bm{w}}\|^{2}\lesssim\sigma_{z}\sqrt{\frac{2\log
J}{k}}.$

Theorem 2 describes how the mean squared error of the predictor match changes
with the number of predictors and donor units. The main difference between the
sparse synthetic control and the standard method is that the rate is of order
$O(\sqrt{k_{1}}/k)$ instead of $O(1/\sqrt{k})$. This means that in a sparse
setting, when $k_{1}$ is small with respect to $k$, the sparse synthetic
control has a faster MSE rate. In practice, this is important because it
implies that the sparse synthetic control will achieve lower MSE than the
standard synthetic controls when both methods use the same number of
predictors. More so, given Lemma 1, a faster predictor MSE rate also implies
that the sparse synthetic control will achieve lower bias than the standard
method. Formally, recall that by Cauchy-Schwartz inequality the MAD is bounded
above by $\sqrt{J}MSE$, so the proposed method achieves a lower MAD, and so
bias, than the standard method. In section 4 we explore these properties
further by estimating the expected mean absolute deviations empirically and
show in a simulation study that the sparse synthetic control achieves both
better outcome pre-treatment fit and better ”useful” predictor fit than the
standard synthetic control.

##  4 Simulation Study

In this section we study the performance of the sparse synthetic control in
relation to two benchmark models: the standard synthetic control with $\bm{V}$
chosen as $(\mathbf{X}_{0}^{train^{\prime}}\mathbf{X}_{0}^{train})^{-1}$,
which we label SCM, and the synthetic control with $\bm{V}$ chosen to minimize
$\frac{1}{T_{val}}\|\mathbf{Y}_{1}^{val}-\mathbf{Y}_{0}^{val}\mathbf{w}(\mathbf{V})\|^{2}$
as proposed by [2], which we label SCM $\lambda=0$ as it can be understood as
the unpenalized version of the sparse synthetic control.

The findings below rely on the following simulation design, similar to the one
used in [4], for $B=1000$ draws:444We also set $\delta_{t}=100$, but without
loss of generality $\delta_{t}$ could be set to zero.

$\displaystyle T$ $\displaystyle=30,\text{ }T_{0}=20,\text{ }T_{v}=10,$
$\displaystyle\bm{Z}_{i}$ $\displaystyle=[\bm{Z}^{1}_{i},\text{
}\bm{Z}^{2}_{i}],\text{ where }\bm{Z}^{1}_{i},\bm{Z}^{2}_{i}\sim_{iid}U[0,1],$
$\displaystyle\bm{Z}^{1}_{1}$
$\displaystyle=\frac{1}{2}\bm{Z}^{1}_{2}+\frac{1}{2}\bm{Z}^{1}_{3},$
$\displaystyle\lambda_{t}$ $\displaystyle\text{ follows an }AR(1)\text{ with
coefficient }\rho=0.5,$ $\displaystyle\epsilon_{it}$ $\displaystyle\sim
N(0,\sigma^{2})\text{ with }\sigma=0.25,$ $\displaystyle F$
$\displaystyle=7\text{ in groups of 3 units and }J+1=21.$

This simulation design implies that unit 1 (the treated unit) can be perfectly
replicated (up to noise) by an average of units 2 and 3. Hence, the optimal
synthetic control would choose $w_{2}=w_{3}=\frac{1}{2}$. We study two
different predictor settings. The first is one in which there are a similar
amount of useful and useless predictors ($k_{1}=k_{2}=5$); the second,
includes only one ”useful” predictor ($k_{1}=1$ and $k_{2}=9$). In both cases
we add 10 lags of the outcome variable to the design matrix, for a total of 20
predictors. Note that this is a challenging design for the method as both
useful and useless predictors are drawn from the same distribution. We
summarize the simulation results in two Figures that show the performance of
the different methods and explore the theoretical insights from Section 3.

First, focus on the post-treatment mean squared error (MSE) of the outcome
variable. Given that the MSE is an informative measure of fit that includes
both bias and variance it gives us an idea of the performance of the
estimator. In particular, lower post-treatment MSEs will imply lower standard
errors for the treatment effect of interest. Figure 1 shows the distribution
of MSEs for the simulations for the two settings. Panels (a) and (b) show that
the sparse synthetic control has on average lower MSE and less dispersion than
the two benchmark methods. Panels (c) and (d) show the distribution of the
gaps between the predicted outcome and the real outcome for all periods. The
sparse synthetic control has tighter confidence intervals both before and
after treatment and sets unit weights closer to the optimal control (83% of
the weight is given to units 2 and 3). Furthermore, observe that whereas the
benchmarks methods perform worse in the $k_{1}=1,k_{2}=9$ setting, the sparse
synthetic control is able to perform similarly in both settings. This shows
the ability of the method to perform well regardless of the number of useful
and nuissance predictors.

(a) $k_{1}=k_{2}=5.$

(b) $k_{1}=1$, $k_{2}=9.$

(c) $k_{1}=k_{2}=5.$

(d) $k_{1}=1$, $k_{2}=9.$

Figure 1: Mean Squared Errors.

  * •

Notes: Panels (a) and (b) show the kernel density across simulations of the
MSEs for the outcome variable in the post-treatment period, with average
values in parenthesis. Panels (c) and (d) show the inter-quartile range of the
$Y_{1t}-\hat{Y}_{1t}$ with $w^{*}_{2}+w^{*}_{3}$ in parenthesis. SCM lmb=0
refers to the unpenalized synthetic control with $\lambda=0$.

Recall that in section 3 the bias bound crucially depends on the MAD of the
pre-treatment outcomes and useful predictors. A figure in the appendix shows
the $\mathbb{E}\text{MAD}$s for the outcome and useful predictors in the pre-
treatment period. As in Figure 1, the sparse synthetic control is able to
perform well in both settings whereas the benchmark methods perform poorly in
the $k_{1}=1,k_{2}=9$ setting.

(c) $k_{1}=k_{2}=5.$

(d) $k_{1}=1$, $k_{2}=9.$

(e) SCM $\lambda^{*}=0$ $\bm{V}^{*}$

(f) Sparse SCM $\bm{V}^{*}$

Figure 2: Pre-treatment Fit and Variable Selection.

  * •

Notes: Panels (a) - (b) show the share of the $\bm{V}$ and $\bm{w}$ weights
that are zero for the different values of $\lambda^{*}$ across simulations for
the sparse synthetic control. Panels (c) - (d) show the histogram of the
$v_{k}$ weights across simulations for the $k_{1}=k_{2}=5$ setting for the
unpenalized synthetic control with $\lambda=0$ and the sparse synthetic
control respectively.

