Propensity Score–Based Methods versus MTE-Based Methods in Causal Inference: Identification, Estimation, and Application*

Abstract

Since the seminal introduction of the propensity score by Rosenbaum and Rubin, propensity-score-based (PS-based) methods have been widely used for drawing causal inferences in the behavioral and social sciences. However, the propensity score approach depends on the ignorability assumption: there are no unobserved confounders once observed covariates are taken into account. For situations where this assumption may be violated, Heckman and his associates have recently developed a novel approach based on marginal treatment effects (MTE). In this paper, we (1) explicate consequences for PS-based methods when aspects of the ignorability assumption are violated; (2) compare PS-based methods and MTE-based methods by making a close examination of their identification assumptions and estimation performances; (3) apply these two approaches in estimating the economic return to college using data from NLSY 1979 and discuss their discrepancies in results. When there is a sorting gain but no systematic baseline difference between treated and untreated units given observed covariates, PS-based methods can identify the treatment effect of the treated (TT). The MTE approach performs best when there is a valid and strong instrumental variable (IV). In addition, this paper introduces the “smoothing-difference PS-based method,” which enables us to uncover heterogeneity across people of different propensity scores in both counterfactual outcomes and treatment effects.

1. Introduction

Since the seminal introduction of the propensity score by Rosenbaum and Rubin (1983), propensity-score-based (PS-based) methods, including matching, stratification, and weighting, have become a mainstay strategy for drawing causal inferences in the behavioral and social sciences. By reducing a large array of confounding variables to a univariate measure that preserves all the relevant information of potential confounders, the propensity score provides a more effective tool than covariate adjustment does for eliminating confounder bias (Rosenbaum and Rubin 1984). Furthermore, social science researchers have recently utilized propensity score methods to study heterogeneous treatment effects across individuals with different propensities of being treated. For example, Brand and Xie (2010) recently found that those students who are least likely to obtain a college education benefit most from college.

Like all other attempts to resolve confounding problems in causal inference, the propensity score approach is by no means a panacea. The primary limitation of this approach lies in the impossibility of capturing unobserved individual and contextual confounders. In fact, the whole justification of propensity-score-based methods hinges on the common “ignorability assumption”: through control of a given set of relevant observed covariates, treatment status is assumed to be independent of potential outcomes. This assumption is unverifiable, indeed unlikely to be true, in practice. For instance, economic theory predicts that attainment of college education may be selective because it may attract young persons who are motivated by economic gain from college education (Willis and Rosen 1979; Carneiro, Heckman, and Vytlacil 2011). This example illustrates the effect of “sorting on gain” that may not be captured by observed covariates such as family background and cognitive abilities.

Despite the aforementioned limitation, PS-based methods are still widely used by empirical researchers in a variety of disciplines. Not only is the propensity-score approach simple and straightforward, but methods of addressing unobserved selection would require either additional data unavailable to the researcher or strong assumptions implausible in a research setting. However, the performance of PS-based methods is questionable when the ignorability assumption breaks down. Although sensitivity analysis is usually employed to assess the plausibility of findings (Harding 2003; DiPrete and Gangl 2004), systematic investigation is also needed to directly examine the consequences for PS-based methods when ignorability is violated. A related discussion can be found in Heckman and Navarro-Lozano (2004), who compared matching, instrumental variables (IVs) and control functions in the estimation of economic choice models. Blundell, Dearden, and Sianesi (2005) also compared least squares, matching, control functions and IV from a methodological point of view within a common framework. More recently, Shadish, Clark, and Steiner (2008) explored the performances of OLS adjustment and propensity score adjustment with different sets of predictors in an experimental setting. Inspired by these studies, this paper aims to provide another examination of PS-based methods in a variety of plausible situations.

Our paper goes beyond PS-based methods by evaluating a structural approach, developed by James Heckman and his associates, for situations in which the ignorability assumption is violated (Heckman and Vytlacil 1999, 2001, 2005; Heckman, Urzua, and Vytlacil 2006a, 2006b). Different from traditional IV-based methods, this approach is based on the building block of marginal treatment effect (MTE), which enables us to derive various parameters of interest within a single framework. However, MTE-based methods have not been widely used in empirical research (for a few exceptions, see Carneiro, Heckman, and Vytlacil 2011; Moffitt 2008; Tsai and Xie 2011), partly due to its complexity and demands on data. In fact, the aforementioned literature suggests that the utility of MTE hinges heavily on the validity of the exclusion restriction as well as the strength of instrumental variables.¹ The properties of this approach are not yet well known when either the exclusion restriction is violated or the instrumental variable is too “weak.”

In this paper, we evaluate and compare the widely adopted PS-based methods and the less popular MTE-based approach, as follows. In Section 2, we revisit population heterogeneity and two types of selection bias in causal inference, presenting propensity-score-based methods and their implications in settings where the ignorability assumption is partially or completely violated. In particular, we propose a PS-based method by modeling counterfactual outcomes as nonparametric functions of the propensity score, which we call the “smoothing-difference method.” In Section 3, we introduce the MTE-based approach as a remedy for situations where the ignorability assumption may be violated. In Section 4, we compare PS-based methods and MTE-based methods by examining their identification assumptions and estimation performances. We use numerical simulation to explore (1) the relative efficiency of these two approaches when both ignorability and the exclusion restriction hold true, and (2) potential biases from using methods based on the two approaches when neither ignorability nor the exclusion restriction is guaranteed. In Section 5, we illustrate both methods in analyzing the economic return to college education using a sample of white males from the National Longitudinal Survey of Youth of 1979 (NLSY), and discuss their discrepancies in results. In Section 6 we conclude.

2. Population Heterogeneity, Ignorability, and Propensity-Score-Based Methods

Population sciences, including economics, demography, epidemiology, psychology, and sociology, treat individual-level variation as a part of reality subject to scientific inquiry, rather than a mere nuisance or measurement error (Angrist and Kruger 1999; Ansari and Kamel 2000; Bauer and Curran 2003; Greenland and Poole 1988; Heckman 2001, 2005; Heckman and Robb 1985; Heckman and Vytlacil 2005; Lubke and Muthen 2005; Manski 2007; Moffitt 1996; Rothman and Greenland 1998; Winship and Morgan 1999; Xie 2007). The recognition of inherent individual-level heterogeneity has important consequences for research designs in the social sciences. Because individuals differ from one another and differ in their responses to a common treatment, results can vary widely depending on population composition.

The large methodological literature on causal inference using statistical methods recognizes the importance of and consequently allows for population heterogeneity (Heckman and Vytlacil 2005; Holland 1986; Manski 1995; Rubin 1974; Winship and Morgan 1999). Suppose that a population, U, is being studied. Let Y denote an outcome variable of interest (its realized value being y) that is defined for each member in U. Let us define treatment as an externally induced intervention that can, at least in principle, be given to or withheld from a unit under study. For simplicity, we consider only dichotomous treatments and use D to denote the treatment status (its realized value being d), with D = 1 if a member is treated and D = 0 if a member is not treated. Let subscript i represent the i^th member in U. We further denote $y_i^1$ as the i^th member’s potential outcome if treated (i.e., when d_i=1), and $y_i^0$ as the i^th member’s potential outcome if untreated (i.e., when d_i=0). The framework for counterfactual reasoning in causal inference (Heckman 2005; Holland 1986; Manski 1995; Morgan and Winship 2007; Rubin 1974; Sobel 2000; Winship and Sobel 2004) states that we should conceptualize a treatment effect as the difference in potential outcomes associated with different treatment states for the same member in U:

$${\delta }_i=y_i^1-y_i^0,$$ (1)

where δ_i represents the hypothetical treatment effect for the i^th member.² The fundamental problem of causal inference (Holland 1986) is that, for a given unit i, we observe either $y_i^1$ (if d_i=1) or $y_i^0$ (if d_i=0), but not both. Given this fundamental problem, Holland describes two possible solutions: the “scientific solution” and the “statistical solution.” The scientific solution capitalizes on homogeneity in assuming that all members in U are the same, in either the treated state or the control state: $y_i^1=y_j^1$ and $y_i^0=y_j^0$, where j ≠ i in U. This strong homogeneity assumption would enable a researcher to identify individual-level treatment effects by as few as two cases in U. However, as we discussed above, pervasive heterogeneity across units is the norm rather than the exception in a population science. Thus, in general, the scientific solution has no practical value in the social and behavioral sciences.

2.1. Quantities of Interest

For a population science, the statistical solution is a necessity. The statistical approach is to compute quantities of interest that reveal treatment effects only at the group level. For example, we may evaluate the average difference between a set of members in U that were randomly selected for treatment and another set of members that were randomly selected for control. This comparison yields a quantity that is called the average treatment effect (ATE):

$$\mathrm{ATE}=E(Y^1-Y^0).$$

While is defined for the whole population, the researcher may wish to focus on and define a treatment effect for a well-defined subpopulation. In contexts of program evaluation, for example, researchers may be primarily interested in the treatment effect of the treated (Heckman and Robb 1985), which refers to the average difference by treatment status among those individuals who are actually treated:

$$\mathrm{TT}=E(Y^1-Y^0\mid D=1).$$

Although various statistical quantities of interest can easily be defined theoretically with the statistical “solution,” estimating these quantities in social research can be very difficult, due to two types of selection bias, a topic to be discussed below.

