# On the Assumptions of Synthetic Control Methods

Claudia Shi  Columbia University  Dhanya Sridhar  University of Montreal
Vishal Misra  Columbia University  David M. Blei  Columbia University

###### Abstract

Synthetic control (SC) methods have been widely applied to estimate the causal
effect of large-scale interventions, e.g. the state-wide effect of a change in
policy. The idea of synthetic controls is to approximate one unit’s
counterfactual outcomes using a weighted combination of some other units’
observed outcomes. The motivating question of this paper is: how does the SC
strategy lead to valid causal inferences? We address this question by re-
formulating the causal inference problem targeted by SC with a more fine-
grained model, where we change the unit of the analysis from “large units"
(e.g. states) to “small units" (e.g. individuals in states). Under this re-
formulation, we derive sufficient conditions for the non-parametric causal
identification of the causal effect. We highlight two implications of the
reformulation: (1) it clarifies where “linearity" comes from, and how it falls
naturally out of the more fine-grained and flexible model, and (2) it suggests
new ways of using available data with SC methods for valid causal inference,
in particular, new ways of selecting observations from which to estimate the
counterfactual.

##  1 Introduction

Since their introduction [AG03, ADH10], synthetic control (SC) methods have
become commonplace for estimating causal effects from observational studies
with panel data.

Consider the following example. In 1988 California implemented a large-scale
tobacco control program, which increased the tobacco tax by 25 cents. [ADH10]
uses SC to study the effect of this program on the average cigarette
consumption in California. The dataset contains the annual per-capita
cigarette sales across a number of states, where none of the states other than
California implemented a similar tobacco program. This dataset is illustrated
in Table 1.

|  $-$1970 |  $-$1971 |  $-$1972 |  |  $-$1988 |  $-$1989
---|---|---|---|---|---|---
California | 123 | 121 | 123.5 |  | 90.1 | 82.4
Alabama | 89.8 | 95.4 | 101.1 |  | 112.1 | 105.6
Arkansas | 100.3 | 104.1 | 103.9 | $\cdots$ | 121.5 | 118.3
Virginia | 124.3 | 128.4 | 137 |  | 129.5 | 122.5
Wisconsin | 106.4 | 105.4 | 108.8 |  | 102.6 | 100.3
$\vdots$ | $\vdots$ | $\vdots$ | $\vdots$ |  | $\vdots$ | $\vdots$
Wyoming | 132.2 | 131.7 | 140.0 |  | 114.3 | 111.4
Table 1:  We observe the annual per-capita cigarette sales in packs of
different states from 1970 to 1989. The blue shaded cell reports California’s
per-capita sales under a tobacco program. The remaining cells report other
states’ per-capita sales without a tobacco program.

We observe that smoking in California decreased after the tobacco program.
However, we do not know whether the decrease is caused by the program or by
other causes. Thus, to assess this difference, our goal is to estimate
California’s _counterfactual outcome_. What would the 1989 smoking rate of
California had been if its tobacco program had _not_ been implemented?

SC is a method to solve this problem. It uses the data from before 1989—when
neither California nor the other states had implemented the tobacco program—to
learn a model of California’s smoking rate as a weighted combination of the
other states’ smoking rates. SC then uses the fitted weights to estimate
California’s counterfactual smoking rate in 1989.

In the general terminology of SC, California is the target, the other states
are the donors, and the tobacco program is the intervention. A typical
application of SC involves aggregated time series data, such as in Table 1,
with one target unit and a number of donor units. These units are often
“large” units, such as states [ADH10, BLR14, CS18], counties [AG03], and
districts [BRS17]. The causal question is one about the target’s
counterfactual, after the intervention.

To justify SC estimators, existing works often make parametric assumptions
about the true data generating process (DGP) of the potential outcomes of the
aggregated data. A common assumption is that the potential outcomes under
control (no tobacco program) are generated according to a linear factor model
with additive noise [Bai09]. Follow-up works develop different estimators
based on this assumption [Xu17, IKM21].

The purpose of this paper is to investigate the assumptions behind SC. When is
it suitable to assume a linear factor model, and why can we write the target
outcome as a weighted combination of the donors? We will show how to recover
the SC methodology, but without making explicit parametric assumptions about
the DGP of the potential outcomes.

The key idea behind this analysis is to construct a more fine-grained model of
potential outcomes, one where we change the unit of analysis from a “large
unit" to a “small unit." In the example, this change means that the potential
outcomes are defined by individuals instead of states. We assume that
different states index different distributions of individuals, and the state-
level outcome of interest (average smoking rate) is an average of the
individual outcomes in the state.

Under this fine-grained model, the causal effect targeted by classic SC is the
sub-population average treatment effect (SATE), averaged over the individuals.
We will derive sufficient conditions for the non-parametric causal
identification of the SATE, and we will see that it uses the SC strategy. That
is, we will derive sufficient conditions for the existence of a set of donors
and weights such that their weighted combination can be used to approximate
the effect.

This identification result further suggests new settings in which to use the
SC estimators, new ways to define the donors, and good heuristics for
selecting auxiliary covariates. In more detail, there are several implications
of this way of deriving the SC methodology.

First, the SC literature usually assumes that the control potential outcomes
are generated according to a linear factor model. With the fine-grained model,
we will see that the linear factor model form needs not be assumed a priori.
Rather, the factor form is a natural consequence of invariance assumptions
across groups (states) and time; and linearity is a consequence of the fact
that expectation is a linear operator. A practical implication of this
perspective is that SC can be used even if the individual-level DGP is non-
linear.