To investigate the model selection result in Theorem 2 we plot the histogram
of the predictor weight values ($v_{k}$) for the useful and useless predictors
across simulations. Panels (c) and (d) in Figure 2 compare the SCM with
$\lambda^{*}=0$ and sparse synthetic control for the $k_{1}=k_{2}=5$ setting.
Whereas the standard SCM does not clearly distinguish between the useful and
nuissance covariates, the sparse synthetic control correctly assigns zero
weight to the nuissance covariates most of the time. The stark difference
between the two models suggests that the sparse synthetic control may be able
to perform variable selection in practice. Finally, in panels (a) and (b) in
Figure 2 we show that the penalized synthetic control induces sparsity when
the $\lambda$ hyper-parameter increases, but that the donor weights ($w_{j}$)
remain stable. The main takeaway is that the unit weights $\bm{w}^{*}$ have
the same amount of sparsity regardless of the magnitude of the optimal
regularization. This is evidence to motivate the technical assumption that
$\psi$ is injective in Theorem 2, and confirms that the method can reliably
achieve a unique optimum. Note that we do see some instability for large
values of $\lambda^{*}$ in cases in which only one predictor is used.

##  5 Extending the California smoking program case study

In 1988 proposition 99 increased California’s cigarette excise tax by 25 cents
per pack and shifted public policy towards a clean air agenda. This policy
intervention has been used extensively to compare the validity and performance
of various synthetic controls and diff-in-diff estimators. The outcome of
interest is cigarette sales per capita in packs in California and the donor
pool includes 38 states without similar policy interventions. The original
data set used in the [1] study used seven predictors: Ln(GDP per capita),
percent aged 15–24, retail price, beer consumption per capita and three lags
of cigarette sales per capita (1975, 1980 and 1988). In the study the standard
synthetic control built using this design matrix falls outside the convex hull
of the predictors, but has very good pre-treatment fit. This can be seen in
Figure 3 panel (a) for the standard synthetic control with $k=7$.

(a) Standard SC

(b) Sparse SC

Figure 3: Synthetic Controls for California.

To study the potential benefits of using penalized synthetic control methods,
we augment the original predictor data set with 33 additional predictors. The
additional predictors are obtained from the IPPSR (MSU) dataset assembled by
[15] of policy correlates in the United States, they include demographic
variables, income related variables, political participation measures and
government spending statistics. Importantly, they also include less useful
variables such as state identifiers, but do not include predictors that do not
vary across states as these would violate A3.1. Figure 3 compares the standard
synthetic control (SCM with $\lambda^{*}=0$) and the synthetic control
calculated using Algorithm 1 using the $k=7$ predictors considered in [1] and
the extended set of predictors ($k=40$).555To choose the optimal predictor
weights, we divide the pre-treatment period in a training period (14 years)
and a validation period (5 years).

Figure 3 highlights the difficulty of the standard synthetic control matching
problem when the number of predictors is large. While a good synthetic control
exists in the $k=40$ case, namely the same as the synthetic control for $k=7$,
the standard procedure may be unable to find a global optima and fail to
recover the set of predictors for which a good match that concurrently
optimizes pre-treatment fit exists. The synthetic control reported in Figure 3
panel (a) for $k=40$ does not have good pre-treatment fit, and therefore, may
lead to biased estimates of the average treatment effect on the treated. This
example reinforces the notion in practice the choice of predictor set is very
important in constructing valid synthetic controls. If researchers do not want
to manually choose the predictors to match, or may not have a good prior on
which predictors might be useful, the sparse synthetic control method we
propose may be an attractive alternative. As can be seen in panel (b) of
Figure 3 the sparse procedure is able to find a good synthetic control in the
original and extended settings.

The theoretical results and simulation evidence suggest that the sparse
synthetic control procedure should perform better in terms of bias and
prediction mean squared error than the standard method in settings in which
the predictors have a sparse representation. To explore this in the context of
the California case study, Table 1 reports the average treatment effect on
California of the passage of proposition 99 over the 11 post-treatment years
and its placebo variance estimate for the Differences-in-Differences estimator
using the rest of the US as control group, the standard synthetic control (SCM
with $\lambda^{*}=0$), and the sparse synthetic control for the original and
extended predictor settings. The placebo variance is estimated using the
placebo bootstrap method proposed in [6], a detailed explanation of the method
can be found in the appendix.

Table 1: Treatment effect estimates.

| DID | SCM |  Sparse SCM | SCM |  Sparse SCM
---|---|---|---|---|---
$\hat{\tau}$ estimate | -27.4 | -18.9 | -18.5 | -21.0 | -18.2
$\hat{V}^{1/2}_{\tau}$ | (16.7) | (13.2) | ( 12.2 ) | ( 12.9 ) | ( 11.7 )
k | - | 7 | 7 | 40 | 40

  * •

Notes: DID is the standard diff-in-diff estimator, SCM is the standard
synthetic control with $\bm{V}$ chosen to minimize
$\frac{1}{T_{val}}\|\mathbf{Y}_{1}^{val}-\mathbf{Y}_{0}^{val}\mathbf{w}(\mathbf{V})\|^{2}$
without penalization ($\lambda^{*}=0$), SDID is the synthetic diff-in-diff
estimator, and the ${}^{\prime}+^{\prime}$ indicates the augmented data
setting. Standard errors are taken from Arkhangelsky et al. 2020.

To benchmark the findings in Table 1 in the first column we report the
Differences-in-Differences estimate which, given that the parallel trends
assumption is likely violated, is biased downwards as discussed in [1]. The
second column shows the standard synthetic control with the seven predictors
as in [1], which given its excellent pre-treatment fit, is believed to have
low bias. Column 3 shows that, unsurprisingly, the sparse method yields a very
similar treatment effect as the standard method when $k=7$. The difference
between the methods become apparent in the last two columns. While the
standard method becomes biased towards the differences-in-differences estimate
when $k=40$, the penalized method obtains a very similar estimate as in the
$k=7$ case. This robustness to the number of predictors highlights the
benefits of the penalized procedures in choosing which predictors to match on
to optimize the pre-treatment fit while avoiding over-fitting. Furthermore, we
also see an improvement in the placebo variance estimates between the standard
method and the penalized method, with the later having 8%-10% lower variance.

Figure 4: Predictor choice in the $k=40$ California case study.