2.2. Two Types of Selection Bias

In the preceding subsection, we established the need to conduct group-level comparisons for causal inference, because causal inference is impossible at the individual level. However, due to population heterogeneity, there is no guarantee that the group that actually receives the treatment is comparable, in observed and particularly in unobserved contextual and individual characteristics, to the group that does not receive the treatment.³ Individuals may self-select into treatment based on their anticipated monetary and nonmonetary benefits and costs of treatment. To see this, let us partition the total population U into the subpopulation of the treated U₁ (for which D=1) and the subpopulation of the untreated U₀ (for which D=0). We can thus decompose the expectations for the two counterfactual outcomes as follows:

$$E\left(Y^1\right)=E(Y^1\mid D=1)P(D=1)+E(Y^1\mid D=0)P(D=0),$$

and

$$E\left(Y^0\right)=E(Y^0\mid D=1)P(D=1)+E(Y^0\mid D=0)P(D=0).$$

The issue of selection stems from the scenario

$$E(Y^1\mid D=1)\ne E(Y^1\mid D=0)\ne E\left(Y^1\right),$$ (2)

and

$$E(Y^0\mid D=1)\ne E(Y^0\mid D=0)\ne E\left(Y^0\right).$$ (3)

Note that what we observe from data are $\widehat{E}(Y^1\mid D=1)$,$\widehat{E}(Y^0\mid D=0)$,$\widehat{P}(D=1)$, and $\widehat{P}(D=0)$. Due to inequalities (2) and (3), the simple-comparison estimator $\widehat{E}(Y^1\mid D=1)-\widehat{E}(Y^0\mid D=0)$, as a naive estimator for ATE, may be contaminated by selection bias. Denoting this estimator by ${\widehat{\beta }}_{naive}$, we can decompose its expectation as follows (Winship and Morgan 1999, p. 667):

$$\begin{array}{cc}\hfill E\left({\widehat{\beta }}_{naive}\right)=& E(Y^1\mid D=1)-E(Y^0\mid D=0)\hfill \\ \hfill =& E(Y^1-Y^0\mid D=1)+E(Y^0\mid D=1)-E(Y^0\mid D=0)\hfill \\ \hfill =& \mathrm{TT}+E(Y^0\mid D=1)-E(Y^0\mid D=0)\hfill \\ \hfill =& \mathrm{ATE}+(\mathrm{TT}-\mathrm{ATE})+E(Y^0\mid D=1)-E(Y^0\mid D=0).\hfill \end{array}$$ (4)

From equation (4), we see two sources of selection bias:

1. The difference in average outcomes between the treatment and control groups if neither group receives treatment: $E(Y^0\mid D=1)-E(Y^0\mid D=0)$. We call this the “pre-treatment heterogeneity bias” or “Type I selection bias.”

2. The difference in average treatment effects between the treated group and the entire population. We call this the “treatment-effect heterogeneity bias” or “Type II selection bias.” There is treatment-effect heterogeneity bias if and only if TT ≠ ATE.

We now illustrate the two different sources of selection bias with two concrete examples. First, pre-school children from poor families are selected into Head Start programs and thus would compare unfavorably to other children who do not attend Head Start programs without an adequate control for family socioeconomic resources (Xie 2000). Second, economic theory predicts that attainment of college education may be selective because it may attract young persons who are more motivated than their peers to gain from college education (Willis and Rosen 1979). While the first example reflects the importance of pre-treatment heterogeneity bias that may be represented by “covariates” or “fixed effects,” the second example underscores the possibility of treatment-effect heterogeneity bias – sorting on the treatment effects – which might not be captured by “covariates” or “fixed effects.”

2.3. Ignorability and Propensity Score

In observational studies, to overcome the two types of selection bias resulting from non-randomness in treatment assignment, a natural idea is to control for observed pre-treatment covariates. While it is not possible for a researcher to claim that he or she has controlled for all of the variables that may affect the outcome, it is more plausible to assume that the researcher has controlled for almost all of the relevant pre-treatment covariates that may affect both the treatment assignment and the outcome, a subset of all the variables affecting the outcome. In fact, only the covariates that meet the condition of affecting both the treatment assignment and the outcome may potentially confound the observed relationship between treatment and outcome (Rubin 1997). Thus, if we assume that all these relevant pre-treatment variables are observed, the treatment status will be independent of potential outcomes through control of these covariates. This conditional independence assumption is called “ignorability,” “unconfoundedness,” or “selection on observables.” If we let X be the vector of these observed covariates, the ignorability assumption states:

$$(Y^1,Y^0)\underset{¯}{\parallel }D\mid X.$$ (5)

Because we can never be sure after inclusion of which covariates equation (5) would hold true, the ignorability condition is always held as an assumption, indeed an unverifiable assumption. Substantive knowledge about the subject matter needs to be brought in before a researcher can entertain the ignorability assumption. Measurement of theoretically meaningful confounders makes ignorability tentatively plausible, but not necessarily true. However, the researcher can always consider the ignorability assumption and then assess its plausibility in a concrete setting through sensitivity or auxiliary analyses (Cornfield et al. 1959; DiPrete and Gangl 2004; Harding 2003; Rosenbaum 2002; Xie and Wu 2005).

If the ignorability assumption (5) holds true, we can change inequalities (2) and (3) into two equations by conditioning on X⁴:

$$E(Y^1\mid D=1,\mathit{X})=E(Y^1\mid D=0,\mathit{X})=E(Y^1\mid \mathit{X});$$ (6)

$$E(Y^0\mid D=1,\mathit{X})=E(Y^0\mid D=0,\mathit{X})=E(Y^0\mid \mathit{X}).$$ (7)

For now, we are concerned only with identification and postpone inference issues to a later discussion. Let us define quantities of interest for causal inference, conditioning on X, as follows:

$$\begin{array}{cc}\hfill \mathrm{ATE}\left(\mathit{X}\right)=& E(Y^1-Y^0\mid \mathit{X}),\hfill \\ \hfill \mathrm{TT}\left(\mathit{X}\right)=& E(Y^1-Y^0\mid D=1,\mathit{X}),\hfill \end{array}$$

Similarly, we define the naive estimator conditioning on X as:

$${\widehat{\beta }}_{naive}\left(\mathit{X}\right)=\widehat{E}(Y^1\mid D=1,\mathit{X})-\widehat{E}(Y^0\mid D=0,\mathit{X}).$$

Then equations (6) and (7) imply the following identity

$$E\left({\widehat{\beta }}_{naive}\left(\mathit{X}\right)\right)=\mathrm{ATE}\left(\mathit{X}\right)=\mathrm{TT}\left(\mathit{X}\right).$$ (8)

As a result, the ignorability assumption enables the naive estimator to identify both ATE and TT through control of X. Conditioning on X, however, can be difficult in applied research due to the “curse of dimensionality.” Rosenbaum and Rubin (1983, 1984) show that, when the ignorability assumption holds true, it is sufficient to condition on the propensity score as a function of X. That is to say, relation (5) implies:

$$(Y^1,Y^0)\underset{¯}{\parallel }D\mid P(D=1\mid \mathit{X}),$$

where P(D = 1|X) is the propensity score, the conditional probability of treatment given all the relevant information in covariates X. In other words, only through the propensity score P(D = 1|X) may covariates X confound the observed relationship between treatment D and outcome Y. In empirical settings, however, the propensity score first needs to be estimated. Because a fully nonparametric estimation of the propensity score would also suffer from the curse of dimensionality, the estimation is conventionally accomplished by a logit or probit regression. From here on, we denote by p the propensity score and by ${\widehat{\beta }}_{naive}\left(p\right)$ the naive estimator of treatment effect conditional on p. Note that ${\widehat{\beta }}_{naive}\left(p\right)$ here is a function of p, but not necessarily a linear function of p. There are a variety of methods for constructing ${\widehat{\beta }}_{naive}\left(p\right)$, such as matching and stratification (see Morgan and Winship 2007, chapter 4). Below, we introduce a new PS-based method by modeling counterfactual outcomes as nonparametric functions of the propensity score, which we call the “smoothing-difference method.”⁵

2.4. The Smoothing-Difference PS-Based Method

If treatment effects are heterogeneous, there are many possible ways to characterize the heterogeneity (Heckman and Robb 1985; Pearl 2009; Winship and Morgan 1999; Xie, Brand, and Jann 2012). The basic idea of the smoothing-difference method is fitting two nonparametric functions for E(Y¹|p) and E(Y⁰|p) and taking their differences as estimates of treatment effects. Specifically, it consists of the following four steps:

1. From observed Y¹ and Y⁰ and estimated propensity score $\widehat{p}$, fit two univariate functions, f₁(p) and f₀(p), to approximate E(Y¹|p) and E(Y⁰|p)

2. Use f₁(p) and f₀(p) to predict counterfactual outcomes $Y_i^1$ and $Y_i^0$ for each individual i in the sample.

3. Obtain the estimated treatment effect δ_i for each individual i by taking the difference between the predicted counterfactual outcomes.