Second, the SC literature does not generally offer guidance about the
selection of the donors or how the choice of donors might affect the
corresponding estimate. When reasoning from the fine-grained model, we will
see how causal identifiability depends directly on properties of the target
and selected donors; it may be possible to write California as a weighted
combination of New York and Nevada, but not as a (non-zero) weighted
combination of New York, Nevada, and Florida. Practically, the identification
results suggest how to best choose donors for good SC estimation, and show
that SC does not require that donors belong to the same type of group-level
data. For example, we may correctly use data from Chicago (a city) to
approximate the counterfactual of California (a state).

Finally, the analysis here provides a general heuristic of deciding which
auxiliary covariates are suitable to include and which are not. We will see
that alternative measurements of the target outcomes (e.g. per-capita tobacco
spending measured in USD) are, in general, suitable auxiliary covariates,
whereas summaries of group-level characteristics (e.g. average age in states)
may be unsuitable auxiliary covariates.

#### Organization.

The paper proceeds as follows. In Section 1.1, we briefly review related work.
In Section 2, we formulate the tobacco tax example using both classical SC and
individual-level potential outcomes and introduce the corresponding estimands.
In Section 3.1, we introduce the SC estimators and review the common
assumptions made in the SC literature. In Section 3.2, we introduce the fine-
grained model. In Section 3.3, we establish sufficient conditions for causal
identification of the estimand using the SC strategy. In Section 3.4, we
discuss implications of the reformulation and the identification result, how
it points to new settings in which to use SC estimators and new ways to define
donors. In Section 4, we use the identification result to reason about what
are suitable auxiliary covariates. In Section 5, we study these implications
using simulation studies and the tobacco tax dataset. Finally, in Section 6,
we discuss limitations and future work.

###  1.1 Related Work.

This paper builds on the literature pioneered by [AG03, ADH10]. A large part
of the literature is about novel estimators [AI11, ADH15, Won15, DI16, Xu17,
ASS18, BMFR18, AL19, Amj+19, Ark+19, Li20, Aga+20, Ath+21, IKM21] and
inference methods [ADH10, DI16, FP17, ST19, CWZ21]. See [Aba19] for an
excellent review. This paper complements the existing work, as it interrogates
the assumptions made by many of these estimators and inference methods.

This paper contributes to the growing effort of providing causal
interpretations for synthetic controls [O’N+16] formalize and synthesize the
common assumptions in various methods for panel data inference. [Bot+21] study
SC estimators properties under a randomized experiment setup. [Shi+21] develop
identification and inference theory for the SC methods by drawing insights
from the proximal causal inference literature [MGTT18]. However, all of this
existing literature performs its analysis with group-level aggregates as
units. In contrast, this paper takes advantage of the nature of the group-
level data and shows how SC assumptions can arise from reasoning about
individual-level potential outcomes.

Finally, this paper contributes to the growing research on invariance and
causality [Sch+12, BP14, PBM16, Büh18, LC20, Sch+21]. In particular, a key
assumption in this paper is the independent causal mechanism principle
[PJS17].

##  2 Data and Problem Formulation

In this section we define the observed data, the group-level potential
outcomes that underlie classical SC, and the individual-level potential
outcomes that we consider in this paper. We define the causal estimand of
interest in both settings. For expository purposes we omit the auxiliary
covariates for now. We introduce them in Section 4.

###  2.1 The Observed Data

We have a dataset that contains the average smoking rate of $j=1,...,J$ states
for $t=1,...,T$ time periods. Let $\mu^{obs}_{jt}$ denote the average smoking
rate of state $j$ and time $t$. The _target_ state is $j=1$, i.e. California.
It is the only state that levied tobacco taxes. The remaining states $j\geq 1$
are potential _donors_ , which did not impose tobacco taxes. The intervention
(the tobacco taxes) happened at time $T_{0}$. To simplify notation, we assume
one post-intervention time period, $T=T_{0}+1$, though the analysis easily
generalizes to more post-intervention time periods. The number of time periods
$T$ and the potential donors $J$ are fixed.

###  2.2 Classical SC Potential Outcomes

SC estimators are usually developed under the potential outcomes framework for
causal inference [SNDS90, Rub74]. Each state is considered a unit. The
potential outcomes for each unit at each time period are
$(\mu_{jt}(0),\mu_{jt}(1))$. These variables are the average smoking rates of
state $j$ at time $t$, one in the world where state $j$ increased tobacco
taxes, and one in the world where state $j$ did not increase tobacco taxes. We
assume the treatment is well-defined and there is no interference between the
states [Rub80].

The observed outcomes are:

$\mu^{obs}_{jt}=\begin{cases}\mu_{jt}(1)&\text{if }j=1\text{ and }t=T\\\
\mu_{jt}(0)&\text{otherwise. }\end{cases}$ (1)

In other words, we observe each states’ smoking rate under no tobacco taxes
_except_ for California at time $T$, where we observe its smoking rate with
the tax.

###  2.3 Fine-Grained Potential Outcomes

This paper considers a more fine-grained model, where we treat individuals as
units and states as distributions of individuals. The pair
$(Y_{ijt}(1),Y_{ijt}(0))$ denotes the potential outcomes of individual $i$ in
group $j$ at time $t$, e.g. how many packs of cigarettes person $i$ in state
$j$ consumed at time $t$, under increased tobacco taxes or not. Note we never
make observations at an individual level, only in aggregate, but still we will
reason about these variables.