(a) Top 7 predictors SCM |  Sparse SCM
---|---
smk_80 | smk_75
general_revenue_inc | incshare_top1
smk_75 | smk_88
smk_88 | pc_inc_ann
loginc | region
general_expenditure_inc | budget_surplus
pc_inc_ann | taxes_gsp

(b) Predictor weight distribution

Finally, in Figure 4 we explore the predictor weight choices of each method
when $k=40$. Panel (b) shows that, as expected, the penalized method uses
predominantly a small set of predictors, with a large fraction of predictors
receiving zero or close to zero weight. This comes in stark opposition to the
standard method that uses denser predictor weights, with many predictors
having similar weight and only a few being set to zero. Panel (a) confirms
that the choice of predictors in [1] was very good. Amongst the top seven
predictors with highest weight, both methods use the lagged cigarette sales
variables (smk) and personal income related variables log income and per
capita annual income. Departing from the [1] predictor set both methods also
assign weight to state level revenue and spending variables such as the
general revenue, the budget surplus or the tax revenue as a percentage of the
gross state product and both methods assign close to zero weight to the beer
consumption measure. Additionally, the sparse method also uses a regional
indicator (South-West-Midwest-East) and an inequality measure (the share of
income by the top 1%). Finally, the sparse method assigns zero weight to the
state indicator (a predictor we expected not to be useful in the match), while
the standard method uses the indicator with positive weight. Suggesting that
the model selection result for the sparse method is relevant in applied
settings in identifying nuisance predictors.

The main takeaways from the empirical application are (1) that the standard
SCM may struggle to generate a valid synthetic control, and so may be biased,
when we use a large number of predictors, (2) that the sparse synthetic
control is a potential solution to this problem and is robust to increasing
the number of predictors, and (3) that using the penalized method in
combination with a larger set of predictors may be useful for researchers that
have many predictors at their disposal and are unsure about which ones may be
the useful ones.

##  6 Conclusion

Researchers and policy makers are increasingly drawn towards synthetic control
methods to analyze policy interventions. A key step in using these methods is
deciding what predictors to use in building the synthetic control. Using a
large number of predictors is not a valid alternative as it can lead to biased
treatment effects and poor post-treatment performance. In this paper, we
advocate for a data-driven penalized synthetic control method that
automatically chooses the important predictors. We suggest that this method
can be used as an alternative to the standard synthetic control when the
researcher has many predictors at his disposal but does not know which ones
should be used.

We show that, in a linear factor model setting, that the sparse synthetic
control is model consistent and can successfully recover which predictors are
useless when the number of pre-treatment periods is large. Furthermore, by
deriving an MSE convergence rate result and a bias bound result, we show that
the sparse synthetic control has better theoretical performance properties
than the un-penalized method. Motivated by this insight we then show through a
simulation study that the proposed method is able to reduce both the bias and
the mean-squared error measures with respect to the un-penalized synthetic
control.

Finally, we highlight the practical relevance of the method by applying it to
the passage of Proposition 99 in California in a setting with 8 predictors
versus a setting with 40 predictors. Whereas the standard synthetic control
estimate becomes more biased when the number of predictors is increased, the
sparse synthetic control is robust to the number of predictors used. Through
this exercise, we confirm that the choice of predictors in the original study
of [1] was good, as the penalized method uses the original predictors with
positive probability.

A natural next step for future work is to explore alternative penalized
synthetic control methods with multidimensional shrinkage ([23]), for example
with elastic net penalties, that may further improve the performance of the
method and the standard errors of the treatment effect estimates.

## References

  * [1] Alberto Abadie, Alexis Diamond and Jens Hainmueller  “Synthetic Control Methods for Comparative Case Studies: Estimating the Effect of California’s Tobacco Control Program”  In _Journal of the American Statistical Association_ 105.490 Taylor & Francis, 2010, pp. 493–505  DOI: 10.1198/jasa.2009.ap08746
  * [2] Alberto Abadie, Alexis Diamond and Jens Hainmueller  “Comparative Politics and the Synthetic Control Method”  In _American Journal of Political Science_ 59.2, 2015, pp. 495–510  DOI: https://doi.org/10.1111/ajps.12116
  * [3] Alberto Abadie and Javier Gardeazabal  “The Economic Costs of Conflict: A Case Study of the Basque Country”  In _American Economic Review_ 93.1, 2003, pp. 113–132  DOI: 10.1257/000282803321455188
  * [4] Alberto Abadie and Jaume Vives-i-Bastida  “Synthetic Controls in Action”, 2022  URL: https://ideas.repec.org/p/arx/papers/2203.06279.html
  * [5] Takeshi Amemiya  “Regression Analysis when the Dependent Variable Is Truncated Normal”  In _Econometrica_ 41.6 [Wiley, Econometric Society], 1973, pp. 997–1016  URL: http://www.jstor.org/stable/1914031
  * [6] Dmitry Arkhangelsky et al.  “Synthetic Difference-in-Differences”  In _American Economic Review_ 111.12, 2021, pp. 4088–4118  DOI: 10.1257/aer.20190159
  * [7] Jushan Bai  “Panel Data Models With Interactive Fixed Effects”  In _Econometrica_ 77.4, 2009, pp. 1229–1279  DOI: https://doi.org/10.3982/ECTA6135
  * [8] Eli Ben-Michael, Avi Feller and Jesse Rothstein  “The Augmented Synthetic Control Method”  In _Journal of the American Statistical Association_ 116.536 Taylor & Francis, 2021, pp. 1789–1803  DOI: 10.1080/01621459.2021.1929245
  * [9] Victor Chernozhukov, Kaspar Wüthrich and Yinchu Zhu  “An Exact and Robust Conformal Inference Method for Counterfactual and Synthetic Controls”  In _Journal of the American Statistical Association_ 116.536 Taylor & Francis, 2021, pp. 1849–1864  DOI: 10.1080/01621459.2021.1920957
  * [10] Denis Chetverikov, Zhipeng Liao and Victor Chernozhukov  “On cross-validated Lasso in high dimensions”  arXiv, 2016  DOI: 10.48550/ARXIV.1605.02214
  * [11] Nikolay Doudchenko and Guido W Imbens  “Balancing, Regression, Difference-In-Differences and Synthetic Control Methods: A Synthesis”, Working Paper Series 22791, 2016  DOI: 10.3386/w22791
  * [12] Bruno Ferman  “On the Properties of the Synthetic Control Estimator with Many Periods and Many Controls”  In _Journal of the American Statistical Association_ 116.536 Taylor & Francis, 2021, pp. 1764–1772  DOI: 10.1080/01621459.2021.1965613
  * [13] Bruno Ferman and Cristine Pinto  “Synthetic controls with imperfect pretreatment fit”  In _Quantitative Economics_ 12.4, 2021, pp. 1197–1221  DOI: https://doi.org/10.3982/QE1596
  * [14] Laurent Gobillon and Thierry Magnac  “Regional Policy Evaluation: Interactive Fixed Effects and Synthetic Controls”  In _The Review of Economics and Statistics_ 98.3, 2016, pp. 535–551  DOI: 10.1162/REST˙a˙00537
  * [15] M. Grossmann, M. Jordan and J. McCrain  “The Correlates of State Policy and the Structure of State Panel Data.”  In _State Politics and Policy Quarterly_ , 2021
  * [16] Maximilian Kasy and Lukas Lehner  “Employing the unemployed of Marienthal: Evaluation of a guaranteed job program”  In _AEA RCT Registry_ , 2021  DOI: https://doi.org/10.1257/rct.6706
  * [17] Henrik Jacobsen Kleven, Camille Landais and Emmanuel Saez  “Taxation and International Migration of Superstars: Evidence from the European Football Market”  In _American Economic Review_ 103.5, 2013, pp. 1892–1924  DOI: 10.1257/aer.103.5.1892
  * [18] Stefan Klößner, Ashok Kaul, Gregor Pfeifer and Manuel Schieler  “Comparative politics and the synthetic control method revisited: a note on Abadie et al. (2015)”  In _Swiss Journal of Economics and Statistics_ 154.11, 2018
  * [19] Pekka Malo, Juha Eskelinen, Xun Zhou and Timo Kuosmanen  “Computing Synthetic Controls Using Bilevel Optimization”  MPRA, 2020
  * [20] Whitney K. Newey and Daniel McFadden  “Chapter 36 Large sample estimation and hypothesis testing” 4, Handbook of Econometrics  Elsevier, 1994, pp. 2111–2245  DOI: https://doi.org/10.1016/S1573-4412(05)80005-4
  * [21] Guillaume A. Pouliot and Zhen Xie  “Information Criteria and Degrees of Freedom for the Synthetic Control Method”, 2022  URL: https://www.dropbox.com/s/p516z6khu9576cf/df_sc_draft_version2.pdf?dl=0
  * [22] Brian Quistorff, Matt Goldman and Jason Thorpe  “Sparse Synthetic Controls: Unit-Level Counterfactuals from High-Dimensional Data”  In _Microsoft Journal of Applied Research_ , 2020, pp. 155–170
  * [23] Jaume Vives-i-Bastida  “STRETCHING THE NET: MULTIDIMENSIONAL REGULARIZATION”  In _Econometric Theory_ Cambridge University Press, 2021, pp. 1–30  DOI: 10.1017/S0266466621000347
  * [24] Peng Zhao and Bin Yu  “On Model Selection Consistency of Lasso”  In _Journal of Machine Learning Research_ 7.90, 2006, pp. 2541–2563  URL: http://jmlr.org/papers/v7/zhao06a.html