4. Average estimated δ_i over the entire sample as the estimate of ATE, or over a specific subsample to estimate a corresponding group-level causal effect. For example, we may estimate TT by averaging δ_i over those subjects who are actually treated.

Note that in the first step, f₁(p) and f₀(p) could be fitted via different estimation methods. One simple possibility is to fit two linear models of Y₁ and Y₀ on p through OLS. However, this strategy imposes too strong a parametric assumption concerning the relationship between the outcome variables and the propensity score. As we will see in Section 5.2, empirical data could suggest a non-monotone treatment effect of college education as a function of propensity score. In this case, imposing a linear structure would mask interesting patterns of treatment effect heterogeneity, making it impossible to identify population subgroups that benefit differently from the treatment. Therefore, we propose to fit two smoothing splines (Hastie, Tibshirani, and Friedman 2008) of Y₁ and Y₀ on p with the smoothing parameter determined by generalized cross validation or some other criterion,⁶ an approach that we will adopt in our simulation studies in Section 4, as well as the analysis of NLSY data in Section 5.

Other propensity-score-based methods include matching, stratification, and weighting, all of which have been widely used in empirical research. Compared to these traditional methods, our smoothing-difference method has three distinct advantages.⁷ First and foremost, the research interest may lie in the trend of Δf(p), i.e., f₁(p) – f₀(p), which characterizes how the treatment effect varies across subjects with different propensities of being treated being treated (Brand and Xie 2010; Xie, Brand, and Jann 2012; Xie and Wu 2005). Such a pattern may identify population subgroups that benefit the most, or the least, from treatment, thus offering meaningful policy implications. For example, many countries are now rapidly expanding the size of college enrollment. The expansion of college education would be more effective if it were targeted at those individuals who are likely to benefit most from attending college. As the propensity of attending college could be directly estimated from individual characteristics for every potential college-goer, the expected returns to college could likewise be estimated. Hence, a propensity-score-based cost-benefit analysis would enable policymakers to fine-tune their strategies in expanding higher education. Furthermore, the researcher may be interested in the trends of the outcome as a function of the propensity score among either treated or untreated subjects, i.e., f₀(p) or f₁(p), which could not be extracted from results using matching or weighting methods. As we will illustrate in Section 5.2, these trends can enhance our understanding of the social processes that may be masked by too exclusive a focus on the estimation of causal effects. In addition, after we pool information through nonparametric regressions across adjacent cases within either treated or untreated groups, we are able to derive the estimated treatment effect δ_i for each individual i, before we calculate any group-level treatment effect through averaging over an appropriate subsample.

2.5. Decomposition of Ignorability

Equations (4) and (8) reveal that, under the ignorability assumption, controlling for observed covariates eliminates both types of selection bias. This suggests that the ignorability assumption should contain two components corresponding to the two types of bias. Indeed, ignorability expressed as relation (5) can be rewritten as

$$(Y^0,Y^1-Y^0)\underset{¯}{\parallel }D\mid \mathit{X}.$$

This expression reveals the two conditions underlying the ignorability assumption: Condition 1

$$Y^0\underset{¯}{\parallel }D\mid X,$$

i.e., given observed covariates, treatment status is independent of the baseline outcome; Condition 2

$$Y^1-Y^0\underset{¯}{\parallel }D\mid \mathit{X},$$

i.e., given observed covariates, treatment status is independent of the treatment effect. We may call Condition 1 the ignorability of Type I selection bias, and Condition 2 the ignorability of Type II selection bias.⁸ The ignorability assumption, in essence, means the ignorability of both Type I selection bias and Type II selection bias.

As mentioned in Section 2.3, Rosenbaum and Rubin (1983) derive the sufficiency of propensity score under the assumption of complete ignorability for eliminating confounding bias:

$$\text{If}(Y^1,Y^0)\underset{¯}{\parallel }D\mid \mathit{X},\text{then}(Y^1,Y^0)\underset{¯}{\parallel }D\mid P(D=1\mid \mathit{X}).$$

Indeed, the proof provided by Rosenbaum and Rubin (1983) implies the following two propositions: Proposition 1

$$\text{If}{Y}^0\underset{¯}{\parallel }D\mid \mathit{X},\text{then}{Y}^0\underset{¯}{\parallel }D\mid P(D=1\mid \mathit{X});$$ (9)

Proposition 2

$$\text{If}{Y}^1-Y^0\underset{¯}{\parallel }D\mid \mathit{X},\text{then}{Y}^1-Y^0\underset{¯}{\parallel }D\mid P(D=1\mid \mathit{X}).$$ (10)

As before, we denote by p the propensity score P(D = 1|X) and by ${\widehat{\beta }}_{naive}\left(p\right)$ the naive estimator of treatment effect conditional on p. In light of equation (4), the expectation of ${\widehat{\beta }}_{naive}\left(p\right)$ could be decomposed as

$$E\left({\widehat{\beta }}_{naive}\left(p\right)\right)=\mathrm{ATE}\left(p\right)+\mathrm{TT}\left(p\right)-\mathrm{ATE}\left(p\right)+E(Y^0\mid D=1,p)-E(Y^0\mid D=1,p)-E(Y^0\mid D=0,p).$$ (11)

Equation (11), combined with Propositions 1 and 2, shows that the naive estimator ${\widehat{\beta }}_{naive}\left(p\right)$ identifies different quantities under different conditions. First, if Condition 1 holds true, Type I selection bias thus becomes ignorable, i.e.,

$$E(Y^0\mid D=1,p)=E(Y^0\mid D=0,p).$$

In this scenario, we have

$$E\left({\widehat{\beta }}_{naive}\left(p\right)\right)=\mathrm{TT}\left(p\right)$$

Second, if Condition 2 holds true, Type II selection bias becomes ignorable, i.e.,

$$E(Y^1-Y^0\mid p,D=1)=E(Y^1-Y^0\mid p),$$

or

$$\mathrm{TT}\left(p\right)=\mathrm{ATE}\left(p\right).$$

In this scenario, we have

$$E\left({\widehat{\beta }}_{naive}\left(p\right)\right)=\mathrm{ATE}\left(p\right)+E(Y^0\mid D=1,p)-E(Y^0\mid D=0,p).$$

As a result, we conclude that:

1. If the ignorability of Type I selection bias (i.e., Condition 1) holds true, the naive estimator conditional on the propensity score, ${\widehat{\beta }}_{naive}$ confronts only Type II selection bias (treatment-effect heterogeneity bias), i.e., TT(p) ≠ ATE(p). However, if our quantity of interest is TT rather than ATE, ${\widehat{\beta }}_{naive}$ is an unbiased estimator.

2. If the ignorability of Type II selection bias (i.e., Condition 2) holds true, the naive estimator conditional on the propensity score, ${\widehat{\beta }}_{naive}$, is subject only to Type I selection bias (pre-treatment heterogeneity bias), i.e., E(Y⁰|D = 1, p) ≠ E(Y⁰|D = 0, p).⁹

3. Marginal-Treatment-Effect-Based Approach

So far, we have seen that propensity-score-based methods are subject to biases when the ignorability assumption is violated. Unfortunately, the ignorability assumption can never be verified. What recourse is available to a researcher who finds the ignorability assumption implausible in a research setting? In this section, we introduce the marginal treatment effect (MTE) approach developed by Heckman and his associates (Heckman and Vytlacil 1999, 2001, 2005; Heckman, Urzua, and Vytlacil 2006a, 2006b). Essentially, these researchers show that consistent estimates of a wide range of treatment parameters (including ATE and TT) can be obtained through different weighted averages of MTE (Björklund and Moffitt 1987). MTE could be estimated either parametrically or semi-parametrically. In the following, we briefly review this class of methods, under the heading of “MTE-based approach.”

