Causal Inference Using Factor Models

Causal Inference Using Factor Models

Introduction

Causal inference methods for policy evaluation, particularly synthetic control and difference-in-differences, have become widely used in empirical work. The synthetic control method, introduced by Abadie_Gardeazabal_2003 and developed further by Abadie_Diamond_Hainmeuller_2010,Abadie_Diamond_Hainmeuller_2015, constructs a weighted combination of control units that matches the treated unit's pre-treatment characteristics and outcomes, and uses this synthetic counterpart to form a post-intervention counterfactual. Similarly, the difference-in-differences approach, exemplified by Card_Krueger_1994, compares the change in outcomes for a treated group before and after an intervention to the corresponding change for a control group over the same period.

Both methodologies rely on restrictions that make the untreated potential outcomes for treated units recoverable from the behavior of untreated or control units. In difference-in-differences, this restriction is commonly expressed as parallel trends; in synthetic control, it is based on pre-treatment fit and the stability of the relationship between treated and control outcomes. However, real-world data often exhibit heterogeneous trends, challenging the plausibility of these restrictions. Gobillon_Magnac_2016 and Xu_2017 address heterogeneous trends through panel data models with interactive fixed effects, allowing for unit-specific exposure to common shocks.

In this paper, we employ a factor model to decompose potential outcomes into systematic and idiosyncratic components. A policy intervention can affect both components. The individual causal effect can therefore be written as the sum of a systematic and an idiosyncratic causal component. We emphasize that, while the idiosyncratic component is not point identified for a fixed unit and date, the systematic component is identified. Moreover, we interpret the impact of the policy intervention as a structural-break problem in the factor representation, which can be rigorously studied using established structural-break theory. The structural-break perspective also clarifies which features of the data are required for identification under different empirical environments.

The paper makes three contributions. First, it separates the realized unit-time treatment effect into a systematic component, generated by changes in factor loadings, slope coefficients, and possibly factors, and an idiosyncratic component that is not point identified for a fixed unit and date. Second, it provides estimation and inference for the systematic component in settings with one treated unit or many treated units, making the framework applicable to empirical settings in which synthetic-control methods are commonly used. Third, it extends the framework to policies that may alter the factor process itself, showing when such effects are identifiable and when additional restrictions, such as constant or affine factor shifts, are needed.

These contributions are developed across a number of empirically relevant environments. First, the policy intervention may leave the common-shock process unchanged but alter treated units' exposure to these shocks, so that treatment effects arise through structural breaks in factor loadings and possibly slope coefficients. This benchmark is appropriate for targeted interventions whose general-equilibrium feedback to aggregate trends is plausibly negligible. It remains feasible even when the number of treated units is very small, including a single treated unit, because the common factors can be learned from the control group and treated parameters are identified from time-series variation. Second, the intervention may also alter the common-shock process itself; in this case, a flexible post-treatment factor process can be identified when the treated cross section is large, which permits direct estimation of post-treatment treated factors. Third, when the intervention may affect both factors and loadings but the treated group is small, a fully flexible post-treatment factor process is not separately identifiable; we therefore impose a restricted post-treatment factor perturbation, such as an affine shift, which preserves tractable identification and inference while still allowing the policy to change the common-shock process.

A main feature of our approach is a dual modeling strategy: we model both the counterfactual potential outcome $Y_{it}(0)$ and the observed outcome $Y_{it}(1)$ within the same factor structure. In many panel settings, researchers observe only a subset of the relevant determinants of outcomes, and idiosyncratic variation can be large relative to the predictable component. Consequently, if one models only $Y_{it}(0)$, the gap between the realized outcome $Y_{it}(1)$ and the model-implied counterfactual $\hat Y_{it}(0)$ may be dominated by residual noise and unmeasured determinants, making the difference $Y_{it}(1)-\hat Y_{it}(0)$ an unstable object for inference. By modeling both potential outcomes, the analysis targets the change in the systematic component directly, instead of treating unit-time idiosyncratic noise as part of the causal signal.

Our framework relates to, but differs from, existing approaches to panel-data program evaluation. Difference-in-differences and synthetic-control methods typically focus on constructing the untreated counterfactual outcome for treated units. Interactive fixed-effect methods enrich this counterfactual by treating latent factors as controls for unobserved confounding, analogous to observed covariates. In these approaches, the factor component is primarily a control for the untreated outcome process.

In contrast, our framework models both potential outcomes within a factor structure and allows the treated units' factor loadings to change after the intervention. Thus the factor component is not merely a control for unobserved heterogeneity: changes in exposure to common shocks are themselves part of the systematic causal effect. This shift leads to a different target, the systematic component of the unit-time treatment effect, rather than the difference between a realized treated outcome and an imputed untreated outcome. Section (ref) discusses these connections in more detail.

The remainder of the paper is organized as follows. Section (ref) introduces the model and conceptual framework and compares our approach to existing methods. Section (ref) studies identification of systematic causal effects. Section (ref) extends the framework to allow for potential factors, in which the intervention may also alter the common-shock process. Section (ref) develops estimation and inference procedures. Section (ref) reports Monte Carlo evidence. Section (ref) presents empirical applications to the two datasets analyzed by Abadie_Diamond_Hainmeuller_2010,Abadie_Diamond_Hainmeuller_2015. The last section concludes. Additional technical material is collected in the Appendix, and proofs are provided in the Online Appendix.

Modeling the Potential Outcomes

We consider a panel data set that includes an outcome variable and some covariates. The observed outcome variable $Y$ is indexed by unit and time, i.e., $Y_{it}$, $i=1,2,\ldots,n$, $t=1,2,\ldots,T$. The potential outcome for unit $i$ in period $t$ is denoted by $Y_{it}\left(d\right)$, $d=0,1$, with $d=1$ referring to the case of treatment and $d=0$ for the case of no treatment. Assume that a policy intervention occurs in period $T_{0}+1$ with $1<T_{0}<T$. Let $D_{it}$ denote the observed treatment dummy. The policy intervention only applies to units $i\leq n_{0}$ without directly affecting units $i>n_{0}$. To focus on the main idea, we assume that the policy intervention occurs in the same period for all treated units. The treatment status can be summarized by

More compactly, $D_{it}=1\left\{ i\leq n_{0},t>T_{0}\right\} $, where $1\left\{ \cdot\right\} $ is the indicator function.

Our theory will be developed under the conditions where $n-n_{0}\rightarrow\infty$, $T_{0}\rightarrow\infty$, and $T-T_{0}\rightarrow\infty$. Within this framework, the number of treated units, $n_{0}$, may either be a fixed constant or approach infinity. Importantly, we allow for the case of a single treated unit ($n_{0}=1$), which is directly related to the synthetic control literature.

We use a dual modeling strategy that characterizes both potential outcomes through a factor model:

where $X_{it}$ denotes the vector of observed covariates and $f_{t}$ is an $r\times1$ vector of unobserved factors. For a given treatment status $d$, $\lambda_{i}\left(d\right)$ represents the $r\times1$ vector of unobservable factor loadings, $\beta\left(d\right)$ is the vector of coefficients, and $\varepsilon_{it}\left(d\right)$ denotes the idiosyncratic error, where the factor loadings, slope coefficients, and idiosyncratic errors are indexed by treatment status $d$.