We also consider the variable $X_{ijt}\in\mathbb{Z}^{D}$. It is a vector of
causes that contribute to individual $i$’s outcome, such as age, education
level, or income. The relationship between the causes $X_{ijt}$ and potential
outcomes $(Y_{ijt}(0),Y_{ijt}(1))$ can be linear or non-linear, and can also
change across time periods. We emphasize that we _will not_ observe these
individual-level causes, but their existence will be crucial in our reasoning
about the assumptions of SC.

We assume that interventions are made at a group-level and individuals in each
group comply with their group-level intervention, i.e. individuals in
California do not go to Nevada to purchase tobacco and vice versa. The
observed group-level averages approximate expected individual-level potential
outcomes,

$\mu^{obs}_{jt}\approx\begin{cases}\mathbb{E}\left[Y_{jt}(1)\right]&\text{ if
}j=1\text{ and }t=T\\\
\mathbb{E}\left[Y_{jt}(0)\right]&\text{otherwise.}\end{cases}$ (2)

The expectation is taken over the individuals $i$.

###  2.4 Causal Estimand

We are interested in the causal effect of the tobacco taxes on the average
smoking of individuals in California at time period $T$. Using the classical
SC notation, this estimand is formally defined as the unit-specific treatment
effect,

$\displaystyle\tau_{T}=\mu_{1T}(1)-\mu_{1T}(0).$ (3)

Under the individual-level notation, the estimand is the sub-population
average treatment effect, averaged over individuals in the target
distribution,

$\displaystyle\tau_{T}=\mathbb{E}\left[Y_{1T}(1)-Y_{1T}(0)\right].$ (4)

######  Remark 1.

Being precise about the causal estimand is important, because different
estimands require different identifying assumptions. Eq. 3 is the unit-
specific treatment effect (UTE). 111The more common name for Eq. 3 is the
individual treatment effect, where the units are individuals. To avoid
potential confusion, we use UTE instead of ITE. In general, UTE is incredibly
difficult, if not impossible, to identify [HR10]. It involves strong
parametric assumptions on the data generating mechanism and the distribution
of the noise variable. In contrast, the causal estimand in Eq. 4 is the an
average causal effect. Causal identification of the average causal effect is
easier, and in general, does not require parametric assumptions [RR83, Imb04].

##  3 A Fine-Grained Model for SC

In this section, we first review the classical SC approach to causally
identify and estimate the estimand. We then develop a fine-grained model for
SC, one that makes several assumptions that will eventually lead to the non-
parametric identification of the causal estimand. Finally, we discuss the
practical implications of reasoning about the fine-grained model, and the
corresponding identification result.

###  3.1 Classical Synthetic Controls

The idea behind SC is to use the observed outcomes of the donor states, which
did not pass a tobacco tax, to help estimate the counterfactual California
outcome. Specifically, SC posits that there exists a donor set $D$ in the
potential donor pool $J$ and a weight set $\\{\beta_{j}\\}_{j\in D}$, such
that,

$\displaystyle\mu_{1t}(0)=\sum_{j\in D}\beta_{j}\mu_{jt}(0)\quad\forall t\leq
T.$ (5)

The validity of SC usually relies on parametric assumptions about the control
potential outcomes $\mu_{jt}(0)$. A common assumption is that the control
potential outcomes are generated according to a linear factor model plus noise
[Bai09],

$\displaystyle\mu_{jt}(0)=\lambda_{t}^{T}\gamma_{j}+\epsilon_{jt}.$ (6)

Here $\lambda_{t}\in\mathbb{R}^{R}$ is a time-specific vector of factors
shared across different units and $\gamma_{j}\in\mathbb{R}^{R}$ are unobserved
unit-specific factor loadings. The factor size $R$ is usually assumed to be
significantly smaller than the number of potential donors $J$ and the total
time periods $T$. The noise variable $\epsilon_{jt}$ is zero centered.222The
original SC [ADH10] for the tobacco tax example assume a variant of the factor
model in Eq. 6, which we discuss in Section 4.

Classical SC uses group-level observations to estimate the weights in Eq. 5.
Specifically, it fits the regularized least squares,

$\displaystyle\hat{\beta}=\min_{\hat{\beta}_{j\in
D}}\sum^{T_{0}}_{t=1}\big{(}\mu^{obs}_{1t}-\sum_{j\in
D}\mu^{obs}_{jt}\cdot\hat{\beta}_{j}\big{)}^{2}+\Upsilon(\hat{\beta}),$ (7)

where $\Upsilon(\hat{\beta})$ is a prior or regularizer. SC uses the learned
weights $\hat{\beta}$ to estimate the counterfactual California at time $T$.

To ensure a unique set of weights, existing works place restrictions on
$\hat{\beta}$. For example, the original SC estimator [ADH10] restricts the
weights to be positive and add up to one. [DI16] proposes an elastic-net
regularizer. [RSK17] suggests an entropy penalty.

###  3.2 Invariance Assumptions for the Fine-Grained Model

We now consider the fine-grained model, where we reason about an individual
$i$, and treat each state $j$ as a distribution of individuals. We will show
how to recover the SC strategy without making an explicit parametric
assumption on the data generating process of the potential outcomes.