3.1. The Definition of Marginal Treatment Effect

It is most convenient to explicate the MTE-based approach with three equations: outcome equations under two counterfactual regimes (D=0, D=1) and a treatment selection equation. In writing out each of the equations, we assume separability of the outcome variable into a structural component due to a linear function of pre-treatment covariates and residual components due to unobserved variables:¹⁰

$$\begin{array}{cc}\hfill Y^0=& {\beta }_0^{\prime }\mathit{X}+∊,\hfill \\ \hfill Y^1=& {\beta }_1^{\prime }\mathit{X}+∊+\eta .\hfill \end{array}$$

Here, corresponding to our decomposition of the two sources of ignorability, the error term ε captures the unobserved factors that affect only the baseline outcome, while the error term η represents the unobserved factors that affect only units that are treated. Thus, the treatment effect contains both the structural component (${\beta }_0^{\prime }\mathit{X}$ versus ${\beta }_1^{\prime }\mathit{X}$) and the residual component η. This setup changes equation (1) so that heterogeneous treatment effect can be written in a structural form:

$$\delta \left(X\right)=Y^1\left(X\right)-Y^0\left(X\right)={({\beta }_1-{\beta }_0)}^{\prime }\mathit{X}+\eta .$$

Note that the treatment effect δ depends on covariates X. If we denote byY the observed outcome and by D the treatment status, the above model could be written in the notation of switching regression models:

$$\begin{array}{cc}\hfill Y=& (1-D)Y^0+D{Y}^1\hfill \\ \hfill =& Y^0+D(Y^1-Y^0)\hfill \\ \hfill =& {\beta }_0^{\prime }\mathit{X}+{({\beta }_1-{\beta }_0)}^{\prime }\mathit{X}D+∊+\eta D.\hfill \end{array}$$

We further specify a model for selection into treatment. Let D* be the latent tendency to be treated:

$$\begin{array}{cc}\hfill D^{\ast }=& {\gamma }^{\prime }\mathit{z}-V,\hfill \\ \hfill D=& 1(D^{\ast }>0).\hfill \end{array}$$ (12)

Here, Z is a vector of variables that predict the treatment probability, γ is a vector of coefficients, and V is a latent random variable representing disturbance. As in standard regression models, we assume that error terms (ε, η, V) have zero means and are jointly independent of X and Z. In practice, Z consists of observed predictors of treatment probability, including all the components in X as well as some additional variables that predict only the treatment status D. These additional variables are called instrumental variables (IVs). The assumption that IVs affect only the treatment status D but not the outcome variable Y directly is called the exclusion restriction.

We can easily rewrite the treatment selection model (12) in the following form

$$\begin{array}{cc}\hfill {\tilde{D}}^{\ast }=& p\left(\mathit{Z}\right)-U_D\hfill \\ \hfill D=& 1({\tilde{D}}^{\ast }>0),\hfill \end{array}$$

where p(Z) = p(D = 1|Z) = F_v(γ’Z) denotes the propensity score of being treated given Z and U_D = F_V(V) follows a standard uniform distribution on [0,1]. U_D represents a catch-all unobserved selection component, interpretable as the level of unobserved resistance to receiving treatment, normalized between 0 and 1. We see that Z enters the treatment selection model only through the propensity score p(Z).

Based on the above specification of the outcome models and treatment selection model, the Marginal Treatment Effect (MTE) is defined as follows:

$$\begin{array}{cc}\hfill \mathrm{MTE}(x,u_D)=& E(\delta \mid \mathit{X}=x,U_D=u_D)\hfill \\ \hfill =& E({({\beta }_1-{\beta }_0)}^{\prime }x+\eta \mid \mathit{X}=x,U_D=u_D)\hfill \\ \hfill =& {({\beta }_1-{\beta }_0)}^{\prime }x+E(\eta \mid V=F_v^{-1}\left(u_D\right)).\hfill \end{array}$$ (13)

Thus, MTE is essentially the expected treatment effect conditional on observed covariates X = x as well as the unobserved selection component U_D = u_D.

As mentioned above, Heckman, Urzua, and Vytlacil (2006a, 2006b) have shown that group-level treatment effects such as ATE and TT can be expressed as weighted averages of MTE(x, u_D).¹¹ However, the estimation of MTE(x, u_D) is not straightforward since neither the counterfactual outcome nor the latent variable u_D is observed. Now we briefly sketch the two approaches to estimating MTE: (1) the parametric method, and (2) the semi-parametric method.

3.2. Parametric and Semi-parametric Estimation of MTE

First we write out the expectation of the observed outcome Y given covariates X = x and the propensity score p(Z) = p:

$$\begin{array}{cc}\hfill E(Y\mid \mathit{X}=x,p\left(\mathit{Z}\right)=p)=& E({\beta }_0^{\prime }\mathit{X}+{({\beta }_1-{\beta }_0)}^{\prime }\mathit{X}D+∊+\eta D\mid \mathit{X}=x,p(\mathit{Z}=p))\hfill \\ \hfill =& {\beta }_0^{\prime }x+{({\beta }_1-{\beta }_0)}^{\prime }xp+E(\eta \mid D=1,p\left(\mathit{Z}\right)=p)p\hfill \\ \hfill =& {\beta }_0^{\prime }x+{({\beta }_1-{\beta }_0)}^{\prime }xp+E(\eta \mid V<F_V^{-1}\left(p\right))p\hfill \\ \hfill =& {\beta }_0^{\prime }x+{({\beta }_1+{\beta }_0)}^{\prime }xp+{\int }_0^{p}E(\eta \mid V=F_V^{-1}\left(u_D\right))d{u}_D.\hfill \end{array}$$ (14)

Incorporating equation (13), the above expression can be simplified:

$$E(Y\mid \mathit{X}=x,p\left(\mathit{Z}\right)=p)={\beta }_0^{\prime }x+{\int }_0^p\mathrm{MTE}(x,u_D)d{u}_D.$$

Differentiating the above equation with respect to p, we obtain MTE:

$$\mathrm{MTE}(x,p)=\frac{\partial E(Y\mid \mathit{X}=x,p\left(Z\right)=p)}{\partial p}.$$ (15)

This expression relates MTE(x, p) to E(Y|X = x, p(Z) = p) and thus provides a possible route for estimating MTE.

In general, the third term in equation (14), ${\int }_0^{p}E(\eta \mid V=F_V^{-1}\left(u_D\right))d{u}_D$, is an unknown function of p. However, if we assume that error terms (ε, η, V) follow a joint Gaussian distribution N(0, Σ), E(Y|X = x, p(Z) = p) would become a linear combination of x, xp and ϕ(Φ⁻¹(p)). Accordingly, the expression of MTE reduces to

$$\mathrm{MTE}(x,u_D)={({\beta }_1-{\beta }_0)}^{\prime }x+{\sigma }_{nV}{\Phi }^{-1}\left(u_D\right),$$

where σ_ηv represents the covariance between η and V. With this parametric specification, we can estimate its unknown parameters (β₁, β₀, σ_ηv) via maximum likelihood. This is the parametric MTE-based method, which is also called the “control function approach.” In fact, given the parametric assumption, identification of MTE(x, u_D) is theoretically possible even without the presence of IVs.

In empirical settings, the assumption of joint normality is rarely justifiable. This motivated Heckman, Urzua, and Vytlacil (2006b) to develop a semi-parametric method to identify MTE(x, p), using equation (15), after first estimating equation (14) under more flexible assumptions. Their method involves four steps¹²:

1. Fit local linear regressions of Y, X, and X_p on p and extract their residuals R_Y, R_X, R_Xp.

2. Regress R_Y on R_X and R_Xp using least squares to estimate the parametric component of equation (14), i.e., β₀ and β₁ – β₀, and denote its residuals by $R_Y^{\ast }$.

3. Regress $R_Y^{\ast }$ on p using standard nonparametric techniques (such as local polynomial regression) to model the third term in equation (14) as well as its derivative, i.e., $E(\eta \mid V=F_v^{-1}\left(p\right))$

4. Construct MTE(x, u_D), expressed in equation (13), using ${\widehat{\beta }}_1-{\widehat{\beta }}_0$ from Step 2 and the estimate of $E(\eta \mid V=F_v^{-1}\left(p\right))$ from Step 3.

Appendix A provides our implementation of these procedures in R for estimating returns to college with a sample of white males from NLSY79.

Since this method capitalizes on the net relationship of E(Y|X = x, p(Z) = p) with p(Z) after all covariates in X are controlled for, the presence of at least a valid instrumental variable in Z is indispensable for identification. For this reason, the semi-parametric approach is also called the “local instrumental variable” (LIV) method. In spite of its flexibility, the LIV method has not been widely adopted in empirical research, due partly to its high data demand pertaining to IVs. Although a detailed discussion on the asymptotic variance of the maximum likelihood estimator for the parametric MTE method can be found in Heckman (1979) and Puhani (2000), statistical properties of the semi-parametric LIV method are not yet familiar to a wider research community.¹³ This motivates us to evaluate the performance of MTE-based methods through numerical simulation.

4. Evaluation of Different Methods

4.1. Assumptions for Identification

The preceding discussion indicates that different methods require different assumptions to identify group-level treatment effects. Table 1 summarizes the assumptions that are required for the PS-based methods, the parametric MTE-based method, and the semi-parametric MTE-based method to identify ATE and TT. Generally speaking, both the PS-based and MTE-based methods rely on strong and unverifiable assumptions, the former on ignorability, and the latter on exclusion restriction or the distribution of error terms. In particular, several facts deserve our attention. First, as we note in Section 2, the applicability of propensity-score-based methods is not limited to settings in which complete ignorability is satisfied. As long as the ignorability of Type I selection bias is satisfied, i.e., there is no systematic baseline difference between treated and untreated units given observed covariates, the PS-based models yield good estimates of TT, even in the presence of a heterogeneous treatment effect bias.

Table 1.

Assumptions for Identification

Method	Exclusion Restriction (A valid IV)	Distributional Form of Error Terms	Ignorability Assumption
PS-Based Methods	No	No	Yes
Parametric MTE	No	Yes	No
Semi-parametric MTE (LIV)	Yes	No	No

Notes: For the parametric MTE-based method, multivariate normality is conventionally assumed for error terms. For PS-based methods, when the parameter of interest is TT, only the ignorability of Type I selection bias is necessary.