We interpret the factors $f_t$ as latent common shocks or trends generated outside individual units, such as aggregate macroeconomic conditions, industry-wide demand shifts, or other pervasive forces that move many units simultaneously. The policy intervention is assumed not to create these common forces; rather, it changes how treated units respond to them. In the factor representation, this corresponds to structural breaks in the treated units' factor loadings (and possibly slope coefficients), while the factor process itself remains common across units. This benchmark is especially appropriate when the treated group is small relative to the population or when the intervention is plausibly partial-equilibrium, so that general-equilibrium feedback to aggregate trends is negligible. We relax this restriction in the potential-factor analysis, allowing the intervention to alter the factor process when such feedback is plausible.

For treated units, the observed outcome is

For untreated units, the observed outcome is \[ Y_{it}=\lambda_{i}\left(0\right)^{\prime}f_{t}+X_{it}^{\prime}\beta\left(0\right)+\varepsilon_{it}\left(0\right)=Y_{it}\left(0\right),\;i=n_{0}+1,\ldots,n,\;t=1,\ldots,T. \]

The causal effect for the treated units is defined as: \[ \tau_{it}=Y_{it}\left(1\right)-Y_{it}\left(0\right)=Y_{it}-Y_{it}\left(0\right),\;t>T_{0},\;i=1,\ldots,n_{0}. \] Using the factor model, we can rewrite $\tau_{it}$ for $i\le n_{0}$ and $t>T_{0}$ as the sum of a systematic causal effect and an idiosyncratic causal effect:

This representation enables us to assess the sources of heterogeneous causal effects arising from structural breaks in factor loadings, covariate coefficients, or both. We will use $\tau_{it}^{*}$ to denote the systematic causal effect

Our object of interest is the systematic causal effect $\tau_{it}^*$. Note that the idiosyncratic causal effect $\varepsilon_{it}\left(1\right)-\varepsilon_{it}\left(0\right)$ is unobserved, making the individual causal effect $\tau_{it}$ non-identifiable without additional assumptions. Nevertheless, the cross-sectional average causal effect $\bar{\tau}_{t}\equiv\frac{1}{n_{0}}\sum_{i=1}^{n_{0}}\tau_{it}$ remains identifiable, as the average difference in errors $\frac{1}{n_{0}}\sum_{i=1}^{n_{0}}\left[\varepsilon_{it}\left(1\right)-\varepsilon_{it}\left(0\right)\right]$ will converge to zero in probability if $n_{0}\rightarrow\infty$, under some standard assumptions on the error terms $\varepsilon_{it}(d)$. Likewise, the time average causal effect $\bar{\tau}_{i}\equiv\frac{1}{T-T_{0}}\sum_{t=T_{0}+1}^{T}\tau_{it}$ is also identifiable if $T-T_0$ goes to infinity. Thus the average causal effect and the average systematic causal effect can be asymptotically equivalent under additional assumptions. In Section (ref), we detail the identification of the systematic causal effect $\tau_{it}^{*}$.

The existing literature on causal inference typically focuses on modeling the potential outcome $Y_{it}\left(0\right)$ exclusively, estimating a model-implied $\hat{Y}_{it}\left(0\right)$, while imposing no model on $Y_{it}\left(1\right)$. Consequently, the implied estimator for the treatment effect for the treated unit is defined as $Y_{it}\left(1\right)-\hat{Y}_{it}\left(0\right)$. We argue in subsections (ref) and (ref) that this approach may lead to estimators with large imputation errors due to the presence of $\varepsilon_{it}\left(d\right)$, which is $O_{p}\left(1\right)$. To see a simple example, assume $Y_{it}\left(1\right)$ is model-free while the model for $Y_{it}\left(0\right)$ consists of a single regressor and no factors, i.e., $Y_{it}\left(0\right)=X_{it}\beta\left(0\right)+\varepsilon_{it}\left(0\right)$. Given a consistent estimator $\hat{\beta}\left(0\right)$ for $\beta\left(0\right)$, this model implies $\hat{Y}_{it}\left(0\right)=X_{it}\hat{\beta}\left(0\right)$. The conventional estimator for the treatment effect for the treated would be $Y_{it}-\hat{Y}_{it}\left(0\right)$ for $i\leq n_{0}$ and $t>T_{0}$, which can be further represented as

where $\tau_{it} =Y_{it}\left(1\right)-Y_{it}\left(0\right)$. The estimator contains an idiosyncratic imputation error that does not vanish for a fixed treated unit and post-treatment period. As a result, the conventional estimator $Y_{it}-\hat{Y}_{it}\left(0\right)$ is generally inconsistent for $\tau_{it}$.

In contrast, our approach models both potential outcomes, \(Y_{it}(0)\) and \(Y_{it}(1)\). The purpose is not to claim that each potential outcome can be predicted without error. In panel applications, the fitted value of a potential outcome may differ substantially from the realized outcome because of omitted variables, idiosyncratic shocks, or model misspecification. This concern is especially relevant when panel regressions have low explanatory power.

The distinction matters because conventional imputation methods usually model only the missing untreated outcome \(Y_{it}(0)\), while using the realized treated outcome \(Y_{it}(1)\) directly. Even if the imputation recovers the systematic component of \(Y_{it}(0)\), the resulting estimator may still contain the one-sided idiosyncratic error associated with the untreated potential outcome. Thus, for a fixed unit and period, the imputation error need not vanish, and the resulting estimator need not be consistent for the realized individual effect. This problem can be severe when \(\varepsilon_{it}(0)\) is large.

Our dual-modeling approach instead places the two potential outcomes on equal footing. Both \(Y_{it}(0)\) and \(Y_{it}(1)\) are represented by their systematic components under the factor structure. Using ((ref)) and ((ref)), we can write

Hence, even when \(\varepsilon_{it}(1)\) and \(\varepsilon_{it}(0)\) are individually large, their difference may be small. In that case, the systematic causal effect \(\tau_{it}^{*}\) can be close to the realized individual effect \(\tau_{it}\).

The condition $\varepsilon_{it}(1)-\varepsilon_{it}(0)=0$ is not imposed as an identifying assumption for \(\tau_{it}^{*}\). Rather, it is a special case under which the systematic causal effect coincides with the realized individual effect. In general, the object of interest in this paper is \(\tau_{it}^{*}\), the component of the unit-time treatment effect generated by the systematic parts of the two potential outcomes.

Table (ref) provides a timeline of the potential and observed outcomes. For the control group $(j>n_{0})$, the observed outcome $Y_{jt}$ equals the potential outcome $Y_{jt}(0)$ for all $t$. For the treatment group $(i\leq n_{0})$, the observed outcome $Y_{it}$ equals the potential outcome $Y_{it}(0)$ before the intervention $(t\leq T_{0})$ and equals the potential outcome $Y_{it}(1)$ after the intervention $(t>T_{0})$. The last three rows of Table (ref) give, respectively, the counterfactual, individual and systematic causal effects for the treated group. Our discussion of ((ref)) and ((ref)) demonstrates that we can consider the systematic causal effect ($\tau_{it}^{*}$) as the primary objective of interest.

Figure (ref) provides an example of the relationship among factors, realized individual trend before the intervention ($\lambda_{i}\left(0\right)^{\prime}\cdot f_{s}$, $s\leq T_{0}$) and after the intervention ($\lambda_{i}\left(1\right)^{\prime}\cdot f_{t}$, $t>T_{0}$), as well as the potential individual trend ($\lambda_{i}\left(0\right)^{\prime}\cdot f_{t}$, $t>T_{0}$). In the figure, $f_{t}$ is represented as a smooth function of time $t$, though smoothness is not required. The illustration depicts only a single factor for clarity. We have omitted the unit subscript $i$ from the factor loadings for notational simplicity; thus, $\lambda\left(d\right)$ in the figure corresponds to $\lambda_{i}\left(d\right)$ for the treated unit $i$, where $d=0,1$. To emphasize the conceptual framework, we have omitted the covariates in Table (ref) and Figure (ref).