The target estimand is the sub-population average treatment effect in Eq. 4.
Since the expected outcome under intervention
$\mathbb{E}\left[Y_{1T}(1)\right]$ can be trivially identified, the goal is to
causally identify the control expected outcome
$\mathbb{E}\left[Y_{1T}(0)\right]$ from the data distribution.

In this subsection, we discuss the invariance assumptions that will lead to
causal identification. In the next subsection, we will complete the derivation
of how to identify the expected counterfactual.

The first assumption is that of an independent causal mechanism (ICM) [Sch+12,
Sch+21]. ICM is a principle that the conditional distribution of each variable
given its causes (i.e. its “mechanism") does not inform or influence the other
conditional distributions [Sch+12].

In this context, the assumption means that the causal mechanism of an
individual’s tobacco consumption $Y_{ijt}(0)$ is independent of the
distribution of their causes $X_{ijt}$. If we know all the potential causes of
an individual’s tobacco consumption, then the distribution of the control
potential outcome is independent of which distribution (i.e. state) the
individual is from.

A1. (Independent Causal Mechanism)

Conditional on the causes $X$, the potential outcome $Y(0)$ is independent of
the population distribution $j$. For population distribution $j$ at time
$t\leq T$, the joint distribution of $Y(0)$ and $X$ is

$P_{jt}(X,Y(0))=P_{jt}(X)P_{t}(Y(0)\,|\,X).$ (8)

The assumption says that the distribution of individual causes $X$ can vary
across states and time, but the conditional outcome $Y(0)\,|\,X$ only varies
by time. For each time point $t$, if we know all the potential causes of an
individual’s smoking behavior, which state they are from does not provide any
additional information about the distribution of their control potential
outcome.

Using Eq. 8, we rewrite the expected counterfactual as

$\displaystyle\mathbb{E}\left[Y_{jt}(0)\right]=\sum_{x}\underbrace{\mathbb{E}_{t}\left[Y(0)\,|\,X=x\right]}_{\lambda_{t}}P_{jt}(X=x),$
(9)

where $\mathbb{E}_{t}$ denotes the expectation with respect to
$P_{t}(Y(0)|X=x)$, a distribution that is invariant across states.

Eq. 9 is similar to the factor model in Eq. 6, where the vector of factors
$\lambda_{t}$ is the vector of conditional expected outcomes, but notice we
did not make any assumptions about the relationship between the causes
$X_{ijt}$ and potential outcomes $Y_{ijt}(0)$. Rather, the linearity in Eq. 9
comes from the independent causal mechanism and iterated expectation — the
group-level outcomes are the averages of individual-level outcomes.

The second assumption is one of stable distributions. Given the target and the
_selected donors_ , i.e. donors that will be used to construct the SC, we can
further decompose the causes $X$ into causes that differentiate the target and
the selected donors, and causes that are invariant.

A2. (Stable Distributions)

Decompose the causes into two subsets $X=\\{U,S\\}$. Let $S$ denote the subset
that differentiates the target from the selected donors, i.e., its
distribution in the target group is different from its distribution in the
selected donor groups. We assume that, for all groups, the distribution of $S$
does not change for all time periods $t\leq T$,

$\displaystyle P_{jt}(X)=P_{j}(S)P_{t}(U\,|\,S).$ (10)

In other words, The subset $S$ contains causes that vary across states, but
are invariant across time. The conditional distribution of $U$ varies by time
but is invariant across states. We call $S$ the _minimal invariant set_.

######  Remark 2.

The minimal invariant set $S$ is determined by the choice of the selected
donors. For example, if we choose New Zealand as a donor to California, then
the set $S$ may be the same as $X$, because these two groups are very
different. If the donor is a “twin California," then the minimal invariant set
$S$ is an empty set.

With these assumptions in hand, we use Eq. 9 and Eq. 10 to rewrite the
expected counterfactual,

$\displaystyle\mathbb{E}\left[Y_{jt}(0)\right]=\sum_{s}\underbrace{\mathbb{E}_{t}\left[Y(0)\,|\,S=s\right]}_{\lambda_{t}}\underbrace{P_{j}(S=s)}_{\gamma_{j}}.$
(11)

Comparing Eq. 11 with the factor model in Eq. 6, we can see that the
conditional expectations are analogous to the time varying factors
$\lambda_{t}$. The probabilities are analogous to the state specific factor
loadings $\gamma_{j}$. What this equation shows is that with the two
invariance assumptions, the expected outcome is naturally expressed as a
factor model. Using the fine-grained model, we discover that the “linearity"
in SC comes from aggregation, and the factor model arises from the invariance
assumptions A1 & A2.

###  3.3 Causal Identifiability

While Eq. 11 is similar to the factor model in Eq. 6, it does not guarantee
causal identifiability. The reason is that the cardinality of the minimal
invariant set $S$ can be very large. In particular, if the cardinality of $S$
is larger than the number of donors then we cannot write the target as a
weighted combination of the donors.

Here, we establish sufficient conditions for the causal identifiability of the
causal estimand using the SC strategy. Causal identifiability is about
_whether we can_ express a causal estimand as a parameter of the observed
distributions [Pea00]. In classical SC, causal identifiability is assumed in
Eq. 5, that is, there exist a set of donors and weights, such that the
target’s counterfactual can be approximated as a weighted combination of the
donors’ observed outcomes.333Note, that causal identifiability is different
from model identifiability, which is about whether we can recover a unique set
of parameters from data.