Second, in contrast to the semi-parametric LIV approach, the parametric MTE-based method requires the assumption of joint normality for error terms. Although in principle the parametric MTE method does not need an instrumental variable for identification, estimation based on the parametric distribution can be highly imprecise. In practice, availability of IVs that satisfy the exclusion restriction would greatly improve the precision of the ML estimation.¹⁴ We shall study this facet of the MTE-based methods through numerical simulation in the next subsection.

In comparison with the PS-based methods, the MTE-based methods require a more explicit micro-level model. From the discussion in Section 3.2, we see that the expression of MTE in equation (13) requires the separability of observables and unobservables in the outcome equations. Also, to estimate the parametric component of the model, we need to specify a functional form (such as linearity) to characterize the dependence of Y⁰ and Y¹ on X. For the PS-based methods, however, the assumption of ignorability allows us to model counterfactual outcomes (or treatment effects) along the single dimension of propensity score. As this can be conducted in a purely nonparametric manner (as is commonly done in practice), the PS-based methods do not require an explicit model specification (except for the propensity score model).

Ultimately, a choice between the PS-based methods and the MTE-based methods is driven by the plausibility of the ignorability assumption versus the exclusion restriction assumption. On one hand, if we suspect violation of ignorability but have valid IVs, the MTE-based approach is preferable to the PS-based methods. However, as the exclusion restriction is also a strong and unverifiable assumption, determining its degree of plausibility requires substantial knowledge in an actual research setting. On the other hand, if we have no satisfactory instruments that would satisfy the exclusion restriction but have sufficient information on relevant individual and contextual characteristics so that the ignorability assumption becomes plausible, the PS-based approach is a reasonable choice.

From the above discussion, the general guideline is quite clear when one assumption is more plausible than the other. What, however, happens if the ignorability and the exclusion restriction assumptions are equally plausible -- or equally implausible? In the rest of this section, we examine the performances of different methods for the following two scenarios: (1) when both the ignorability and the exclusion restriction assumptions hold true; (2) when both the ignorability and the exclusion restriction assumptions break down.

4.2. When Both Ignorability and the Exclusion Restriction Hold True

As Table 1 shows, when both the ignorability and the exclusion restriction assumptions hold true, both the PS-based methods and the MTE-based methods can correctly identify group-level causal effects (as long as the data-generating model is rightly specified). In this case, they both provide estimates of ATE and TT that are asymptotically unbiased. Nonetheless, their statistical efficiency may differ. Although estimation uncertainty may converge to zero as sample size goes to infinity, we cannot avoid the limitation of sample size in empirical research. At present, we know little about the asymptotic variance of the estimators produced by the semi-parametric MTE method. It is therefore of practical relevance for us to explore the statistical efficiency of the methods being evaluated in this paper.

To achieve this end, we utilize simulated data. First, we generate data through the two potential outcome models and the treatment selection model described in Section 3:

$$\begin{array}{cc}\hfill Y^0=& {\beta }_{00}+{\beta }_{01}X+∊\hfill \\ \hfill Y^1=& {\beta }_{10}+{\beta }_{11}X+∊+\eta \hfill \\ \hfill D^{\ast }=& {\gamma }_0+{\gamma }_{1}X+{\gamma }_{2}Z-V\hfill \\ \hfill D=& 1(D^{\ast }>0),\hfill \end{array}$$

with the following parameterization:

$$\begin{array}{c}\hfill {\beta }_0=[{\beta }_{00},{\beta }_{01}]=[0,1],{\beta }_1=[{\beta }_{10},{\beta }_{11}]=[3,2]\hfill \\ \hfill \gamma =[{\gamma }_0,{\gamma }_1,{\gamma }_2]=[0,{\gamma }_1,{\gamma }_2],{\gamma }_1^2+{\gamma }_2^2=1\hfill \\ \hfill X,Z\sim N(0,1),X\underset{¯}{\parallel }Z\hfill \end{array}$$

ε, η, V~N(0,1), ε , η, V mutually independent

$$∊,\eta ,V\underset{¯}{\parallel }X,Z.$$

Note that in this parameterization, the mutual independence of error terms ε, η and V implies the validity of the ignorability assumption. The exclusion restriction is made true by the joint independence of error terms and Z, which serves here as an IV. However, the values of γ₁ and γ₂ are not fixed. We manipulate the value of γ₂ to vary the relative importance of Z in determining the treatment status. Evidently, when γ₂ is small, the strength of the IV, Z, is weak. Meanwhile, since X and Z are distributed as independent standard normal, we fix ||γ|| at 1 to keep the importance of the observables (X and Z) relative to the unobservable V roughly constant regardless of the value of γ₁ or γ₂.

In our simulation, we alter the value of ${\gamma }_2^2$ from 0 to 1 with a step size of 0.125, thus generating nine scenarios with a gradual change in the strength of the IV. For each of these scenarios, we conduct a Monte Carlo experiment as follows. First, we generate a hypothetical population of size 100,000. Next, we draw 100 samples of size 2500 from each of these populations. Then, for each sample, we estimate the causal parameters of ATE and TT with the three methods that we discussed in Section 2.4 and Section 3: (1) the smoothing-difference PS-based method (using smoothing splines); (2) the parametric MTE-based method; (3) the semi-parametric LIV method. For the first method, we construct the propensity score using only X.¹⁵ Finally, for each estimator, we report its standard error as an indicator of statistical efficiency.

In Figure 1, we plot the trends of the standard error for estimates of ATE and TT as we vary the explanatory power of the IV in the treatment selection model. First of all, we see that the semi-parametric MTE method (dotdash line) generally yields estimates with much larger standard errors than those from the other two methods. Indeed, when γ₂is very small (weak IV), the standard error of the semi-parametric LIV method (around 0.5) is more than five times as large as that of the PS-based method (less than 0.1). More importantly, Figure 1 shows that the relative strength of IV matters greatly for the efficiency of the two MTE-based methods. In fact, both the parametric and the semi-parametric MTE-based estimates undergo a substantial decline in standard error when the IV becomes a stronger predictor of treatment selection. In summary, two findings emerge from the results. On the one hand, when the IV is relatively weak, the PS-based method outperforms both MTE-based methods. On the other hand, when treatment selection is dominated by the IV (γ₂=1), the parametric MTE method and the PS-based method converge in their estimation uncertainty (around 0.1), whereas the semi-parametric MTE approach still suffers from an inefficiency penalty with a significantly larger standard error (around 0.3) for either ATE or TT.

Figure 1.

Standard Error by Strength of IV for Different Estimators of ATE (Left) and TT (Right)

Notes: The standard error for each estimator is calculated from 100 random samples of size 2500. Solid line: estimators using the smoothing-difference PS-based method; dashed line: estimators using the parametric MTE method; dotdash line: estimators using the semi-parametric MTE method.

From this simulation, we observe that when both ignorability and the exclusion restriction hold true, the PS-based method is generally preferable to the MTE-based methods, especially when the IV is relatively weak. Although the parametric MTE-based approach does not require the exclusion restriction for identification, its estimation efficiency depends heavily on the availability of a strong IV. The semi-parametric LIV estimation depends on an IV for identification and a strong IV for efficiency. As Figure 1 shows, when the IV strengthens as a predictor of treatment selection, estimates from the MTE-based methods become less uncertain.

4.3. When Both Ignorability and the Exclusion Restriction Break Down

When the ignorability and the exclusion restriction assumptions are both violated, neither PS-based methods nor MTE-based methods produce theoretically unbiased estimators of ATE and TT. Unfortunately, this is a likely situation in actual settings of empirical research. This motivates us to explore potential patterns of under/over-estimation due to the violation of both ignorability (for PS-based methods) and exclusion restriction (for MTE-based methods).

In Section 2.5, we showed some implications of PS-based estimation when ignorability is violated. Rewriting equation (11), we can express the biases of PS-specific estimators as

$$\begin{array}{cc}\hfill \mathrm{BiasATE}\left(p\right)=& E(Y^0\mid D=1,p)-E(Y^0\mid D=0,p)+\mathrm{TT}\left(p\right)-\mathrm{ATE}\left(p\right);\hfill \\ \hfill \mathrm{BiasTT}\left(p\right)=& E(Y^0\mid D=1,p)-E(Y^0\mid D=0,p).\hfill \end{array}$$

Therefore, the bias of ATE is an aggregate of Type I and Type II selection biases due to unobservables, whereas the bias of TT is due only to unobserved Type I selection. Neither of them depends on the validity of the exclusion restriction since IVs play no role in PS-based methods. According to the above two expressions, we summarize the directions of BiasATE and BiasTT under different scenarios of unobserved selection in Table 2. Hence, if we postulate with some confidence the underlying pattern of unobserved selection, we may surmise the direction of over/under-estimation of ATE and TT in PS-based estimation. For example, when there is a sorting on gain but no selection on level, PS-based methods are likely to overestimate ATE but not TT. If unobserved Type I and Type II selection biases are in the opposite direction, the sign of BiasATE, but not of BiasTT, would be indeterminate.