In Section (ref), we show that the systematic causal effect $\tau_{it}^{*}$ in ((ref)) is identifiable because $\left\{ \lambda_{i}\left(d\right),f_{t},\beta\left(d\right)\right\} $, $d=0,1$, are all identifiable. Then a natural estimator for $\tau_{it}^{*}$ is given by

where the hatted variables are the corresponding estimators.

We will show that $\hat{\tau}_{it}^{*}$ is a consistent estimator for the systematic causal effect $\tau_{it}^{*}$, i.e., \[ \hat{\tau}_{it}^{*}-\tau_{it}^{*}=o_{p}\left(1\right), \] when the number of untreated units ($n-n_{0}$) and the number of periods before and after the treatment ($T_{0}$ and $T-T_{0}$) are large. Such a model-based approach allows us to identify the systematic component irrespective of the idiosyncratic errors. Existing causal inference methods, such as difference-in-differences, synthetic control, and matrix completion (e.g., Athey_2021,Bai_Ng_2021) focus on constructing the counterfactual $Y_{it}\left(0\right)$ from the control group. In contrast, our model-based method emphasizes the systematic component of the difference $Y_{it}\left(1\right)-Y_{it}\left(0\right)$, rather than attributing a one-sided idiosyncratic residual to the causal effect.

Relationship with Interactive Fixed Effects Models

The causal model that we propose is closely related to interactive fixed-effect approaches such as Gobillon_Magnac_2016 and Xu_2017, but differs in the role assigned to the factors. In those approaches, the factor component is primarily used as a latent control for unobserved confounding: common shocks enter the untreated potential outcome with unit-specific exposures, analogous to observed covariates. The treatment effect is then estimated as the difference between the realized treated outcome and an imputed untreated outcome.

In contrast, our framework allows the treated unit's exposure to the same common shocks to change after the intervention. Thus the factor loadings are not merely nuisance parameters used to control for unobserved heterogeneity; changes in these loadings are themselves part of the systematic causal effect. This distinction is especially important when the intervention changes how a treated unit responds to aggregate conditions, industry-wide shocks, or other latent forces.

The potential outcomes in the causal model of Gobillon_Magnac_2016 and Xu_2017 have the following representation

where the error term $\varepsilon_{it}$ is not indexed by the treatment status ($d=0,1$) and $\delta_{it}=Y_{it}\left(1\right)-Y_{it}\left(0\right)$ is defined as the individual causal effect. The estimator for this causal effect is

Plugging in the model for $Y_{it}\left(1\right)$ to obtain

Under appropriate assumptions such as those in Bai_2009, $\lambda_i'f_t-\hat{\lambda}_i'\hat f_t=o_p(1)$ and $\beta-\hat\beta=o_p(1)$. Therefore,

Consequently, under the modeling strategies of Gobillon_Magnac_2016 and Xu_2017, the idiosyncratic error $\varepsilon_{it}$ persists as an imputation error in the individual causal estimate. This component does not vanish for a fixed treated unit and time period, but it may be averaged out when the number of treated units, $n_0$, is large. This framework may be less suitable when $n_0$ is small, as in many applications in the synthetic control literature.

Similarly, Callaway_Karami_2023 propose to model the untreated potential outcomes as $ Y_{it}\left(0\right)=\theta_{t}+\xi_{i}+\lambda_{i}^{\prime}f_{t}+\varepsilon_{it}. $ This framework focuses on the average treatment effect. Their framework is helpful for the applications in the difference-in-differences literature but is not designed for the small $n_{0}$ case as in the synthetic control literature.

More importantly, Gobillon_Magnac_2016,Xu_2017,Callaway_Karami_2023 focus on modeling the untreated potential outcome $Y_{it}(0)$ and impose no restrictions on the causal effect $\delta_{it}$. They do not specify an explicit model for the treated potential outcome $Y_{it}(1)$. This flexibility comes at the cost of a nonvanishing imputation error in estimators of individual causal effects, as shown in (ref). In contrast, we explicitly model both $Y_{it}(0)$ and $Y_{it}(1)$, which restricts the causal effect $\tau_{it}$ through (ref). The resulting estimator (ref) targets the systematic unit-time causal effect and does not contain the one-sided idiosyncratic imputation component that appears in (ref), even when the number of treated units is small.

Recently, Brown_2023 proposed a framework for modeling potential outcomes across all treatment statuses using factor models, employing Pesaran_2006's Common Correlated Effects (CCE) method to identify average causal effects. Their approach differs from ours in two main ways. First, they concentrate on identifying average causal effects, which necessitates that the group size for treated units approaches infinity at the same rate as the group size for untreated units. In contrast, our framework can identify unit-time systematic effects even when the treated group is small, and average realized effects under additional averaging assumptions. While their method is designed for a large $n$ and small $T$ setup, we focus on a large $n$ and large $T$ configuration. Second, in their framework, the common component $\lambda_{i}^{\prime}f_{t}$ remains unaffected by treatment status, aligning with the setup used by Ferman_2021 in the context of the synthetic control method and Freyaldenhoven_2021 in the context of event-study design. In contrast, our approach permits this component to vary across treatment statuses.

Panel models with factor structures have been studied extensively; see, for example,Ahn_2001,Ahn_2013,Pesaran_2006,Bai_2009. Much of this literature focuses on estimating slope coefficients associated with observed covariates. Recent work has brought factor models into causal inference, mainly to estimate treatment effects averaged across treated units or post-treatment periods. This paper instead uses a dual factor structure for $Y_{it}(0)$ and $Y_{it}(1)$ to study systematic unit-time causal effects for a given unit $i$ and time period $t$. The resulting estimand has a direct structural interpretation and can be consistently estimated under standard large-panel conditions.

Relationship with Difference-in-Differences Using Interactive Fixed Effects

We next show that difference-in-differences, with or without interactive fixed effects, can be viewed as a special case of our setup. A standard difference-in-differences model with constant treatment effects and a common treatment timing is represented by the following two-way-fixed-effects (TWFE) panel regression model:

where $D_{it}$ is the treatment indicator defined in ((ref)). Adding the interactive fixed effects gives

In both specifications, $\rho$ represents the treatment effect.

The corresponding potential outcomes are given by

where the error term $\varepsilon_{it}$ is not indexed by the treatment status $d$. As a result, $\tau_{it}=\tau_{it}^{*}$. Define $g_{t}=\left[1,\theta_{t},f_{t}^{\prime}\right]^{\prime}$, $\lambda_{i}\left(0\right)=\left[\alpha_{i},1,\lambda_{i}^{\prime}\right]^{\prime}$, $\lambda_{i}\left(1\right)=\left[\alpha_{i}+\rho,1,\lambda_{i}^{\prime}\right]^{\prime}$, and then the potential outcomes can be represented as

which is a special case of causal model ((ref)) in which $\beta\left(d\right)=\beta,\;d=0,1$. Our representation of the causal effect ((ref)) or ((ref)) takes into account variations in $\lambda_{i}$ and $\beta$ across different treatment statuses to model the heterogeneous causal effects.