To establish causal identifiability, we need to make two more assumptions
about the data distribution.

A3. (Sufficiently Similar Donors)

Let $D$ be the set of donors used to construct the synthetic control and $S$
be the minimal invariant set for the target and the selected donors. The
donors are sufficiently similar if the cardinality of the donor set is greater
than or equal to the cardinality of the minimal invariant set,

$\displaystyle|D|\geq|S|.$ (12)

As discussed in Remark 2, the cardinality of the minimal invariant set $S$ is
determined by the selected donors. If the selected donors are very different
from the target, the cardinality of $S$ is large. If they are similar, the
cardinality of $S$ is small.

A4. (Target Donors Overlap)

Let $\\{s_{1},...,s_{R}\\}$ be the support of $S$. There exists at least one
donor distribution $j$ in the selected donor set $D$, where $P_{j}(S=s)>0$.

A4 implies that every type of individual living in California with
characteristics $S=s$ might also live in one of the selected donor states.

A3 and A4 are two assumptions on the distribution of the minimal invariant set
$S$. While we do not directly observe $S$ in practice, we can still use it to
reason about the differences among the population distributions, and discuss
its influence on causal identifiability.

Finally, we derive sufficient conditions for non-parametric identification of
the causal estimand using the SC strategy.

######  Theorem 1.

(Causal Identifiability) Assume the causal mechanism is independent (A1), the
target and the selected donors are stable during the periods of investigation
(A2), the selected donors are sufficiently similar to each other (A3), and
there is overlap between the target and the selected donors (A4). Then there
exists a set of weights $\\{\beta_{j}\\}_{j\in D}$, such that across all time
periods, the target’s counterfactual can be written as a weighted combination
of the donors’ outcomes,

$\mathbb{E}\left[Y_{1t}(0)\right]=\sum_{j\in
D}\beta_{j}\mathbb{E}\left[Y_{jt}(0)\right]\quad\forall t\leq T.$ (13)

The proof is in Appendix A.

The conditions in Theorem 1 lead to the assumption (Eq. 5) commonly made in
the literature: the existence of synthetic controls. Note that we have arrived
at Eq. 5 without making any parametric assumptions about the mechanism
generating individual-level outcomes.

###  3.4 Implications

We have presented a set of causal assumptions that justify the SC methodology.
What are the implications of these results?

#### Mixing types of donors.

The fine-grained potential outcomes model in Section 2.3 provides insights
about what can be treated as a donor. Classical SC typically treats a state as
a unit, and chooses donors as other states. For example, [ADH10] excluded the
District of Columbia as a possible donor. The fine-grained model implies that
each donor need only be a group of individuals, and does not need to be the
same type of group as the target. A donor’s influence on the SC estimator has
to do with how different it is to the target and other donors, i.e., the
cardinality of the minimally invariant set. For example, in Section 5, we will
see that we can use districts or regions as potential donors to a target
state.

#### SC with non-linear DGPs.

Previous work on SC begins with a linear factor model assumption, such as the
one in Eq. 6 [Xu17]. However, it is unclear whether the role of the parametric
model is for causal identification, for statistical necessity, or for
notational convenience. As discussed in Remark 1, because the estimand is the
unit-specific treatment effect, a natural interpretation of Eq. 6 is that it
is an assumption on the data generating mechanism. Assuming the true mechanism
is linear can be an unrealistic assumption.

In contrast, using the fine-grained model, we explained why, fundamentally,
linearity can be a reasonable assumption in SC. We cast the estimand as an
average effect over sub-populations, and SC as a population re-weighting
algorithm. It make clear that the linear factor model in Eq. 6 encodes
invariance assumptions for causal identifiability, and that the linearity in
Eq. 6 arises from expectation being a linear operator. A practical implication
of this perspective is that the causal identification result holds even if the
fine-grained model involves a nonlinear mechanism. Thus SC estimators are
valid in settings where the individual-level DGPs are nonlinear.

#### The Role of $S$ and its relations to the donors.

Classical SC assumes the latent factors $\lambda_{t}$ in Eq. 6 are fixed and
low rank [Aba19]. Consequentially, we may be tempted to use information from
all the donors. We show that different donors can lead to different latent
factors. Specifically, in Eq. 11, we draw the analogy between the size of the
factors and the cardinality of the minimal invariant set $S$. We show that the
minimal invariant set $S$ is _determined_ by the donors used to construct the
synthetic control. Different donor sets can lead to different minimal
invariant sets and naively including additional donors may lead to the non-
existence of synthetic controls. Whether the assumption in Eq. 5 holds is a
property of the target and the selected donors.

##  4 Auxiliary Covariates

So far, we have discussed how to analyze panel data as in Table 1. In many
practical settings, we may observe additional state-specific covariates. For
example, we may observe the percentage of teenagers in each state.

Previous work incorporates the auxiliary covariates into the linear factor
model [ADH15]. For example, [ADH10] posits the following model,

$\displaystyle\mu_{jt}(0)=\delta_{t}+\lambda_{t}^{T}\gamma_{j}+\theta_{t}^{T}A_{j}+\epsilon_{jt},$
(14)

where $\theta_{t}\in\mathbb{R}^{R}$ and $\delta_{t}\in\mathbb{R}^{R}$ are
time-specific vectors of factors shared across different units and
$A_{j}\in\mathbb{R}^{k}$ is a vector of $K$ observed state-specific
covariates.