## Appendix

###  6.1 Note on computational problem

Consider the lower level problem:

$\psi(\mathbf{V})=\text{argmin}_{\mathbf{w}\in\mathcal{W}}L_{W}(\mathbf{V},\mathbf{w})=\|\mathbf{X}^{train}_{1}-\mathbf{X}^{train}_{0}\mathbf{w}\|^{2}_{V}.$

The objective function can be re-written as follows, dropping the train label
for ease of notation

$\displaystyle\|\mathbf{X}_{1}-\mathbf{X}_{0}\mathbf{w}\|^{2}_{V}$
$\displaystyle=(\mathbf{X}_{1}-\mathbf{X}_{0}\mathbf{w})^{\prime}V(\mathbf{X}_{1}-\mathbf{X}_{0}\mathbf{w})$
$\displaystyle=\sum_{k}x_{1k}^{2}v_{k}-2\sum_{j}w_{j}(\sum_{k}x_{jk}v_{k}x_{1k})+\sum_{i}w_{i}\sum_{k}x_{ik}v_{k}(\sum_{j}x_{jk}w_{j}).$

Then, the derivative with respect to $w_{j}$ is given by

$\frac{\partial L_{W}}{\partial
w_{j}}=-2(\sum_{k}x_{jk}v_{k}x_{1k})+\sum_{k}x_{jk}v_{k}(\sum_{i}x_{ik}w_{i})+\sum_{i}w_{i}\sum_{k}x_{ik}v_{k}x_{jk}$

and the derivative with respect to $v_{k}$

$\frac{\partial L_{W}}{\partial
v_{k}}=x_{1k}^{2}-2\sum_{j}w_{j}x_{jk}x_{1k}+\sum_{i}w_{i}x_{ik}(\sum_{j}x_{jk}w_{j}).$

Oberve that this implies that while the magnitude of $\psi(\mathbf{V})$
changes with the scale of $\mathbf{V}$ the minimizers $\mathbf{w}$ satisfying
$\frac{\partial\psi(\mathbf{V})}{\partial w_{j}}=0$ do not. Indeed,
multiplying all $v_{k}$s by a scalar $a>0$ will not change the set of
minimizers. This implies that we can not jointly minimize the upper and lower
level problems directly with the penalty
$\lambda\|\text{diag}(\mathbf{V})\|_{1}$, as
$\|\text{diag}(\mathbf{V})\|_{1}\to 0$ is optimal when $v_{k}\geq 0$. This is
why in Algorithm 1 we set a $v_{k}=1$ before the minimization step.

If $v_{k_{0}}=1$ for some $k_{0}\in\\{1,\dots,K\\}$, then

$\displaystyle\frac{\partial L_{W}}{\partial w_{j}}=-2(x_{jk_{0}}x_{1k_{0}}$
$\displaystyle+\sum_{k\neq
k_{0}}x_{jk}v_{k}x_{1k})+x_{jk_{0}}(\sum_{i}x_{ik}w_{i})+\sum_{k\neq
k_{0}}x_{jk}v_{k}(\sum_{i}x_{ik}w_{i})$
$\displaystyle+\sum_{i}w_{i}\sum_{k\neq
k_{0}}x_{ik}v_{k}x_{jk}+\sum_{i}w_{i}x_{ik_{0}}x_{jk_{0}}.$

In this case, the scale of $\mathbf{V}$ is relative to the
$\mathbf{X}_{k_{0}}$, so re-scaling the $v_{k}$ for $k\neq k_{0}$ by a
positive constant will change the set of minimizers given by
$\\{\frac{\partial L_{W}}{\partial w_{j}}=0\\}$. In practice, the choice of
$k_{0}$ is meaningful as every $k_{0}$ will yield slightly different
$\mathbf{w}_{j}^{*}$ and the predictor $k_{0}$ will be included with
probability one in the model. Researchers may choose a $k_{0}$ that they know
to be important (i.e. a covariate that should be included in the model given
domain knowledge), or may treat the $k_{0}$ as a hyper-parameter and iterate
over all possible $k$s and choose the $k_{0}$ that minimizes the upper level
loss.