Table 2.

Biases of ATE and TT Due to Unobserved Selection for PS-based Estimators

Unobserved Selection		BiasATE	BiasTT
Type I	Type II
+	+	+	+
+	0	+	+
+	−	Uncertain	+
0	+	+	0
0	0	0	0
0	−	−	0
−	+	Uncertain	−
−	0	−	−
−	−	−	−

In contrast, when the exclusion restriction breaks down, it is difficult to know the direction of the bias for MTE-based estimators, because their analytical expressions are not readily available. To complicate things, the breakdown of the exclusion restriction may take different forms. The IV may be correlated, either positively or negatively, with either of the two error terms (ε, η). In any of these scenarios, the potential biases for ATE and TT may also be affected by the specific pattern of unobserved selection, i.e., the dependence of V on ε and η. In sum, there is no simple sum guideline that helps us decide whether ATE or TT will be over- or under-estimated by MTE-based methods when the exclusion restriction is violated.

However, for any particular case, we can still explore its consequences through numerical simulation. As an illustration, we explore below a concrete case that merits detailed investigation in which (1) there is a negative (unobserved) Type I selection and a positive (unobserved) Type II selection; and (2) the IV used for estimating MTE is correlated with the treatment effect Y₁ – Y₀. We use the same simulation setup as that in Section 4.2 with the following parameterization:

$$\begin{array}{c}\hfill {\beta }_0=[{\beta }_{00},{\beta }_{01}]=[0,1],{\beta }_1=[{\beta }_{10},{\beta }_{11}]=[3,2]\hfill \\ \hfill \gamma =[{\gamma }_0,{\gamma }_1,{\gamma }_2]=[0,1,0.2]\hfill \\ \hfill X,Z\sim N(0,1),X\underset{¯}{\parallel }Z\hfill \\ \hfill ∊,\eta ,V\sim N(0,1),∊\underset{¯}{\parallel }\eta ,cor(∊,V)=0.5,cor(\eta ,V)=-0.5\hfill \\ \hfill ∊,\eta ,V\underset{¯}{\parallel }X,∊,V\underset{¯}{\parallel }Z.\hfill \end{array}$$

Note that in this specification, we assume a positive correlation between ε and V (Type I selection) but a negative correlation between η and V (Type II selection). Since represents the latent resistance to receiving treatment, this setup is one of “negative sorting on level” and “positive sorting on gain.” This pattern reflects the literature in estimating returns to schooling. Under the conventional common effects model, the argument for “ability bias” (Griliches 1977) predicted a positive Type I selection due to unobserved ability, i.e., more capable individuals tend to acquire more education as well as to earn more money. However, more recent research considering heterogeneous effects has found support for the “comparative advantage” argument, which implies negative sorting on level as well as positive sorting on gain (Cunha, Heckman, and Navarro 2005; Willis and Rosen 1979). In other words, it is predicted that individuals who actually went to college would be worse off than those who did not if they had not attended college, although the former group has benefitted more from college education than the latter group would have had they attended college. Patterns of self-selection have been widely observed in other contexts (Winship and Mare 1992). For example, Smock, Manning, and Gupta (1999, p.809) found that “divorced women would not fare as well economically as married women had they remained married instead of divorcing,” indicating some self-selection into divorce among women who have less to lose from divorce.

Further, we assume independence between Z and ε but not between Z and η. The dependence between Z and η implies that Z is not truly exogenous but “moderates” the treatment effect. In the literature estimating earnings returns to college education, researchers have used the distance from a youth’s home to college as an IV (Cameron and Taber 2004; Card 1995; Currie and Moretti 2003; Kane and Rouse 1995). However, if returns to college vary by the distance measure, e.g., students living closer to colleges would benefit more from college than those who live further away, the IV would be correlated with η. Here, we vary the correlation between Z and η from −0.8 to 0.8 with a step size of 0.1, generating 17 scenarios.¹⁶ For each of these scenarios, we simulate a hypothetical sample of 20,000 and estimate the causal parameters of ATE and TT using the same three methods as specified in the previous subsection.¹⁷ Finally, we display the results in Figure 2.

Figure 2.

Estimated ATE (Left) and TT (Right) When Exclusion Restriction Breaks Down

Notes: This figure shows the estimates of ATE and TT using different methods as the correlation between Z and η changes from −0.8 to 0.8. Solid line: actual values of ATE and TT; dashed line: estimates using the smoothing-difference PS-based method; dotdash line: estimates using the parametric MTE method; longdash line: estimates using the semi-parametric MTE method.

The left panel of Figure 2 shows the estimates of ATE, along with its actual values (solid line). First of all, we can see that the MTE-based estimates of ATE are upwardly biased when cor(Z, η) > 0 and downwardly biased when cor(Z, η) < 0. In fact, the larger the correlation between Z and η, the higher the estimates from the MTE-based methods, especially the semi-parametric LIV estimates (longdash line). For example, when cor(Z, η) is larger than 0.5, the semi-parametric LIV estimates are greater than 6.0, twice as large as its actual value (3.0), whereas the parametric MTE-based estimates (dotdash line) are upwardly biased by a smaller magnitude, at about 4.0. In comparison, the PS-based estimates (dashed line) show a moderate downward bias in this setup. As expected, the magnitude of bias for the PS-based estimates does not depend on cor(Z, η), because the PS-based estimates do not rely on the exclusion restriction for estimation.

The right panel compares estimates of TT. Similar to the case of ATE, the semiparametric LIV approach yields estimates that are significantly upwardly biased when cor(Z, η) > 0, and downwardly biased when cor(Z, η) < 0. Nonetheless, the parametric MTE-based estimates are almost equal to the true value of TT across the entire range of cor(Z, η). Finally, the PS-based estimates of TT show a significant underestimation. In fact, we may infer this last result from an earlier discussion, as Table 2 indicates that TT is underestimated as long as there is a negative sorting on level.

Overall, the above simulation reveals that, when there is a negative sorting on level (Type I selection) and positive sorting on gain (Type II selection) due to unobservables, the MTE-based methods, especially the semi-parametric LIV method, may severely over- or under-estimate ATE and TT due to the use of an improper IV. As expected, the same causal parameters may be underestimated by the PS-based method. As we will see in the next section, these results can reasonably explain apparent discrepancies in an assessment of returns to college.

5. Empirical Example

To illustrate the three methods we discussed earlier, we applied them to the data used in Carneiro, Heckman, and Vytlacil’s (2011) study of returns to college education using MTE. In the subsections that follow, we (1) describe the data, (2) demonstrate the use of the smoothingdifference PS-based method, (3) replicate Carneiro, Heckman, and Vytlacil’s (2011) results using MTE, and (4) compare MTE-based and PS-based estimates of ATE and TT. In Appendix A, we provide R codes that we used to generate the results presented in this section.

5.1. Data Description

Following Carneiro, Heckman, and Vytlacil (2011), we reanalyze a sample of white males (N = 1747) who were 16-22 years old in 1979, drawn from the National Longitudinal Survey of Youth 1979 (NLSY). Treatment is college attendance, measured by having attained any postsecondary education by 1991. By this definition, the treated group consists of 865 subjects and the control group consists of 882 subjects. The wage variable is measured as an average of deflated (to 1983 constant dollars) non-missing hourly wages reported between 1989 and 1993. Pretreatment covariates (X) are urban residence at 14, AFQT score adjusted by years of schooling, mother’s years of schooling, number of siblings, permanent local log earnings at 17 (county log earnings averaged between 1973 and 2000), permanent local unemployment rate at age 17 (state unemployment rate averaged between 1973 and 2000) and cohort dummies. Instrumental Variables (Z/X) include (a) the presence of a four-year college in the county of residence at age 14, (b) local wage in the county of residence at age 17, (c) local unemployment rate in the state of residence at age 17, and (d) average tuition in public 4-year colleges in the county of residence at age 17. More detailed description of the dataset is provided in Carneiro, Heckman, and Vytlacil (2011).

5.2. The Smoothing-Difference PS-Based Results

Below we show results from the smoothing-difference PS-based method. First of all, we estimate the propensity score of attending college for each subject in the sample given X using a probit regression model. Table 3 presents the fitted propensity score model. We can see that the likelihood of attending college is predicted positively by corrected AFQT score and negatively by number of siblings and permanent local log earnings at age 17.

Table 3.

Propensity Score Probit Model Predicting College Attendance

Predictors	Coefficient
Urban Residence at 14	0.127 (0.084)
Corrected AFQT	0.667*** (0.045)
Corrected AFQT Squared	0.196*** (0.039)
Mother’s Years of Schooling	−0.110 (0.089)
Mother’s Years of Schooling Squared	0.010** (0.004)
Number of Siblings	−0.090† (0.053)
Number of Siblings Squared	0.002 (0.006)
Permanent Local Log Earnings at 17	−43.9* (17.2)
Permanent Local Log Earnings at 17 Squared	2.15* (0.84)
Permanent State Unemployment Rate at 17	0.240 (0.369)
Permanent State Unemployment Rate at 17 Squared	−0.018 (0.029)
Model χ2	684.4 (D.F.=18)

Notes: Numbers in parentheses are standard errors.