Specifically, [ADH10] assumes that is there exists a set of weights, such
that,

$\displaystyle A_{1k}=\sum_{j\in D}\beta_{j}A_{jk}\quad\forall k\leq
K\quad\text{and}\quad\mu_{1t}(0)=\sum_{j\in D}\beta_{j}\mu_{jt}(0)\quad\forall
t\leq T.$ (15)

Consequentially, one approach to using auxiliary covariates is to analyze them
in parallel with the outcomes to solve for the SC weights [ADH10, ADH15,
BMFR18, BF19].

This use of auxiliary covariates requires us to assume Eq. 14, that the
underlying data generating process is linear. A natural question is whether we
can still use auxiliary covariates to construct the SC weights without
assuming the underlying DGP is linear. Here, we will use the fine-grained
model to reason about _suitable auxiliary covariates_ , those that inherently
satisfy Eq. 15.

Using Eq. 11, we can reason about several types of suitable auxiliary
covariates. The first type are the state-specific probabilities of the
variables in the minimal invariant set $S$: $P_{j}(S=s)$. We observe that in
Eq. 11, the relationships between the probabilities and the outcomes are
linear. Therefore, the probabilities have the same relationship with one
another that the outcomes have with each other. For example, suppose we know
that the variable “age” differentiates the target and the donor distributions,
i.e. “age" is in $S$, then the “percentage of young adults" can be a suitable
covariate.

Note that some group-level summaries of individual-level characteristics may
not be suitable auxiliary covariates. For example, consider the average age
(within a state). Since we _do not_ assume a linear relationship between the
individual-level characteristics and the individual-level outcomes, we can not
expect linear relationships between the group-level summaries and the group-
level outcomes.

The second type of suitable auxiliary covariates are different measurements of
the target outcomes. With a bit of algebra, we can see that the SC weights in
Eq. 13 are combinations of the state-specific probabilities on the minimal
invariant set: $P_{j}(S=s)$. Recall that the minimal invariant set $S$ is
solely determined by the target and the selected donor and that they are not
influenced by the outcome measurements. Therefore, the SC weights should be
invariant to different measurements of the outcome variable $Y$. For example,
per-capita tobacco spending measured in USD would be a suitable auxiliary
covariate to the target outcome: average cigarette consumption measured in
packs.

Similarly, variables that share the same causes as the target outcomes and
satisfy assumption A1 are suitable auxiliary covariates. For example, if we
believe that the same set of causes influence “drinking” and “smoking”, and
none of the states implemented any policy for alcohol consumption during the
periods of consideration (A1 holds), then “annual average beer consumption"
would be a suitable auxiliary covariate to average cigarette consumption.

##  5 Empirical Studies

We use simulations and tobacco-program data to study this perspective on SC
and the implications of the theory around the fine-grained model.444code is
available at github.com/claudiashi57/fine-grained-SC We find the following.

  1. 1.

There is no reason the donors need to come from the same type of group as the
target. We can still recover meaningful causal estimates when using donors
from a different type.

  2. 2.

The SC estimators are valid even when the individual-level causal mechanisms
are nonlinear.

  3. 3.

The cardinality of the minimal invariant set $S$ is dependent on the donor and
target choices and is crucial to whether the weights can be generalized to the
counterfactual.

  4. 4.

We may improve SC estimates when we include suitable auxiliary covariates in
the analysis. However, unsuitable covariates will bias the estimates.

#### Simulations.

Following the fine-grained model in Section 3, we first generate individual-
level data, then construct group-level summaries. The individual-level
covariates $X$ take $K=12$ values. Individual-level outcomes are derived from
a set of non-linear and time-varying functions. We create one target group and
$5$ donor groups. Each group has a different composition of individuals. The
compositions do not change over time.

We consider $T$ time periods. For each group, at each time period, we sample
$2000$ individuals according to its population composition. The group-level
summaries, $\mu^{obs}_{jt}$, are the average outcomes of individuals in group
$j$ at time point $t$. The randomness is on an individual level, instead of a
group level.555More simulation details are in Appendix B

We create two knobs in the simulation, $S$ and $T$. The variable $T$ denotes
the number of time periods, corresponding to the number of data points when
fitting and evaluating the SC estimator. The set $S$ is the minimal invariant
set. We use $|S|$ to denote the cardinality of $S$, and specifically how much
the target and selected donor distributions differ from each other. $|S|$
ranges from $0$ to $K$. If the donors are identical to the target $|S|=0$. If
the donors are very different in all aspects of the population composition
$|S|=K$. We do not observe the minimal invariant set $S$ and its cardinality.
The SC estimators do not use $S$ or $|S|$.

Figure 1: Donors are not required to be of the same type: we use a linear
combination of divisions to capture the outcome trends of California (a state)
with high fidelity.

#### Prop 99.

Following [ADH10], we analyze data about the Prop 99 tobacco program. We use
the state-level data for the period 1970–2000. We exclude states that also
implemented large tobacco programs during the time frame and the states that
raised tobacco tax by more than $50$ cents, resulting in $39$ potential
donors. The outcome measurement is the per-capita cigarette sales in packs.
The main distinctions to [ADH10] are that (1) we include Washington DC in the
donor pool, and (2) exclude the state-level covariates.

#### Methods and evaluation.

For the Prop 99 example, we use the original SC estimator, with positive
weights that sum up to one. Since we cannot observe counterfactuals, we
evaluate the estimation quality by plotting out the estimated counterfactuals.