###  6.2 Proof of Lemma 1

Consider the linear factor model described in section 3. For notational
convenience in this section we do not use boldface terms, and following [1] we
use $Y^{P}$ to denote the vector of outcomes for the pre-treatment period. Our
counterfactual will be a weighted average of the outcome variable for the
donor pool

$\sum_{j=2}^{J+1}w_{j}Y^{N}_{jt}=\delta_{t}+\theta_{t}\sum_{j=2}^{J+1}w_{j}Z_{j}+\lambda_{t}\sum_{j=2}^{J+1}w_{j}\mu_{j}+\sum_{j=2}^{J+1}w_{j}\epsilon_{jt}.$

As a result, the treatment effect
$\tau_{1t}^{w}=Y_{1t}-\sum_{j=2}^{J+1}w_{j}Y^{N}_{jt}$ for some weight vector
$w=\\{w_{j}\\}_{j=2}^{J+1}$ takes the form

$\tau^{w}_{1t}=\theta_{t}\left(Z_{1}-\sum_{j=2}^{J+1}w_{j}Z_{j}\right)+\lambda_{t}\left(\mu_{1}-\sum_{j=2}^{J+1}w_{j}\mu_{j}\right)+\sum_{j=2}^{J+1}w_{j}(\epsilon_{1t}-\epsilon_{jt}).$

Under some additional definitions and mean independence of the error term we
have that:

$\displaystyle\tau_{1t}^{w}$
$\displaystyle=\lambda_{t}(\lambda^{P^{\prime}}\lambda^{P})^{-1}\lambda^{P^{\prime}}\left(Y_{1}^{P}-\sum_{j=2}^{J+1}w_{j}Y_{j}^{P}\right)$
$\displaystyle+\left(\theta_{t}-\lambda_{t}(\lambda^{P^{\prime}}\lambda^{P})^{-1}\lambda^{P^{\prime}}\theta^{P}\right)\left(Z_{1}-\sum_{j=2}^{J+1}w_{j}Z_{j}\right)$
$\displaystyle-\lambda_{t}(\lambda^{P^{\prime}}\lambda^{P})^{-1}\lambda^{P^{\prime}}\left(\epsilon_{1}^{P}-\sum_{j=2}^{J+1}w_{j}\epsilon_{j}^{P}\right)$
$\displaystyle+\sum_{j=2}^{J+1}w_{j}(\epsilon_{1t}-\epsilon_{jt}).$

In [1], a bias bound is derived in the case in which we perfectly replicate
the treated unit and the first two terms are zero. They show that the last two
terms are $\text{O}\left(\frac{1}{T_{0}}\right)$. This paper explores the case
in which we have many covariates and therefore are likely to fall outside the
convex hull of the donor pool. In such cases, the synthetic control will not
be able to replicate the design matrix of the treated unit and the pre-
treatment fit will not be perfect.

Assume that $\sum_{t=1}^{T_{0}}\lambda_{t}^{\prime}\lambda_{t}$ is positive
semi-definite with smallest eigenvalue bounded away from zero by
$\underline{\xi}$ and $|\lambda_{tf}|<\bar{\lambda}$,
$|\theta_{tf}|<\bar{\theta}$ for all $t,f$. Then, it can be shown by the C-S
inequality that:

$\left(\lambda_{t}\left(\sum_{s=1}^{T_{0}}\lambda_{t}^{\prime}\lambda_{t}\right)^{-1}\lambda_{m}^{\prime}\right)^{2}\leq\left(\frac{\bar{\lambda}^{2}F}{T_{0}\underline{\xi}}\right)^{2}.$

Then, consider the first term in the decomposition of the treatment effect,

$\displaystyle\lambda_{t}(\lambda^{P^{\prime}}\lambda^{P})^{-1}\lambda^{P^{\prime}}\left(Y_{1}^{P}-\sum_{j=2}^{J+1}w_{j}Y_{j}^{P}\right)$
$\displaystyle=\sum_{m=1}^{T_{0}}\lambda_{t}\left(\sum_{s=1}^{T_{0}}\lambda_{t}^{\prime}\lambda_{t}\right)^{-1}\lambda_{m}^{\prime}(Y_{1m}-\sum_{j=2}^{J+1}w_{j}Y_{jm})$
$\displaystyle\leq\sum_{m=1}^{T_{0}}\left|\lambda_{t}\left(\sum_{s=1}^{T_{0}}\lambda_{t}^{\prime}\lambda_{t}\right)^{-1}\lambda_{m}^{\prime}\right|\left|Y_{1m}-\sum_{j=2}^{J+1}w_{j}Y_{jm}\right|$
$\displaystyle\leq\left(\frac{\bar{\lambda}^{2}F}{T_{0}\underline{\xi}}\right)\sum_{m=1}^{T_{0}}\left|Y_{1m}-\sum_{j=2}^{J+1}w_{j}Y_{jm}\right|$
$\displaystyle=\left(\frac{\bar{\lambda}^{2}F}{\underline{\xi}}\right)\text{MAD}\left(Y_{1}^{P},\sum_{j=2}^{J+1}w_{j}Y_{j}^{P}\right).$

Therefore, the bias contribution from the first term in the $\tau_{1t}^{w}$
decomposition (which we denote by $R_{1t}$) is bounded by:

$\mathbb{E}|R_{1t}|\leq\left(\frac{\bar{\lambda}^{2}F}{\underline{\xi}}\right)\mathbb{E}\text{MAD}\left(Y_{1}^{P},\sum_{j=2}^{J+1}w_{j}Y_{j}^{P}\right).$