If one wants to use a TWFE model to learn about the heterogeneous causal effects, the regression model can be specified as

where the coefficient of $D_{it}$ is individual-dependent. The corresponding potential outcomes are given by

Define $g_{t}=\left[1,\theta_{t},f_{t}^{\prime}\right]^{\prime}$, $\lambda_{i}\left(0\right)=\left[\alpha_{i},1,\lambda_{i}^{\prime}\right]^{\prime}$, $\lambda_{i}\left(1\right)=\left[\alpha_{i}+\rho_{i},1,\lambda_{i}^{\prime}\right]^{\prime}$. Then the preceding potential-outcome equations can be represented as ((ref)), again a special case of our causal model ((ref)).

Relationship with Synthetic Control

To deliver the main idea, assume that the potential outcomes follow a factor model without covariates and the error term is not indexed by $d$ (so $\tau_{it}=\tau_{it}^{*}$),

Assume $i=1$ is treated with a policy intervention in period $T_{0}+1$, and the unaffected control units are $i=2,\ldots,n$. The synthetic control method constructs the counterfactual $Y_{1t}\left(0\right)$ as a weighted average of the observed outcomes for the control units: \[ \widehat{Y}_{1t}\left(0\right)=\sum_{i=2}^{n}\omega_{i}Y_{it},\quad t>T_{0},\;\omega_{i}\ge0,\;\sum_{i=2}^{n}\omega_{i}=1. \] Then $\widehat{Y}_{1t}\left(0\right)$ is equal to

The synthetic causal effect for $t>T_{0}$ is

Our model-based causal effect is given by \[ \tau_{1t}^{factor}\equiv\left[\lambda_{1}\left(1\right)-\lambda_{1}\left(0\right)\right]^{\prime}f_{t}=Y_{1t}\left(1\right)-Y_{1t}\left(0\right),\quad t>T_{0}. \] The difference between these two is \[ \tau_{1t}^{synth}-\tau_{1t}^{factor}=\left[\lambda_{1}\left(0\right)-\sum_{i=2}^{n}\omega_{i}\lambda_{i}\left(0\right)\right]^{\prime}f_{t}+\left[\varepsilon_{1t}-\sum_{i=2}^{n}\omega_{i}\varepsilon_{it}\right],\;t>T_{0}. \] The synthetic control chooses the weights such that the distance between $Y_{1t}$ and $\sum_{i=2}^{n}\omega_{i}Y_{it}$ is small for $t\leq T_{0}$. Note that for $t\leq T_{0}$,

In the case that the weights $\omega_{i}$ are chosen such that $ \lambda_{1}\left(0\right)\approx\sum_{i=2}^{n}\omega_{i}\lambda_{i}\left(0\right), $ we have \[ \tau_{1t}^{synth}-\tau_{1t}^{factor}\approx\varepsilon_{1t}-\sum_{i=2}^{n}\omega_{i}\varepsilon_{it},\quad t>T_{0}. \]

If we expect that the factors already capture most of the cross-sectional dependence, then the residual correlation between $\varepsilon_{1t}$ and $\sum_{i=2}^{n}\omega_i\varepsilon_{it}$ should be weak. In the special case where $\{\varepsilon_{it}\}$ is i.i.d.\ across $i$ and the weighted control residual is asymptotically negligible, i.e., $\sum_{i=2}^{n}\omega_i\varepsilon_{it}=o_p(1)$, we have $\varepsilon_{1t}-\sum_{i=2}^{n}\omega_i\varepsilon_{it} =\varepsilon_{1t}+o_p(1)=O_p(1)$. Therefore, $\tau_{1t}^{\mathrm{synth}}-\tau_{1t}^{\mathrm{factor}}=O_p(1)$. Hence, the estimator proposed in this paper and the synthetic-control estimator are generally not asymptotically equivalent for a fixed treated unit and time period. Their difference may become small under additional averaging over many post-treatment periods or many treated units. For a given unit-time treatment effect, however, the difference need not be negligible.

Hsiao_Ching_Wan_2012 adopt a similar method as synthetic control. They start with a factor model for the potential outcome $Y_{it}\left(0\right)$ and propose using a linear function of outcomes for the untreated units to estimate the counterfactual $Y_{1t}\left(0\right)$, $t>T_{0}$. Accordingly, the estimator for the individual causal effect is \[ Y_{1t}-\hat{Y}_{1t}\left(0\right),\;t>T_{0}. \] They use a simple regression method to estimate the optimal linear function. Under their assumptions, Hsiao_Ching_Wan_2012 show that the individual causal effect estimator is unbiased, and they also consider the corresponding post-treatment average estimator. In comparison, our theory provides large-sample inference for the unit-time systematic causal effect. Both our method and the approach of Hsiao_Ching_Wan_2012 do not require numerical optimization and are easy to implement. Li_Bell_2017 extend Hsiao_Ching_Wan_2012's framework and derive large sample theory for the average treatment effect under weaker conditions. They further propose using LASSO selection when the number of control units is large.

Recent research by Imbens_Viviano_2023 explicitly models $Y_{it}\left(0\right)$ as possessing a factor structure that includes both strong and weak factors, with the factors serving to control for unobserved confounders. They extend the Synthetic Difference-in-Differences framework developed by Arkhangelsky_2021 and achieve identification under slightly weaker assumptions, such as limited confoundedness over either units or time. However, while their model assumes constant causal effect, our focus is on heterogeneous and time-varying causal effects.

Li2020 and Chernozhukov_2025 have developed inferential theory for estimating the time average causal effect for the treated unit, $\bar{\tau}_{1}\equiv\frac{1}{T-T_{0}}\sum_{t=T_{0}+1}^{T}\tau_{1t}$, under the assumption that both $T_{0}$ and $T-T_{0}$ are large. While Li2020 assumes a fixed number of untreated units, Chernozhukov_2025 consider a large number of untreated units. In this paper, we focus on the unit-specific systematic causal effect in each post-treatment period ($\tau_{1t}^{*}$, $t>T_{0}$). Our framework assumes that $T_{0}$, $T-T_{0}$, and the number of untreated units ($n-n_{0}$) are all large.

Identification of the Causal Factor Model

To illustrate the main idea, we first consider the case without covariates. The factor model implies the systematic causal effect

This systematic causal effect $\tau_{it}^{*}$ is identifiable under the usual factor-model normalization. Although the factors and loadings are identified only up to a common rotation, the causal contrast $\left[\lambda_{i}\left(1\right)-\lambda_{i}\left(0\right)\right]^{\prime}f_{t}$ is invariant to that rotation. Thus, once the common factor space is recovered from the untreated units and the pre- and post-treatment loadings are expressed in the same normalized factor space, \(\tau_{it}^{*}\) is identified under large $n-n_{0}$, $T_{0}$, and $T-T_{0}$.

The identification strategy works for the cases when $n_{0}$ is either small or large. In particular, it works for the special case where $n_{0}=1$, similar to the synthetic control setup.

A similar strategy can be applied when covariates are included. Consider the data generating process \[ Y_{it}\left(d\right) = \lambda_{i}\left(d\right)^{\prime}f_{t} + X_{it}^{\prime}\beta\left(d\right) + \varepsilon_{it}\left(d\right), \quad d=0,1, \] where changes in \(\beta(d)\) capture systematic treatment-effect heterogeneity associated with covariates. The systematic causal effect is

Under the same factor normalization and appropriate rank conditions, this object is identifiable. The factors and loadings are identified only up to a common rotation, but the factor component \[ \left[ \lambda_{i}\left(1\right)-\lambda_{i}\left(0\right) \right]^{\prime}f_{t} \] is invariant to that rotation. The covariate component \[ X_{it}^{\prime} \left[ \beta\left(1\right)-\beta\left(0\right) \right] \] is identified from the corresponding pre- and post-treatment regressions, provided the usual rank conditions hold.