For the simulation studies, we use ordinary least squares (OLS) as the SC
estimator. We use $75\%$ of the data to fit the estimator and $25\%$ of the
data for out-of-sample evaluation. The evaluation metric is the mean squared
error averaged over data (time) points. For expository purposes, when
discussing the estimation quality, we use “observed" and “counterfactual"
instead of “in-sample" and “out-of-sample".

#### (1) Mixing types of donors.

As discussed in Section 3.4, there is no reason to restrict donors to be of
the same type as the target. To study this possibility empirically, we
consider a type of donor that is different from states. Since 1950, the United
States Census Bureau has defined nine statistical divisions based on
geographical location, e.g. New England, Mountain. Each division contains
several states. We construct divisional-level donors using the United States
census of 1990. The average smoking rate of each division is a weighted
combination of the smoking rate in its corresponding states, weighted by their
population.

We use the original SC estimator to construct a synthetic California using
these divisional-level data. We compare the counterfactual prediction of the
divisional-level SC estimator with the original SC estimator. As shown in Fig.
1, the synthetic California constructed by divisional-level data can capture
the outcome trends of California with high-fidelity. We interpret the weights
of the SC estimator in Appendix C.

Figure 2:  SC estimators are valid even when the causal mechanisms generating
individual-level outcomes are nonlinear. The figure reports the observed and
counterfactual prediction loss, in settings where the group-level measurements
are the “mean” or the “median” of the individuals in the groups.

#### (2) SC with no-linear DGPs.

Section 3.2 argues that the linearity in SC comes from aggregation, rather
than a linear individual-level data generating process. We study this claim
empirically using the nonlinear data simulation described above. We have data
from six groups, one is the target and the other groups are the donors. We set
the cardinality of $S$ to $5$ and consider a range of time periods for the
data, from $T=20$ to $T=90$.

For a given number of time periods, we construct two panel datasets. The first
dataset contains the _average_ outcomes of individuals in groups. The second
includes the _median_ outcomes of individuals in groups. Note that the “mean”
is linear, where the “median” is nonlinear.

We apply the SC estimator to both panel datasets and evaluate the predictive
performance on the observed and counterfactual data. As shown in Fig. 2, when
the individual-level DGP is nonlinear, the SC estimator can still produce
valid counterfactual estimates for the average outcomes. Of course, linearity
does not come for free. SC estimates are valid in this example because the
“mean" is a linear function, and the cardinality of the set $S$ is not greater
than the number of available donors. In contrast, when the measurement is the
“median", the SC estimator fails at predicting the counterfactual, because the
median is a nonlinear function. Thus, we cannot expect a linear relationship
between the median of the target group and the median of the donor groups.

Figure 3: The more different the donors are, the worse the SC counterfactual
estimates become. The red dotted line denotes the number of donors used for
constructing the synthetic controls.

#### (3) The minimal invariant set $S$ is critical to causal identification.

As discussed in Section 3.3, the minimal invariant set $S$ and whether Eq. 5
holds are properties of the target and the donors. If we choose donors that
are drastically different from the target, the SC weights learned with the
observed data may not generalize to the counterfactual data. We use nonlinear
simulations to study the relationship between the donor choice and the quality
of the counterfactual estimates. We fix the number of the donors to $5$, the
number of time periods to $20$, and increase the cardinality of $S$ from $2$
to $11$.

As shown in Figure 3, once the cardinality of $S$ surpasses the number of
available donors, the counterfactual estimation error increases significantly.
Importantly, it is increasing at a significantly faster rate than the observed
error. We cannot determine whether the SC estimator can produce valid
counterfactual estimates from the observed dataset alone.

Table 2: Using suitable covariates improves the estimation quality, whereas unsuitable covariates hurt the estimation quality. The table reports the mean squared error and standard error over 100 simulations. MSE $\pm$ SE | Observed | Counterfactual
---|---|---
Outcome Only | $.07\pm.03$ | $.14\pm.05$
Suitable Covariates | $.06\pm.02$ | $.13\pm.05$
Unsuitable Covariates | $.06\pm.02$ | $.24\pm.13$

#### (4) Auxiliary Covariates.

Finally, we study what happens to the counterfactual estimates when we include
auxiliary covariates. Using the simulations, we construct $10$ suitable
auxiliary covariates and $10$ unsuitable auxiliary covariates. The suitable
covariates are the averages of the sine transformation of individual-level
outcomes. The unsuitable covariates are averages of the individual-level
covariates. We fix the number of the donors to $5$, the cardinality of the
minimal invariant set to $5$, and the number of time periods to $15$. We
examine the observed and counterfactual estimation quality when including
suitable covariates and including unsuitable covariates. As shown in Table 2,
incorporating suitable covariates may improve the counterfactual estimation,
whereas including unsuitable covariates hurts the counterfactual estimation.
Notably, we may not infer whether an auxiliary covariate is suitable by
looking only at the SC estimator’s fit to the observed data.

##  6 Discussion & Future Work

In this paper, we develop a fined-grained model for synthetic controls. Using
the tobacco example, we show that the “linearity" in SC comes from
aggregation: the group-level outcomes are averages of individual-level
outcomes. We further establish sufficient conditions for the non-parametric
identification of the causal estimand and discuss several practical
implications.