Similar, the second term is given by

$\displaystyle\left(\theta_{t}-\lambda_{t}(\lambda^{P^{\prime}}\lambda^{P})^{-1}\lambda^{P^{\prime}}\theta^{P}\right)\left(Z_{1}-\sum_{j=2}^{J+1}w_{j}Z_{j}\right)$
$\displaystyle=\sum_{k=1}^{K}\left(\theta_{tk}-\sum_{l=1}^{T_{0}}\lambda_{t}\left(\sum_{s=1}^{T_{0}}\lambda_{s}^{\prime}\lambda_{s}\right)^{-1}\lambda_{l}^{\prime}\theta_{lk}\right)\left(Z_{1k}-\sum_{j=2}^{J+1}w_{j}Z_{jk}\right)$
$\displaystyle\leq\sum_{k=1}^{K}\left|\theta_{tk}-\sum_{l=1}^{T_{0}}\lambda_{t}\left(\sum_{s=1}^{T_{0}}\lambda_{s}^{\prime}\lambda_{s}\right)^{-1}\lambda_{l}^{\prime}\theta_{lk}\right|\left|Z_{1k}-\sum_{j=2}^{J+1}w_{j}Z_{jk}\right|$
$\displaystyle\leq\left|\bar{\theta}\left(1-\left(\frac{\bar{\lambda}^{2}F}{T_{0}\underline{\xi}}\right)\right)\right|\sum_{k=1}^{K}\left|Z_{1k}-\sum_{j=2}^{J+1}w_{j}Z_{jk}\right|$
$\displaystyle=K\left|\bar{\theta}\left(1-\left(\frac{\bar{\lambda}^{2}F}{T_{0}\underline{\xi}}\right)\right)\right|\text{MAD}\left(Z_{1},\sum_{j=2}^{J+1}w_{j}Z_{j}\right).$

The bias contribution from the second term ($R_{2t}$) is then given by:

$\mathbb{E}|R_{2t}|\leq
K\left|\bar{\theta}\left(1-\left(\frac{\bar{\lambda}^{2}F}{T_{0}\underline{\xi}}\right)\right)\right|\mathbb{E}\text{MAD}\left(Z_{1},\sum_{j=2}^{J+1}w_{j}Z_{j}\right).$

Given that the other two terms are $\text{O}\left(\frac{1}{T_{0}}\right)$ the
result follows.

###  6.3 Proof of Theorem 1

Start by re-writing the bi-level optimization problem as a convex optimization
problem where the lower level problem solutions are characterized by the
necessary Karush-Kuhn-Tucker (KKT) conditions. The program can therefore be
re-written as

$\displaystyle\min_{\bm{w},\bm{v},\kappa^{w}_{1},\boldsymbol{\kappa}^{w}_{2}}\quad$
$\displaystyle\frac{1}{T_{val}}\|\bm{Y}_{1}^{val}-\bm{Y}_{0}^{val}\bm{w}\|^{2}+\lambda(1+\sum_{k\neq
k_{0}}^{K}v_{k})$ $\displaystyle s.t.\quad$ $\displaystyle
2\mathbf{X}_{0}^{train^{\prime}}\mathbf{V}\mathbf{X}_{0}^{train}\mathbf{w}-2\mathbf{X}_{0}^{train^{\prime}}\mathbf{V}\mathbf{X}_{1}^{train}+\kappa_{1}^{w}\mathbf{1}_{J}+\boldsymbol{\kappa}^{w}_{2}=\mathbf{0},$
$\displaystyle\sum_{j}\kappa^{w}_{2j}w_{j}=0,$
$\displaystyle\kappa^{w}_{2j}\geq 0\text{ for all $j$},$ $\displaystyle
v_{k}\geq 0\text{ for all $k\neq k_{0}$}$

where $\kappa_{1}^{w}$ is the Lagrangian multiplier for the sum to 1
constraint and $\bm{\kappa}_{2}^{w}$ are the associated multipliers for the
non-negative constraint for the $w_{j}$ terms in the inner problem.

The associated Lagrangian for parameter vector
$\bm{\nu}=(\bm{w},\bm{v},\kappa^{w}_{1},\boldsymbol{\kappa}^{w}_{2},\boldsymbol{\kappa}^{v},\bm{\xi}_{1},\xi_{2},\bm{\xi}_{3})^{\prime}$
is

$\displaystyle\min_{\bm{\nu}}\mathcal{L}(\bm{\nu})\equiv$
$\displaystyle\quad\frac{1}{T_{val}}\|\bm{Y}_{1}^{val}-\bm{Y}_{0}^{val}\bm{w}\|^{2}+\lambda(1+\sum_{k\neq
k_{0}}^{K}v_{k})$
$\displaystyle+\bm{\xi}^{\prime}_{1}(2\mathbf{X}_{0}^{train^{\prime}}\mathbf{V}\mathbf{X}_{0}^{train}\mathbf{w}-2\mathbf{X}_{0}^{train^{\prime}}\mathbf{V}\mathbf{X}_{1}^{train}+\kappa_{1}^{w}\mathbf{1}_{J}+\boldsymbol{\kappa}^{w}_{2})$
$\displaystyle+\xi_{2}\sum_{j}\kappa^{w}_{2j}w_{j}$
$\displaystyle+\xi_{3}\boldsymbol{\kappa}^{w}_{2}$
$\displaystyle+\bm{\kappa}^{v^{\prime}}\bm{v}.$

subject to the KKT dual feasibility and slackness conditions:

$\displaystyle\text{{Complementary slackness}}:\quad$
$\displaystyle\sum_{k\neq k_{0}}\kappa^{v}_{k}v_{k}=0,$
$\displaystyle\sum_{j}\xi_{3j}\kappa_{j}^{w}=0.$ $\displaystyle\text{{Dual
feasibility}}:\quad$
$\displaystyle\quad\bm{\kappa}^{v}\geq\bm{0},\quad\bm{\xi}_{3}\geq\bm{0},$

where $\kappa^{v}_{1}$ $\bm{\kappa}^{v}_{2}$ are the associated Lagrangian
multipliers for the constraints on $v_{k}$ and $\bm{\xi}_{1},\xi_{2}$, and
$\bm{\xi}_{3}$ are the multipliers associated with the lower level KKT
necessary conditions.