Discussion: Explicit Individual Fixed Effects

So far, for notational compactness, the individual fixed effects have not been written separately from the factor component. This is without loss of generality. If one component of \(f_t\) is identically equal to one, then the factor term \(\lambda_i'f_t\) implicitly includes an individual-specific intercept. Equivalently, writing \[ \widetilde f_t = \left(1,f_t'\right)' \quad\text{and}\quad \widetilde\lambda_i(d) = \left(a_i(d),\lambda_i(d)'\right)', \] the term $a_i(d)+\lambda_i(d)'f_t$ can be represented as $ \widetilde\lambda_i(d)'\widetilde f_t$. Thus, an individual fixed effect can always be incorporated into the factor structure by including a constant factor.

Although this representation is convenient, it is often more transparent to write the individual fixed effects explicitly. We therefore consider the equivalent specification

Here \(a_i(d)\) is the individual fixed effect under treatment state \(d\), while $f_t$ denotes the remaining common factors. The corresponding systematic causal effect is

This explicit-intercept notation will be useful below, especially when the treatment is allowed to shift the common factor process by a constant. In that case, part of the factor shift can be absorbed into a unit-specific intercept. Writing \(a_i(0)\) and \(a_i(1)\) separately therefore clarifies the distinction between a treatment-induced change in the individual fixed effect and a constant shift in the factor component. Except in such cases, we continue to use the more compact notation in which the individual fixed effects are not written separately.

Extension to the Case with Potential Factors

In some settings the policy intervention may alter not only treated units' exposure to common shocks, through factor loadings, but also the common-shock process itself. This arises naturally when the intervention is large enough to change equilibrium conditions faced by the treated group, for example through market clearing prices, entry and exit, institutional constraints, expectations, or other spillovers that are shared across treated units. In such cases, modeling a common factor process that is invariant to treatment may be too restrictive, and it is appropriate to allow treated outcomes to be driven by a different post-treatment factor process, denoted \(f_t(1)\).

Identification of a flexible post-treatment factor process requires sufficient treated cross-sectional variation, which motivates our large-\(n_0\) analysis. When the treated group is small, we consider restricted perturbations of \(f_t(1)\) that restore tractable identification while still permitting the intervention to affect both the factor process and factor loadings.

Potential Factors Framework with a Large Number of Treated Units

Assume \(n_0/n\rightarrow c\in(0,1)\), with \(n_0\), \(n\), the number of pre-treatment periods, and the number of post-treatment periods all large. In this case, the post-treatment treated sample contains enough cross-sectional and time-series variation to identify a flexible factor process for the treated group.

Before the intervention, the same common factor process drives both treated and untreated units. After the intervention, the untreated units continue to be driven by \(f_t(0)\), while the treated units may be driven by a different factor process \(f_t(1)\). Thus, for treated units in the post-treatment period, \(f_t(0)\) can be interpreted as the counterfactual factor process that would have prevailed without the intervention, whereas \(f_t(1)\) is the realized factor process under treatment.

The potential outcome model is \[ Y_{it}(d)=\lambda_i(d)'f_t(d)+\varepsilon_{it}(d),\qquad d=0,1. \] Observed outcomes satisfy $Y_{it}=Y_{it}(0)$ for controls $(i>n_0)$ and, for treated units $(i\le n_0)$, $Y_{it}=Y_{it}(0)$ before treatment and $Y_{it}=Y_{it}(1)$ after treatment. The systematic causal effect is

This representation allows us to evaluate the source of the causal effects due to structural breaks in both factor loadings and factors.

The systematic causal effect \(\tau_{it}^{*}\) is identifiable because the post-treatment treated common component \(\lambda_i(1)'f_t(1)\) and the counterfactual untreated common component \(\lambda_i(0)'f_t(0)\) are identified. A simple identification strategy is given as follows.

The estimator of the systematic causal effect is given by

The above procedure can be extended to include regressors. With regressors, the systematic causal effect becomes \[ \tau_{it}^{*} =\lambda_i(1)'f_t(1)-\lambda_i(0)'f_t(0) +X_{it}'[\beta(1)-\beta(0)], \qquad t>T_0,\ i\le n_0 . \] The corresponding estimator replaces the unknown quantities by their sample analogs. We show that $\hat{\tau}_{it}^{*}$ is a consistent estimator of the systematic causal effect $\tau_{it}^{*}$ and derive its asymptotic standard error in Proposition (ref) below.

Potential Factors Framework with a Small Number of Treated Units

The identification strategy above relies on estimating $f_t(1)$ from the post-treatment treated sample $\{Y_{it}: i\le n_0,\ t>T_0\}$. When $n_0$ is small, and especially when $n_0=1$, principal component analysis using treated post-treatment outcomes is not feasible. A parsimonious alternative is to restrict the effect of the intervention on the factor process.

Suppose that, for treated units in the post-treatment period,

where $\Delta$ is an $r\times 1$ constant vector. If the outcome model contains a unit-specific intercept, this constant factor shift is absorbed into the post-treatment intercept.\footnote{More generally, one may allow \[ f_t(1)=A f_t(0)+\Delta, \] where $A$ is a constant $r\times r$ matrix. This generalization does not affect the results below, because \[ \lambda_i(1)'f_t(1) = \lambda_i(1)'A f_t(0)+\lambda_i(1)'\Delta = \tilde\lambda_i(1)'f_t(0)+\lambda_i(1)'\Delta, \qquad \tilde\lambda_i(1):=A'\lambda_i(1). \] The linear transformation $A$ is therefore absorbed into the post-treatment factor loadings, while the constant shift $\lambda_i(1)'\Delta$ is absorbed into the post-treatment intercept. There is no need to separately identify $A$ and $\Delta$.} Indeed, \[ a_i(1)+\lambda_i(1)'f_t(1) = a_i(1)+\lambda_i(1)'f_t(0)+\lambda_i(1)'\Delta = \tilde a_i(1)+\lambda_i(1)'f_t(0), \] where $a_i(1)$ is the post-treatment intercept, see ((ref)), and \[ \tilde a_i(1):=a_i(1)+\lambda_i(1)'\Delta. \] Thus, $\Delta$ itself need not be separately identified. Its contribution to the systematic causal effect is summarized by the total intercept shift \[ \kappa_i := \tilde a_i(1)-a_i(0) = a_i(1)-a_i(0)+\lambda_i(1)'\Delta . \] The corresponding systematic causal effect is

This has the same form as the baseline model once unit-specific intercepts are included. Hence, the constant-shift specification is covered by the baseline estimation and inference results. Proposition (ref) below therefore applies after augmenting the unit-level regression with a constant term.

To illustrate the estimation of $\tau_{it}^{*,\Delta}$, consider the case with no additional covariates but with unit-specific intercepts. Estimate $f_t(0)$ from the control units and denote the resulting estimate by $\hat f_t(0)$. For each treated unit $i\le n_0$, estimate $(a_i(0),\lambda_i(0))$ by regressing $Y_{it}$ on $(1,\hat f_t(0))$ over the pre-treatment period $t\leq T_0$. Similarly, estimate $(\tilde a_i(1),\lambda_i(1))$ by regressing $Y_{it}$ on $(1,\hat f_t(0))$ over the post-treatment period $t>T_0$.