^†p<.1

^*p<.05

^**p<.01

^***p<.001

In the next step, we fit two separate nonparametric models regressing the log hourly wage on the estimated propensity score, one for the treated group that went to college and one for the untreated group that did not go to college. Here we use smoothing splines with 5 equivalent degrees of freedom.¹⁸ Figure 3 displays the resulting curves, evaluated over the entire interval (with a small portion being extrapolated). In the left panel, the dashed line and the dotdash line show the expected log hourly wage respectively for those who went to college and for those who did not. Two patterns emerge from this figure. First, for persons who attended college, the expected wage increases steadily with the propensity score. That is, labor market outcomes differ systematically among college goers, as those with a higher propensity to attend college earn more than those with a lower propensity. Second, for persons who did not attend college, expected wage shows a rapid increase at the lower end of propensity score but flattens out thereafter. Hence, individuals who are very unlikely to go to college on the basis of their observed covariates included in the propensity score are truly disadvantaged. If they do not go to college, they earn much lower wages than their peers with a higher propensity to attend college earn more than those with a lower propensity. Second, for persons who did not attend college, expected wage shows a rapid increase at the lower end of propensity score but flattens out thereafter. Hence, individuals who are very unlikely to go to college on the basis of their observed covariates included in the propensity score are truly disadvantaged. If they do not go to college, they earn much lower wages than their peers with a higher propensity to attend college (e^1.9 = 6.7 at p ≈ 0, compared to e^2.2 = 9.0 at p ≈ 0.2). However, they also stand to gain a lot from attending college (e^2.2 = 9.0 at p ≈ 0), although their wages would be still substantially lower than those of other college-goers with a higher propensity of attending college (e.g., e^2.8 = 16.4 at p ≈ 1.0).

Figure 3.

The Smoothing-Difference PS-based Method for Estimating Returns to College.

Notes: The left panel shows the expected annual wages respectively for those who attended college (dashed line) and for those who did not attend college (dotdash line). The right panel demonstrates the expected return to college for people with different propensity scores.

We now turn to the right panel, which depicts estimated heterogeneous treatment effects by propensity score.¹⁹ This curve is obtained directly by differencing the two functions in the left panel. The non-monotonic pattern suggests that two groups of individuals exist who benefit most from college: those most unlikely to go to college and those most likely to go to college.²⁰ Thus, college education seems to be more valuable for persons at either the low end or the high end of the propensity score than for those in the middle. Therefore, from the data, we observe a mix of positive selection and negative selection into college using the PS-based approach.

Next, we use the above curve to predict treatment effect δ_i for each individual i in the sample. We then average these δ_i’s over the entire sample to obtain ATE, and over those who actually attended college to estimate TT. We will discuss these summary results in the next subsection, comparing them to those produced by the MTE-based methods.

5.3. MTE-Based Results

We now give up the ignorability assumption and thus the propensity score approach. Instead, we use the MTE-based methods, with covariates X and instrumental variables (IVs) Z/X specified in Section 5.1. We first estimate two sets of marginal treatment effects, one from the parametric model, and the other from the semi-parametric LIV method. Figure 4 plots these two sets of MTE(x, u_D), both evaluated at mean values of X. Both the parametric and the semi-parametric estimates of MTE show a declining trend with respect to u_D, i.e., the unobserved resistance to attending college. These results show that individuals with higher returns to college are more likely to go to college (in having lower u_D). Furthermore, the magnitude of the heterogeneity in MTE is substantial: returns can vary from as high as 80%~100% (for low u_D persons, who would double their wages from attending college) to as low as −40% (for high u_D persons, who would lose from attending college).

Figure 4.

Estimated Marginal Treatment Effects (Averaged over X) from MTE-based Methods

Using weights provided by Heckman, Urzua, and Vytlacil (2006a), we construct standard treatment parameters from the two sets of estimated MTE. Columns 1-4 of Table 4 show the final estimates of ATE and TT from different methods, with bootstrapped standard errors. We observe that MTE-based estimates of ATE and TT are less precise than those from the PS-based method. The lack of precision for MTE-based estimates is expected since the IVs we use are relatively weak compared to X in determining treatment selection (see Section 4.2). More importantly, MTE-based and PS-based results differ in magnitude. For ATE, the differences are not statistically significant, although the semi-parametric LIV method seems to give a larger point estimate than do the other two methods. For TT, the difference between MTE-based and PS-based results is more substantial. Both the parametric and the semi-parametric MTE-based methods yield significantly higher estimates of TT than the PS-based estimate. Specifically, we obtain the TT estimate of college returns at 73.6% by the semi-parametric MTE method but only 27.8% by the PS-based method.

Table 4.

Estimates for Returns to College from NLSY data

Causal Parameters	Smoothing-Difference PS-Based Method	MTE-Based Methods		MTE-Based Methods (without tuition)
		Parametric	Semi- parametric	Parametric	Semi- parametric
ATE	0.242 (0.067)	0.264 (0.159)	0.356 (0.174)	0.231 (0.147)	0.277 (0.202)
TT	0.278 (0.093)	0.567 (0.156)	0.736 (0.226)	0.540 (0.144)	0.604 (0.243)

Notes: Numbers in parentheses are bootstrapped standard errors with 250 repetitions.

5.4. Discussion on the Discrepancy in Estimates of TT

From table 4 a natural question arises: why is there such a large discrepancy between PS-based and MTE-based estimates of TT? In light of our discussion in Section 4.3, we can offer some speculations. On the one hand, there could be an underestimation by the PS-based method due to the breakdown of the ignorability assumption. One way to examine the potential pattern of unobserved selection is from the MTE-based analysis. In fact, the parametric MTE approach provides the following estimates:

$${\widehat{\sigma }}_{∊V}=0.08,{\widehat{\sigma }}_{\eta V}=-0.24,$$

where σ_εv and σ_ηv denote the covariances respectively between ε and V and between η and V. Since V represents a latent resistance to receiving treatment, these estimates suggest a negative sorting on level and a positive sorting on gain. This finding accords well with Willis and Rosen’s (1979) model of comparative advantage, which argues that college-goers would do worse if they did not go to college but benefit more from college education than persons who do not go to college. If we accept these estimates as evidence for a negative Type I selection and a positive Type II selection (due to unobservables), our earlier discussion around Table 2 would suggest indeed a downward bias for the PS-based estimate of TT. Hence, the discrepancy in TT estimates between PS-based and MTE-based methods could be attributed to a negative sorting on pre-college earnings.

On the other hand, there might be an overestimation by MTE-based methods due to the violation of the exclusion restriction. The numerical simulation results in Section 4.3 suggest a potentially upward bias when there is a positive correlation between IV and the treatment effect, i.e., cor(Z, η) > 0 (for γ > 0). Unfortunately, such a correlation is empirically unverifiable, since η is an unobserved attribute that cannot be individually recovered from the data. Nonetheless, our results provide good grounds for questioning the theoretical validity of IV in concrete settings. In our example, one of the instrumental variables is average tuition in public four-year colleges in the county of residence. This variable, however, is likely to be correlated with college quality and thus could influence the returns to college. To test this conjecture, we excluded average tuition as an instrumental variable and reanalyzed the data.²¹ Columns 5 and 6 of Table 4 show the results for ATE and TT after this modification. Compared with columns 3, the new results by the parametric MTE-based method are largely unchanged. However, for the semi-parametric LIV approach, the large estimates reported earlier, especially of TT, are markedly reduced.

In sum, the large discrepancy in TT between PS-based and MTE-based estimates may be caused by one of three underlying causal mechanisms: (1) the negative sorting on pre-college earnings, (2) the use of an improper IV, or (3) a mixture of the previous two. Because of this uncertainty, neither the PS-based method nor the (semi-parametric) MTE-based method yields the true average treatment effect of college education for college goers. Most likely, the truth lies somewhere in between.

6. Concluding Remarks

In this study, we have examined certain statistical properties of PS-based methods and MTE-based methods through an exposition of identification issues, two simulation analyses, and an empirical application. We showed that the applicability of PS-based methods is not limited to settings in which complete ignorability is satisfied. In fact, it is useful to decompose ignorability into two components: (1) ignorability of Type I selection bias, or baseline difference between treated and untreated units; (2) ignorability of Type II selection bias, or difference in treatment effects between treated and untreated units. We have shown that as long as the ignorability of Type I selection bias is satisfied, PS-based methods can still identify TT, even in the presence of a heterogeneous treatment effect bias. Furthermore, when Type I selection bias cannot be ignored, the bias for TT is in the same direction as the Type I selection bias. For example, in the evaluation of returns to college, a negative Type I selection bias is part of the model of “comparative advantage.” An underestimation of TT by PS-based methods would occur under this situation.