Observe that the lower level loss first order condition is given by:

$\mathbf{X}_{0}^{train^{\prime}}\mathbf{V}\mathbf{X}_{0}^{train}\mathbf{w}-\mathbf{X}_{0}^{train^{\prime}}\mathbf{V}\mathbf{X}_{1}^{train}=\sum_{k}\mathbf{x}_{k}\mathbf{x}_{k}^{\prime}v_{k}\cdot\mathbf{w}-\sum_{k}\mathbf{x}_{k}x_{1k}v_{k}.$

Taking the derivative with respect to $v_{k}$ yields

$\frac{\partial}{\partial
v_{k}}\implies\mathbf{x}_{k}(\mathbf{x}_{k}^{\prime}\mathbf{w}-x_{1k}).$

It follows that the derivative of the objective function of
$\mathcal{L}(\bm{\nu})$ with respect to $v_{k}$ is given by

$\displaystyle\frac{\partial\mathcal{L}(\bm{\nu})}{\partial v_{k}}$
$\displaystyle=\xi_{1}^{\prime}\mathbf{x}_{k}(\mathbf{x}_{k}^{\prime}\mathbf{w}-x_{1k})+\kappa_{k}^{v}+\lambda.$

Under the assumption that that $\psi:\mathcal{V}\to\mathcal{W}$ is an
injective function, it follows that there is a unique solution to the lower
level optimization problem. This is the case when every subset of $k$ columns
of $\bm{X}_{0}$ spans $\mathbb{R}^{k}$ (that is, the columns in every subset
are linearly independent) and when $\bm{V}$ is diagonal and positive definite
so that $\bm{X}_{0}^{\prime}\bm{V}\bm{X}_{0}$ is non-singular. Since
$\lambda,\kappa_{k}^{v}\geq 0$, the FOC implies that
$\rho_{k}\equiv\xi_{1}^{\prime}\mathbf{x}_{k}(\mathbf{x}_{k}^{\prime}\mathbf{w}-x_{1k})\leq
0$. Given a choice of $\lambda$, by the complementary slackness condition
$\kappa_{v}^{k}>0$ for all $k$ such that $\rho_{k}+\lambda=0$ and
$\kappa_{v}^{k}=0$ otherwise. Therefore, the choice of $\lambda$, together
with $\bm{w}$ and the multipliers $\xi_{1}$, control how many predictors will
receive zero weight.

We will now show that as $T_{0},T_{val}\to\infty$, the $\rho_{k}$ for $k\in
S=\\{k\mid\theta_{kt}=0\text{ for all }k,t\\}$, do not converge to zero in
probability. Consider using the predictors $Z$ for the design matrix $\bm{X}$,
such that
$\rho_{k}=\xi_{1}^{\prime}\mathbf{x}_{k}(\mathbf{x}_{k}^{\prime}\mathbf{w}-x_{1k})=\xi_{1}^{\prime}\mathbf{Z}_{k}(\mathbf{Z}_{k}^{\prime}\mathbf{w}-Z_{1k})$.
Recall the separation assumption,

$\bm{w}^{*}\in\text{argmin}_{w\in\Delta^{J}}\mathbb{E}\|\bm{Y}^{val}_{1}-\bm{Y}_{0}^{val}\bm{w}\|^{2}$

satisfies that for all $k\in S$ and $l\in S^{c}$,
$|Z_{1k}-Z_{Jk}^{\prime}\bm{w}^{*}|>0$. By the reverse triangle inequality

$\displaystyle|Z_{1k}-Z_{Jk}^{\prime}\bm{w}|$
$\displaystyle=|Z_{1k}-Z_{Jk}^{\prime}\bm{w}^{*}-Z_{Jk}^{\prime}(\bm{w}-\bm{w}^{*})|$
$\displaystyle\geq\left||Z_{1k}-Z_{Jk}^{\prime}\bm{w}^{*}|-|Z_{Jk}^{\prime}(\bm{w}-\bm{w}^{*})|\right|$
$\displaystyle\geq|Z_{1k}-Z_{Jk}^{\prime}\bm{w}^{*}|-\sqrt{k}\sum_{j}(w_{j}-w^{*}_{j}).$

given that by assumption we have that $\|Z_{j}\|^{2}\leq\sqrt{k}$. It follows
that if for fixed $J$ $\bm{w}\overset{p}{\to}\bm{w}^{*}$ as $T_{val}\to\infty$
then $P(|Z_{1k}-Z_{Jk}^{\prime}\bm{w}|>0)\to 1$ as $T_{val}\to\infty$ so we
don’t have convergence in probability. Furthermore, under the injective
assumption of $\psi$ the $Z$ are linearly independent so it follows that
$\xi_{1}^{\prime}\mathbf{Z}_{k}\neq 0$ as by feasibility and the weight sum to
one restriction $\xi_{1j}$ can not be zero for all $j$. Therefore, it follows
that for fixed J, if as $T_{0},T_{val}\to\infty$,
$\bm{w}\overset{p}{\to}\bm{w}^{*}$ and $\lambda\to 0$, then

$P(\rho_{k}=0)\to 0.$

This implies that $P(\kappa_{k}^{v}=0)\to 0$ and, therefore, that for $k\in S$
for fixed J, if as $T_{0},T_{val}\to\infty$,
$\bm{w}\overset{p}{\to}\bm{w}^{*}$ and $\lambda\to 0$, then

$P(v_{k}=0)\to 1.$

This shows the first part of the theorem. If, furthermore, we have that for
$l\in S^{c}$ $|Z_{1k}-Z_{Jk}^{\prime}\bm{w}^{*}|=0$ (i.e. perfect fit) then a
similar argument yields that for fixed J, if as $T_{0},T_{val}\to\infty$,
$\bm{w}\overset{p}{\to}\bm{w}^{*}$ and $\lambda\to 0$, then

$P(v_{l}=0)\to 0.$

Next, we show that for fixed $J$ we have that
$\bm{w}\overset{p}{\to}\bm{w}^{*}$ as $T_{0},T_{v}al\to\infty$. Let
$Q=\mathbb{E}\|\bm{Y}^{val}_{1}-\bm{Y}_{0}^{val}\bm{w}\|^{2}$ and
$\hat{Q}=\frac{1}{T_{val}}\|\bm{Y}^{val}_{1}-\bm{Y}_{0}^{val}\bm{w}\|^{2}$.
Given the covariance stationarity assumption by a suitable LLN it follows that
for any $w$ we have that $\tilde{Q}\overset{p}{\to}Q$ as $T_{val}\to\infty$.
Hence, it follows that $\sup_{w}|\tilde{Q}(\bm{w})-Q(\bm{w})|\to 0$ as
$T_{val}\to\infty$. Furthermore, we have that $\tilde{Q}$ and $Q$ are
continuous and convex, and the simplex $\Delta^{J}$ is compact. Therefore, by
Lemma 3 of [5] (or Theorem 2.1 in [20]) it follows that
$\bm{\tilde{}}{w}\overset{p}{\to}\bm{w}^{*}$ where
$\bm{\tilde{}}{w}\in\text{argmin}_{w\in\Delta^{J}}\hat{Q}(\bm{w})$.