Let \[ \hat\kappa_i:=\hat {\tilde a}_i(1)-\hat a_i(0), \] where $\hat \kappa_i$ captures the total intercept change, including both the structural intercept change and the constant factor shift.\footnote{For notational simplicity, we may simply denote $\tilde a_i(1)$ by $a_i(1)$ since $\Delta$ is not separately identifiable unless the number of treated units is large.} Define

This estimator is the intercept-augmented version of the baseline estimator in Proposition (ref). With additional covariates, the same expression includes $X_{it}'[\hat\beta(1)-\hat\beta(0)]$, provided that the common covariate coefficients are estimated together with unit-specific intercepts.

Relationship with Synthetic Interventions

Extending the baseline synthetic control model, Agarwal_2024 introduce a synthetic interventions framework designed to address multiple treatments. Their model for potential outcomes under treatment status \(d\in\{0,1,2,\ldots,D\}\), with \(D\geq 1\), employs a low-rank tensor factor model represented as \[ Y_{it}(d) = \sum_{l=1}^{r}u_{tl}v_{il}\lambda_{dl} + \varepsilon_{it}(d). \] While their focus is on estimating average treatment effects, they impose a restriction by keeping the factor loadings \(v_{il}\) unaffected by treatment status. Their model incorporates two types of factors: time-varying factors \(u_{tl}\), which are not affected by treatment status, and treatment-specific factors \(\lambda_{dl}\), which are time-invariant.

In contrast, our potential factor model allows for greater flexibility by permitting both the common factors and the factor loadings to vary across treatment status. Specifically, if we consider the \(l\)-th potential factor \(f_{lt}(d)\) in our setup, we can express the synthetic interventions restriction as $ f_{lt}(d)=u_{tl}\lambda_{dl}. $ Under this restriction, their common-factor strategy can be interpreted as a special case of our model when \(D=1\).

Estimation and Inference

The Intervention Does Not Affect the Factors

Consider ((ref)) as the estimator for the unit-specific systematic causal effect in ((ref)): \[ \hat{\tau}_{it}^{*}=\left[\hat{\lambda}_{i}\left(1\right)-\hat{\lambda}_{i}\left(0\right)\right]^{\prime}\hat{f}_{t}+X_{it}^{\prime}\left[\hat{\beta}\left(1\right)-\hat{\beta}\left(0\right)\right],\;t>T_{0},\;i\leq n_{0}. \] The factor estimate $\hat{f}_{t}$ is obtained using panel regression with interactive fixed effects (see, for example, Bai_2009) using the control units. Then $\hat{\lambda}_{i}\left(0\right)$ and $\hat{\beta}\left(0\right)$ are obtained from a regression of $Y_{it}$ on $\hat{f}_{t}$ and $X_{it}$ for $t\leq T_{0}$ and $i\leq n_{0}$. $\hat{\lambda}_{i}\left(1\right)$ and $\hat{\beta}\left(1\right)$ are obtained from another regression of $Y_{it}$ on $\hat{f}_{t}$ and $X_{it}$ for $t>T_{0}$ and $i\leq n_{0}$. Here we assume $\beta(0)$ and $\beta(1)$ are common across $i$, and only the factor loadings vary with $i$. So $\hat \lambda_i(0)$ and $\hat \beta(0)$ are estimated by interacting individual dummies with $\hat f_t$ in a pooled regression to impose common slope coefficients for the covariates. $\hat \lambda_i(1)$ and $\hat \beta(1)$ are obtained similarly. If the slope coefficients are heterogeneous, simple time series regressions can be applied for each $i$ to obtain $\hat \lambda_i(0)$ and $\hat \beta_i(0)$, likewise for $\hat \lambda_i(1)$ and $\hat \beta_i(1)$. The large sample theory is summarized in Proposition (ref).

Thus asymptotic normality holds whether the number of treated units $n_0$ is fixed or diverges. When $n_0\to\infty$ and $f_t\neq0$, the result imposes no additional relative growth restriction between $n_0$ and $n_1$ beyond the maintained assumptions. When $n_0\to\infty$, the knife-edge case $f_t=0$ requires the additional rate condition (ref); see Remark (ref) below. The result does not require any proportionality restriction between $T_d$ and $T$; in particular, it does not require $T_d/T\to c_d\in(0,1)$.

The variance estimator $\widehat V_{it}$ is given in the Appendix. The proof of Proposition (ref) is provided in the Online Appendix.

As discussed previously, the same result continues to hold when the outcome model includes unit-specific intercepts. In this case, the common factors can be estimated from the control units after removing unit-specific time averages from the outcomes and covariates, as in Section 8 of Bai_2009. The normalization that the factors have zero time mean separates the unit-specific intercepts from the common factors. After estimating the factors from the demeaned control-unit panel, we recover the treated-unit coefficients by separately regressing the treated-unit outcome on a constant, the estimated factors, and the covariates over the pre-intervention and post-intervention periods. The feasible treated effect is then defined as the sample analogue of (ref), with the unknown factors and coefficients replaced by their estimates. With this modification, Proposition (ref) remains valid.

The intercept-augmented formulation also covers the constant-shift specification in (ref). When unit-specific intercepts are included, a time-invariant shift in the factor process is absorbed into the post-treatment intercept, and Proposition (ref) continues to apply.

The Intervention Affects the Factors for the Treated Group, Large $n_0$

Consider ((ref)) as the estimator for the unit-specific systematic causal effect ((ref)): \[ \hat{\tau}_{it}^{*}=\hat{\lambda}_{i}\left(1\right)^{\prime}\hat{f}_{t}\left(1\right)-\hat{\lambda}_{i}\left(0\right)^{\prime}\hat{f}_{t}\left(0\right), \qquad \;t>T_{0},\;i\leq n_{0}. \] The factor estimate $\hat{f}_{t}\left(0\right)$ is obtained using the first $r$ leading principal components based on the control units. Then $\hat{\lambda}_{i}\left(0\right)$ is obtained from a regression of $Y_{it}$ on $\hat{f}_{t}(0)$ for $t\leq T_{0}$ and $i\leq n_{0}$. The product $\hat{\lambda}_{i}\left(1\right)^{\prime}\hat{f}_{t}\left(1\right)$ is obtained as the common component estimator from principal component analysis of $Y_{it}$ for $t>T_{0}$ and $i\leq n_{0}$. We have the following proposition.

The variance estimator $\hat V_{it}$ and the proof are given in the online appendix.

The Intervention Affects the Factors for the Treated Group, Small $n_0$

When the number of treated units, $n_0$, is small, a fully flexible post-treatment factor process $f_t(1)$ cannot be reliably estimated from the treated post-treatment sample. Under the constant-shift specification (ref), however, the term $\lambda_i(1)'\Delta$ is absorbed into the post-treatment unit-specific intercept. Thus the systematic causal effect can be written as

Estimate $\hat f_t(0)$ using the control units as in Proposition (ref). For each treated unit $i\le n_0$, estimate the pre- and post-treatment regressions of $Y_{it}$ on $(1,\hat f_t(0),X_{it})$, allowing the intercept and factor loadings to vary by unit. Let \[ \hat\kappa_i=\hat a_i(1)-\hat a_i(0),\qquad \hat\alpha_i=\hat\lambda_i(1)-\hat\lambda_i(0). \] The estimator is

This is the intercept-augmented version of the estimator in Proposition (ref). Therefore no separate inferential theory is needed for the constant-shift case. Proposition (ref) is applicable to this case.