While this paper points to new ways of applying SC methods, the validity rests
on the strong assumptions that an analyst must carefully consider. For future
work, we plan to establish uncertainty quantification methods that are
compatible with the fine-grained model. We also plan to develop sensitivity
analyses that show how violations of the assumptions change the estimated
effects.

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##  Appendix A Proof For Thm 1

######  Theorem 1.

Assume the target and the selected donors are stable during the periods of
investigation (A2), the donors are sufficiently similar to each other (A3),
and there is overlap between the target and the donors (A4). Then there exists
a set of weights $\\{\beta_{d}\\}_{d\in D}$, such that across all time
periods, the target’s counterfactual can be written as a weighted combination
of the donors’ outcomes,

$\mathbb{E}\left[Y_{1t}(0)\right]=\sum_{d\in
D}\beta_{d}\mathbb{E}\left[Y_{dt}(0)\right]\quad\forall t\leq T.$ (16)

###### Proof.

We first show that for a fixed time point $t$, there exist a set of weights
such that the target can be written as a weighted combination of the donors.
We then show that there exists a set of weights that is invariant across time
periods.

Fixing a time point $t$, we can write out Eq. 11,
$\mathbb{E}\left[Y_{jt}(0)\right]=\sum_{s}\mathbb{E}_{t}{Y(0)\,|\,S=s}P_{j}(S=s)$,
for the target $j=1$ and the selected donors $D$. Conceptually, we can think
of the set expanded expectations as a system of linear equations, where the
conditional expectations are the unknowns, and the probabilities are the
scalars. A4 says that the unknowns in the target equation are also in at least
one of the donor equations. A3 says that there are at least as many
independent equations as the number of unknowns. Combining A3 & A4, we can
“solve" the unknowns. Consequentially, we can write the target as a weighted
combination of the donors, where the weights are functions of the
probabilities.

A2 implies the probabilities are the same across time periods. Since the
weights are functions of the probabilities, and the probabilities are
invariant across time periods, the weights are also invariant across time
periods. ∎

##  Appendix B Simulation Details.

We discuss the details of the simulation studies. Recall, the individual-level
covariates take $K=12$ values. There are $6$ groups. Each group has a
different composition of individuals, denoted by $\boldsymbol{P}_{j}$. The
sparsity of the probabilities is determined by the cardinality of the minimal
invariant set $S$.

Group-level parameters $\displaystyle\alpha_{sk}$ $\displaystyle\sim
Bin(1,1-\frac{|S|}{K})$ $\displaystyle\boldsymbol{\alpha}_{s}$
$\displaystyle=(\alpha_{s1},...,\alpha_{sk})$
$\displaystyle\boldsymbol{P}_{j}$ $\displaystyle\sim
Dir(K,\boldsymbol{\alpha}_{s})$ Individual-level data $\displaystyle X_{ijt}$
$\displaystyle\sim Cat(K,\boldsymbol{P}_{j})$ $\displaystyle Y_{ijt}$
$\displaystyle=f^{t}(X_{ijt})+N(0,1)$ $\displaystyle\mu_{jt}$
$\displaystyle=\frac{1}{N_{j}}\sum Y_{ijt}$

Individual-level outcomes are derived from a set of non-linear and time-
varying functions. The exact functions are in the supplementary material. The
individual-level covariates take $K=12$ values. At each point $t$ and for each
group $j$, we sample $N_{j}=1000$ individuals. The group-level summaries,
$\mu^{obs}_{jt}$, are the average outcomes of individuals in group $j$ at time
point $t$.

##  Appendix C Prop 99 Experiment Details.

In Fig. 1, we show that the synthetic California constructed by divisional
level donors can capture the outcome trends of California with high fidelity.
Here we describe how the donors are constructed.

Since 1950, the United States Census Bureau divided the United States into
nine divisions: New England, Mid-Atlantic, East North Central, West North
Central, South Atlantic, East South Central, West South Central, Mountain, and
Pacific. Each division consists of several states. Following [ADH10], we
exclude states that also implemented large tobacco programs during the time
frame and the states that raised tobacco tax by more than 50 cents:
Massachusetts, Arizona, Oregon, Florida, Alaska, Hawaii, Maryland, Michigan,
New Jersey, New York, and Washington.

We construct divisional-level donors according to the United States census of
1990. Each divisional donor is a weighted (by population) combination of its
corresponding states that were not excluded for implementing similar policies.
We drop the Pacific division because all states in the division have been
excluded. We use the original SC estimator to construct a synthetic California
using these divisional-level data.

Division | Weight
---|---
New England | .05
Mid-Atlantic | 0
East North Central | 0
West North Central | 0
South Atlantic | 0
East South Central | 0
West South Central | 0
Mountain | .95
Pacific | -
Table 3: Divisional-level weights used to construct the synthetic California.

As shown in Table 3, the synthetic California uses only two donors: Mountain
division and New England division. This is not surprising because California
is geographically close to the Mountain division. Table 3 is also consistent
with the result in [ADH10], where the chosen state-level donors come from
either the Mountain division or the New England division.

Changing the unit of analysis does not necessarily harm interpretability.
California is a state with a high population density. According to the 1990
census, the population in California is around $30$ million. The total
population in the Mountain division used to construct the control is around
$10$ million. In contrast, the population in Montana, a donor used in [ADH10]
with $0.2$ weights, is only around $0.8$ million. Taking population level into
consideration, it is as interpretable, if not more, to treat divisions as
potential donors to California.