In general $\bm{\tilde{}}{w}$ need not be equivalent to the $\bm{w}$ that
solves the bi-level program. However, as $T_{0},T_{val}\to\infty$ and
$\lambda$ is chosen to minimize the validation loss as in our bilevel program,
$\bm{\tilde{}}{w}\overset{p}{\to}\tilde{w}$. The main observation is that the
bilevel loss nests the $\tilde{Q}$ loss at the optimum. Indeed, set all
$v_{k}$ weights to $0$ and $\lambda=0$, then the lower level problem loss
depends on $|Z_{1k_{0}}-Z_{Jk_{0}}^{\prime}w|$ and the upper level problem
loss is equivalent to $\tilde{Q}$. Under the oracle separation assumption it
follows that we only need to consider the upper level loss as it will
simultaneously minimize the lower level problem. For instance, if we can
perfectly fit the predictors $k\in S^{c}$ it follows that as
$T_{0},T_{val}\to\infty$ our bilevel loss coincides with $\tilde{Q}$ therefore
it follows by the trivial inequality (can’t do better than $\bm{w}^{*}$) that
$\bm{w}\overset{p}{\to}\bm{w}^{*}$.

###  6.4 Proof of Theorem 2: MSE Rates

We focus on the covariate matching problem with subGaussian noise:

$Z_{1}=Z_{0}w^{*}+\epsilon,\quad\epsilon\sim_{ind}\text{subG}(\sigma_{z}^{2}).$

Under A1-A3 we assume a sparse representation where only $k_{1}$ predictors
are non-zero. Theorem 1 implies that as $T_{0}\to\infty$ almost surely the
sparse predictors are not used in the model. Hence, with probability one, we
can re-write the optimization problem in terms of the true underlying sparse
model:

$\displaystyle min_{V,W}$ $\displaystyle
L_{V}(V,W)=\frac{1}{T_{val}}\|Y_{1}^{val}-Y_{0}^{val}W(V)\|^{2}+\lambda\|V\|_{1},$
s.t. $\displaystyle W(V)\in\psi(V),$ $\displaystyle V\in\mathcal{V},$

where $\psi:\mathcal{V}\rightrightarrows\mathcal{W}$ maps the upper level
solutions to the lower level optima

$\psi(V)\equiv
argmin_{W\in\mathcal{W}}L_{W}(V,W)=\|X^{train}_{1}-X^{train}_{0}W\|^{2}_{V},$

and

$\displaystyle W\in\mathcal{W}$
$\displaystyle\equiv\left\\{W\in\mathbb{R}^{J}\text{ }|\text{
}\mathbf{1}^{\prime}W=1,\text{ }W_{j}\geq 0,\text{
}j=2,\dots,J+1\right\\}\equiv\Delta^{J},$ $\displaystyle V\in\mathcal{V}$
$\displaystyle\equiv\\{(v_{1},\dots,v_{k})\mid v_{j}=0\text{ for }j\in
S,\text{ }v_{j}\in\mathbb{R}\text{ for }j=1,\dots k\\}.$

where $S=\\{k\mid\theta_{tk}=0\text{ for all }t\\}$ denotes the set of
nuissance predictors, and $|S^{c}|=k_{1}$. Consider the lower level program of
matching the covariates. For simplicity, restrict design matrix to the
covariates, without including transformations of the outcome variable.
Furthermore, let $Z$ be bounded such that $\max_{j}\|Z_{j}\|\leq\sqrt{k}$ as
in A1-A3. Denote the minimizer of the lower level program by $\hat{w}$, then
it follows that

$\displaystyle\|Z_{1}-Z_{0}\hat{w}\|^{2}_{V}$
$\displaystyle\leq\|Z_{1}-Z_{0}w^{*}\|^{2}_{V}$
$\displaystyle\|Z_{0}w^{*}-Z_{0}\hat{w}\|^{2}_{V}$ $\displaystyle\leq 4\langle
V^{T}\epsilon,\frac{Z_{0}w^{*}-Z_{0}\hat{w}}{\|Z_{0}w^{*}-Z_{0}\hat{w}\|_{V}}\rangle^{2}$
$\displaystyle\leq\sup_{b\in Z_{0}\Delta^{J},\|b\|=1}4\langle
V^{T}\epsilon,b\rangle^{2}$

Given our assumptions it can be shown that
$Z_{j}^{T}V^{T}\epsilon\sim\text{subG}(k_{1}\sigma_{z}^{2})$. Therefore, using
a maximal inequality it follows that

$MSE(Z_{0}\hat{w})=\frac{1}{k}\mathbb{E}\max_{b}\langle
V^{T}\epsilon,b\rangle\lesssim\frac{\sigma_{z}\sqrt{k_{1}}}{k}\sqrt{2\log J}.$

The rate for the standard synthetic control can be derived in a similar way,
without restricting the model to be in the non-sparse support of the
predictors.

###  6.5 Placebo variance estimation

We estimate the noise level using the placebo variance estimation bootstrap
proposed in [6], which follows from the placebo exercises first described by
[1]. This bootstrap procedure is valid when the noise distribution of the
treated and donor units is the same (homoskedasticity). A further discussion
on similar bootstrap procedures when the number of treated units is small can
be found in Conley and Taber (2011).

The bootstrap procedure works as follows. For $B$ replications:

  1. 1.

Randomly choose a donor unit $l$ to be treated.

  2. 2.

Compute the synthetic control weights $\hat{\bm{w}}^{b}$ using the remaining
controls units as the donor pool.

  3. 3.

Estimate the average treatment effect on the treated in the post treatment
period

$\hat{\tau}_{b}=\frac{1}{T-T_{0}}\sum_{t}Y_{lt}-\bm{Y}_{-lt}^{\prime}\hat{\bm{w}}^{b}.$

Then the placebo variance estimator is given by

$\hat{V}_{\tau}=\frac{1}{B}\sum_{b}(\hat{\tau}_{b}-\bar{\tau}_{b})^{2},$

where $\bar{\tau}_{b}=\frac{1}{B}\sum_{b}\hat{\tau}_{b}$. In a simulation
exercise, [6] show that the coverage properties of the placebo variance
bootstrap procedure are good.

###  6.6 Additional Simulation Figures

(c) $k_{1}=k_{2}=5.$

(d) $k_{1}=1$, $k_{2}=9.$

(e) SCM $\lambda^{*}=0$ $\bm{V}^{*}$

(f) Sparse SCM $\bm{V}^{*}$

Figure 5: Pre-treatment Fit and Predictor Fit.

  * •

Notes: Panels (a) - (b) show the kernel density across simulations of MADs of
the outcome variable for the pre-treatment period, with average values in
parenthesis. Panels (c) - (d) show the kernel density across simulations of
MADs of the useful predictors, with average values in parenthesis.