Monte Carlo Simulations

In this section, we conduct Monte Carlo simulations to evaluate the finite sample performance of Propositions 1 and 2. We begin with Proposition (ref), focusing on the case with a single treated unit ($n_{0}=1$), specifically the first unit in our sample. Let $n_1=n-n_0$ denote the number of untreated units. For given sample sizes of $n_{1}$, $T_{0}$, and $T$, we simulate the potential outcomes according to a factor model with two factors. To simplify the illustration, we do not include covariates in the simulation. We assume that the idiosyncratic errors are not indexed by treatment status, so the systematic causal effect is equivalent to the individual causal effect ($\tau_{it}^{*}=\tau_{it}$). We then estimate the causal effect for the treated unit using the estimator in equation ((ref)). We construct the 95% confidence intervals according to $\left[\hat{\tau}_{1t}\pm1.96\cdot SE\left(\hat{\tau}_{1t}\right)\right]$, where the formula for $SE\left(\hat{\tau}_{1t}\right)=\sqrt{\widehat{var}\left(\hat{\tau}_{1t}\right)}$ is provided in the Appendix. Finally, we report the empirical coverage rates for the true causal effect $\tau_{1t}$ for $t=T_{0}+1,T_{0}+1+m,T$, under various combinations of $\left(n,T_{0},T\right)$. We define $m=\left[\frac{T-T_{0}}{2}\right]$ as the nearest integer to $\frac{T-T_{0}}{2}$ so that $T_{0}+1+m$ is positioned in the middle of the treated periods. The data are simulated according to the following factor model, \[ Y_{it}\left(d\right)=\lambda_{i}^{\prime}\left(d\right)f_{t}+\varepsilon_{it}, \; d=0,1. \] We consider three data generating processes (DGPs):

For DGPs 1-3, the second factor is simulated as $f_{2t}=0.8\cdot f_{2,t-1}+e_{t}$, where $e_{t}$ is i.i.d.\ $N\left(0,1\right)$.

We set the number of Monte Carlo repetitions to 5000. In Table (ref), we report the coverage rates of the 95% confidence interval for the three DGPs. The numbers in parentheses represent coverage rates for $\tau_{1,T_{0}+1},\tau_{1,T_{0}+1+m},\tau_{1,T}$ respectively. We set the treatment date $T_{0}+1=30$ when $T=50$, and $T_{0}+1=50$ when $T=100$. For all DGPs and sample sizes, the coverage rates are reasonably close to the nominal rate, with some undercoverage in the smaller-sample designs.

Next, we apply the same procedure to examine Proposition (ref), varying the group sizes for treated units ($n_{0}$) and untreated units ($n_{1}$). For given sample sizes of $n_{0}$, $n_{1}$, $T_{0}$, $T$, we simulate potential outcomes according to the factor model with two factors. Again, we assume that the idiosyncratic errors are not indexed by treatment status, so the systematic causal effect is the same as the individual causal effect ($\tau_{it}^{*}=\tau_{it}$). We report estimates only for the first treated unit ($i=1$). The 95% confidence intervals are constructed as $\left[\hat{\tau}_{1t}\pm1.96\cdot SE\left(\hat{\tau}_{1t}\right)\right]$, where the formula for $SE\left(\hat{\tau}_{1t}\right)=\sqrt{\widehat{var}\left(\hat{\tau}_{1t}\right)}$ is provided in the Appendix. We then report the empirical coverage rates for the true causal effect $\tau_{1t}$ for $t=T_{0}+1,T_{0}+1+m,T$, under different combinations of $\left(n_{0},n_{1},T_{0},T\right)$. We specify $m=\left[\frac{T-T_{0}}{2}\right]$ as the nearest integer to $\frac{T-T_{0}}{2}$. The data are simulated according to the following factor model with potential factors, \[ Y_{it}\left(d\right)=\lambda_{i}^{\prime}\left(d\right)f_{t}\left(d\right)+\varepsilon_{it},\;d=0,1. \] We consider three additional DGPs:

For DGPs 4-6, the second potential factors are simulated as $f_{2t}\left(0\right)=0.8\cdot f_{2,t-1}\left(0\right)+e_{1t}$ with $e_{1t}$ being i.i.d.\ $N\left(0,1\right)$, and $f_{2t}\left(1\right)=0.9\cdot f_{2,t-1}\left(1\right)+e_{2t}$ with $e_{2t}$ being i.i.d.\ $N\left(0,1\right)$.

The number of Monte Carlo repetitions is again set to 5000. In Table (ref), we report the coverage rates of the 95% confidence interval for three choices of the number of treated units ($n_{0}$): 20, 40, 100. The numbers in parentheses in the tables represent coverage rates for $\tau_{1,T_{0}+1},\tau_{1,T_{0}+1+m},\tau_{1,T}$ respectively. We set the treatment date $T_{0}+1=30$ when $T=50$, and $T_{0}+1=50$ when $T=100$. For all DGPs and sample sizes, the coverage rates of the confidence intervals remain close to the nominal rate of 95%.

We next examine the constant-shift factor specification for the case of a small number of treated units. We focus on the case with a single treated unit ($n_{0}=1$), which is specified as the first unit in the sample. The DGPs 7-9 extend DGPs 1-3 under Proposition (ref) to the constant-shift potential-factor case. The data are simulated according to the following factor model, \[ Y_{it}\left(d\right)=\lambda_{i}^{\prime}\left(d\right)f_{t}\left(d\right)+\varepsilon_{it},\;d=0,1, \] where

with $\Delta$ being a constant $r\times1$ vector. We consider three data generating processes (DGPs):

The second factor is simulated as $f_{2t}\left(0\right)=0.8\cdot f_{2,t-1}\left(0\right)+e_{t}$, where $e_{t}$ is i.i.d.\ $N\left(0,1\right)$. The potential factor $f_{t}\left(1\right)$ is given by ((ref)). Across Monte Carlo simulations, elements of $\Delta$ are random draws from $N\left(0,1\right)$.

We set the number of Monte Carlo repetitions to 5000. In Table (ref), we report the coverage rates of the 95% confidence interval for the three DGPs 7-9. The numbers in parentheses represent coverage rates for $\tau_{1,T_{0}+1},\tau_{1,T_{0}+1+m},\tau_{1,T}$ respectively, where $m=\left[\frac{T-T_{0}}{2}\right]$. We set the treatment date $T_{0}+1=30$ when $T=50$, and $T_{0}+1=50$ when $T=100$. For all DGPs and sample sizes, the coverage rates of the confidence intervals are all close to the nominal rate of 95%.

Two Empirical Applications

An Application to California's Tobacco-Control Program

Using data from Abadie_Diamond_Hainmeuller_2010 on per capita cigarette sales across 39 U.S.\ states, we construct a counterfactual California using factor models and compare it with the synthetic California. We find that the two approaches yield close results. Let $Y_C$ be the $n\times T$ data matrix for the control states ($n=38$). Let $S_{C}$ denote the $n\times n$ sample covariance matrix for $Y_C$. Let $\mu_{j}$ be the $j$-th largest eigenvalue of $S_{C}$. Let $m=\min\left\{ n,T\right\} $. Figure (ref) provides the scree plot for the control states, which plots $\frac{\mu_{j}}{\sum_{i=1}^{m}\mu_{i}}$ against $j=1,2,\ldots,10$ (i.e., the ratio of the first ten largest eigenvalues of the covariance matrix and the sum of all eigenvalues). Figure (ref) plots Ahn_Horenstein_2013's Eigenvalue Ratio (ER) and Growth Ratio (GR) criterion functions, where \[ ER\left(j\right)=\frac{\mu_{j}}{\mu_{j+1}},\;GR\left(j\right)=\frac{\log\left(\sum_{i=j}^{m}\mu_{i}/\sum_{s=j+1}^{m}\mu_{s}\right)}{\log\left(\sum_{s=j+1}^{m}\mu_{s}/\sum_{k=j+2}^{m}\mu_{k}\right)}. \] The number of factors can be consistently estimated by \[ \hat{r}^{ER}=\underset{\left\{ 1\leq j\leq r_{max}\right\} }{\mathrm{argmax}}ER\left(j\right),\;\hat{r}^{GR}=\underset{\left\{ 1\leq j\leq r_{max}\right\} }{\mathrm{argmax}}GR\left(j\right). \]

Both the $ER$ and $GR$ criteria select a single factor. The number of factors can also be chosen using the information criteria of Bai_Ng_2002, which suggest more than one factor in this application. As a robustness check, we therefore estimate the model using both one factor and two factors.

Our analysis proceeds with the following steps.

For a robustness check, we estimate the model using either one or two factors. The t-statistic for testing the null hypothesis $\kappa_{CA}=a_{CA}\left(1\right)-a_{CA}\left(0\right)=0$ is $t=1.38$ for the model with a single factor and $t=0.10$ for the model with two factors. This provides little evidence of a post-treatment intercept shift, including any constant shift in the factor process. Our estimator $\hat{\tau}_{CA,t}$ provides an estimator for the causal effect that is robust to such post-treatment intercept shifts.

In Figure (ref), we provide an illustrative comparison of the observed California series with estimated untreated paths obtained from factor models with one or two factors and from the synthetic-control method. The vertical line marks 1988, the year in which Proposition 99 was passed in California. The treatment period runs from $T_0+1=1989$ to $T=2000$. For the factor-model estimates, the predicted systematic untreated component is $\widehat m_{CA,t}(0)=\hat a_{CA}(0)+\hat\lambda_{CA}(0)'\hat f_t$. For demonstration, the path plotted in the figure adds the post-treatment treated residual, so that $\widehat Y_{CA,t}(0)=\widehat m_{CA,t}(0)+\hat\varepsilon_{CA,t}$, where $\hat\varepsilon_{CA,t}$ is obtained in Step 2. Under the assumption that the idiosyncratic residual is not affected by treatment, this object estimates the untreated potential outcome $Y_{CA,t}(0)$. Unlike the synthetic-control comparison, however, our Step 3 causal-effect estimator is constructed directly and does not require first constructing this plotted counterfactual path. In the figure legend, “1factorCA” denotes the one-factor estimate, whereas “2factorCA” denotes the two-factor estimate.

Figure (ref) presents a comparison between the synthetic control approach and the one- or two-factor causal estimates computed in Step 3. Overall, the two methods produce comparable results.

We further investigate whether the policy intervention indeed induced a structural break by regressing California's observed outcome on the single factor using the whole sample. The Quandt likelihood ratio test for a structural break at an unknown date, using 15 percent trimming, rejects parameter stability with a p-value below 0.001. The maximum F-statistic is attained in 1984. The Chow test for a structural break at the 1989 intervention date also rejects stability, yielding an F-statistic of 16.84 with a p-value below 0.001. These tests provide evidence of instability in the treated-unit factor regression, including instability at the intervention date. We interpret these tests as diagnostics supporting the relevance of allowing treated factor loadings to change over time.

Applying the results from Section (ref), we also construct the 95% confidence interval of our causal estimates based on the factor models. Using a single factor, Figure (ref) reproduces Figure (ref) with the shaded region being the 95% confidence interval around the causal estimates. The confidence intervals generally cover the synthetic-control estimates and indicate that the factor-model causal estimates are statistically different from zero for the post-treatment periods shown. Figure (ref) reports similar results using 2 factors.

An Application to German Reunification

In this section, we compare the causal estimates from the synthetic control method and causal factor models using Abadie_Diamond_Hainmeuller_2015's data on per capita GDP for 17 countries. The objective is to evaluate the causal impact of German reunification on Germany's per capita GDP. The synthetic control method uses 16 countries to construct the synthetic West Germany. The causal factor model uses the same 16 countries to construct the counterfactual West Germany. Based on the covariance matrix of all countries excluding West Germany, Ahn_Horenstein_2013's Eigenvalue Ratio and Growth Ratio criteria point to a single factor.

In Figure (ref), time series of per capita GDP for all 17 countries (1969--2003) demonstrate strong comovement but not necessarily parallel trends. The vertical line represents the year 1990 and the treatment periods are from $T_{0}+1=1991$ to $T=2003$.

For a robustness check, we estimate the causal factor model with one or two factors. In Figure (ref), we compare the actual data with counterfactual paths for West Germany constructed using factor models with one or two factors and using synthetic control. The factor causal effects remain similar to the synthetic control estimates as shown by Figures (ref) and (ref).

We then regress West Germany's observed outcome on the single factor using the full sample. The Quandt likelihood ratio test for a structural break at an unknown date, using 15 percent trimming, rejects parameter stability with a p-value below 0.001. The maximum F-statistic is attained in 1993. The Chow test for a structural break at the 1991 treatment date also rejects stability, producing an F-statistic of 634.5 with a p-value below 0.001.

Figures (ref) and (ref) present the 95% confidence intervals of the causal effects using one or two factors. These intervals indicate that our causal estimates are statistically different from zero for most of the post-treatment periods shown. The path of our estimates aligns closely with the synthetic control estimates prior to 2000, beyond which slight deviations emerge. In the 2-factor specification, the 95% confidence intervals generally cover the synthetic control estimates.

Finally, we investigate the possibility of a post-treatment intercept shift for West Germany. The t-statistic for testing the null hypothesis $\kappa_{WG}=a_{WG}\left(1\right)-a_{WG}\left(0\right)=0$ is $t=11.81$ for the specification with a single factor and $t=6.23$ for the specification with two factors. This suggests a statistically significant post-treatment intercept shift, which may reflect either a direct change in the unit-specific intercept or a constant shift in the factor process.

Conclusion

This paper develops a factor-model framework for causal inference in panel data that links systematic treatment effects to changes in the factor representation of potential outcomes. By modeling both potential outcomes within a factor structure, the approach separates systematic effects from unit-time idiosyncratic noise, provides interpretable decompositions, and delivers feasible inference without imposing the standard parallel-trends restriction.

We consider two broad environments. In the first, the policy intervention does not alter the common-shock process, so the same factors drive both treated and control outcomes. Treatment effects arise through structural changes in treated units' factor loadings and, possibly, slope coefficients. In this benchmark case, the common factors can be estimated from the control group and treated parameters are identified from time-series variation. The method can therefore be applied even when the treated group is small, including the single-treated-unit setting.

In the second environment, the policy intervention may also affect the common-shock process. Allowing both potential factors and potential factor loadings provides a flexible representation of post-treatment dynamics. When the treated cross section is large, the framework can accommodate an unrestricted post-treatment factor process and estimate treated-specific post-treatment factors directly. When the treated group is small, a fully flexible post-treatment factor process is generally not separately identifiable; we therefore propose a restricted post-treatment perturbation that preserves the potential-factor interpretation while restoring tractable estimation and inference.

Monte Carlo experiments indicate that the proposed confidence intervals attain coverage close to nominal levels across a range of designs. In applications to California's Proposition 99 and German reunification, the causal factor model produces counterfactual paths and treatment-effect estimates broadly consistent with synthetic control, while offering additional structure for formal inference and interpretable diagnostics, including evidence on structural breaks in treated loadings. Overall, the framework complements synthetic control and difference-in-differences methods by providing a unified factor-based representation of potential outcomes and inference for systematic effects in panels with pervasive comovement.