By comparison, MTE-based methods are robust to different types of violation of the ignorability assumption. However, they require strong instrumental variables to achieve statistical efficiency. This is true for both the parametric model and the semi-parametric method. Furthermore, when the exclusion restriction is violated, MTE-based methods, especially the semi-parametric LIV approach, can be subject to severe over- or under-estimation of treatment effects. In practice, the plausibility of the exclusion restriction assumption cannot be verified but can be evaluated based on substantive knowledge about the research setting. If substantive concerns suggest the violation of the exclusion restriction, we could, as we did in Section 5.4, exclude the susceptible IV in the treatment selection model and reanalyze the data. In addition, we may directly assess the consequence of a violation of the assumption through sensitivity analyses (for examples, see Angrist 1990; Angrist, Imbens, and Rubin 1996).

This paper has also proposed a PS-based method based on first smoothing two counterfactual outcomes, which we call the smoothing-difference method. Compared to traditional matching and stratification methods, the smoothing-difference method has two distinct advantages. On the one hand, it enables the researcher to examine the nonparametric trends of counterfactual outcomes by treatment status across the spectrum of propensity score. In our empirical example, we have shown the variations in wages by both the propensity score of attending college and the status of college attendance. On the other hand, this method produces a nonparametric pattern of treatment effect heterogeneity across individuals with different propensity scores. Such an observed pattern of heterogeneity is of interest to social science researchers, although its interpretation is still ambiguous, depending on the validity of the ignorability assumption (Brand and Xie 2010; Xie, Brand, and Jann 2012). For example, if the ignorability assumption holds true, observed results reveal the pattern of heterogeneous treatment effects. If one accepts only the ignorability of Type I selection bias, heterogeneous treatment effects along the propensity score should be interpreted only for those who are actually treated. If one does not embrace any form of ignorability, the observed pattern may reveal an underlying selection process sorting out treated units from untreated units (Xie and Wu 2005).

Appendix A: R Implementation of Different Methods for the NLSY data

This appendix provides the R codes that were used to estimate returns to college for the NLSY data. The NLSY dataset is available upon request.

The Smoothing-Difference PS-based Method

library(Hmisc)

library(survival)

library(splines)

library(KernSmooth)

library(stats)

#Read Data#

nlsy=read.table(“nlsyfinal.csv”,sep=“,”,header=T)

#Propensity Score Model#

prps=glm(state~urban14+numsibs+I(numsibs^2)+mhgc+I(mhgc^2)+cafqt+I(cafqt^2)+d57+d58+d 59+d60+d61+d62+d63+lavlocwage17+I(lavlocwage17^2)+avurate+I(avurate^2),family=binomial(link=“probit”),data=nlsy)

#Extract Fitted Propensity Scores#

ps=prps$fitted

nlsy=cbind(nlsy,ps)

attach(nlsy)

# PS-based Smoothing Splines#

nlsy1=nlsy[state==1,]

nlsy0=nlsy[state==0,]

ps.ss1=smooth.spline(nlsy1$ps,nlsy1$wage,df=5)

ps.ss0=smooth.spline(nlsy0$ps,nlsy0$wage,df=5)

pred.ss1=predict(ps.ss1,ps)$y

pred.ss0=predict(ps.ss0,ps)$y

TE.pred.ss=pred.ss1-pred.ss0

#Estimating ATE and TT#

ATE.ss=mean(TE.pred.ss)

TT.ss=sum(TE.pred.ss*state)/sum(state)

#Plot of Heterogeneous Treatment Effect along the Propensity Score#

x=seq(0.005,0.995,0.01)

y1=predict(ps.ss1,x)$y

y0=predict(ps.ss0,x)$y

plot(x,y1-y0,type=“l”,ylim=c(0,0.6),xlab=“Estimated Propensity Score”,ylab=“Estimated Treatment Effect”,lwd=2.5,cex.lab=1.4)

The Parametric and Semi-parametric MTE-Based Methods

library(Hmisc)

library(survival)

library(splines)

library(KernSmooth)

library(stats)

library(sampleSelection)

nlsy=read.table(“nlsyfinal.csv”,sep=“,”,header=T)

attach(nlsy)

N=dim(nlsy)[1]

#Propensity Score Model for MTE-based Methods#

prps=glm(state~urban14+numsibs+I(numsibs^2)+mhgc+I(mhgc^2)+cafqt+I(cafqt^2)+d57+d58+d59+d60+d61+d62+d63+lavlocwage17+I(lavlocwage17^2)+avurate+I(avurate^2)+pub4+pub4*caf qt+pub4*mhgc+pub4*numsibs+lwage5_17+lwage5_17*cafqt+lwage5_17*mhgc+lwage5_17*numsib s+lurate_17+lurate_17*cafqt+lurate_17*mhgc+lurate_17*numsibs+tuit4c+tuit4c*cafqt+tuit4c*mhg c+tuit4c*numsibs,family=binomial(link=“probit”),data=nlsy)

#Extract Fitted Propensity Scores#

ps=prps$fitted

# Estimation of TT&ATE Weights #

ud=array(0,c(1,100))

for (i in seq(1,100)){ud[i]=-0.005+0.01*i}

nume=array(0,c(N,100))

deno=array(0,c(N,1))

wate=array(1/100,c(N,100))

wtt=array(0,c(N,100))

for (i in seq(1,100)){

wtt.S=(ps>ud[i])

wtt.glm=glm(wtt.S~exp+d57+d58+d59+d60+d61+d62+d63+expsq+urban14+numsibs+I(numsibs ^2)+cafqt+I(cafqt^2)+mhgc+I(mhgc^2)+lavlocwage17+I(lavlocwage17^2)+avurate+I(avurate^2)+ lwage5+lurate,family=binomial(link=“probit”))

nume[,i]=wtt.glm$fitted}

for (i in seq(1,N)){deno[i]=sum(nume[i,])

for (j in seq(1,100)){wtt[i,j]=nume[i,j]/deno[i]}}

#PARAMETRIC MTE-BASED METHOD#

#Heckman Selection Model#

heckit=selection(state~urban14+numsibs+I(numsibs^2)+mhgc+I(mhgc^2)+cafqt+I(cafqt^2)+d57 +d58+d59+d60+d61+d62+d63+lavlocwage17+I(lavlocwage17^2)+avurate+I(avurate^2)+pub4+p ub4*cafqt+pub4*mhgc+pub4*numsibs+lwage5_17+lwage5_17*cafqt+lwage5_17*mhgc+lwage5_17 *numsibs+lurate_17+lurate_17*cafqt+lurate_17*mhgc+lurate_17*numsibs+tuit4c+tuit4c*cafqt+tuit 4c*mhgc+tuit4c*numsibs,list(wage~exp+d57+d58+d59+d60+d61+d62+d63+expsq+urban14+num msibs+I(numsibs^2)+cafqt+I(cafqt^2)+mhgc+I(mhgc^2)+lavlocwage17+I(lavlocwage17^2)+avura te+I(avurate^2)+lwage5+lurate),nlsy)

#Create a Data-frame for X#

X=data.frame(1,exp,d57,d58,d59,d60,d61,d62,d63,expsq,urban14,numsibs,numsibs^2,cafqt,cafqt^ 2,mhgc,mhgc^2,lavlocwage17,lavlocwage17^2,avurate,avurate^2,lwage5,lurate)

#Estimated Coefficients of X in MTE, that is, β1 – β0#

X.coef=heckit$estimate[61:83]-heckit$estimate[36:58]

#Estimated Coefficient of Φ−1(uD) in MTE, that is, σηv#

ud.coef=-heckit$estimate[85]*heckit$estimate[84]+heckit$estimate[59]*heckit$estimate[60]

#Parametric Estimation of MTE #

MTE.par=array(0,c(N,100))

MTE.par.x=as.matrix(X) %*% matrix(X.coef)

for (i in seq(1,N)){for (j in seq(1,100)){MTE.par[i,j]=MTE.par.x[i]+ud.coef*qnorm(ud[j])}}

#Plot of Parametric MTE#

plot(seq(0.005,0.995,0.01),apply(MTE.par,2,mean),type=“l”,xlab=expression(U[D]),ylab=“Marginal Treatment Effect”,main=“Parametric Estimates of MTE”,lwd=2.5,cex.lab=1.4,cex.main=1.2)

#Parametric Estimation of ATE and TT#

ATE.par.x=apply(MTE.par*wate,1,sum)

TT.par.x=apply(MTE.par*wtt,1,sum)

ATE.par=mean(ATE.par.x)

TT.par=sum(TT.par.x*state)/sum(state)

#SEMI-PARAMETRIC MTE-BASED METHOD#

#Semi-parametric Estimation of MTE: Step 1#

exp.res=loess(exp~ps,degree=1)$res

expsq.res=loess(expsq~ps,degree=1)$res

lwage5.res=loess(lwage5~ps,degree=1)$res

lurate.res=loess(lurate~ps,degree=1)$res

lavlocwage17.res=loess(lavlocwage17~ps,degree=1)$res

lavlocwage17sq.res=loess(lavlocwage17^2~ps,degree=1)$res

avurate.res=loess(avurate~ps,degree=1)$res

avuratesq.res=loess(avurate^2~ps,degree=1)$res

cafqt.res=loess(cafqt~ps,degree=1)$res

cafqtsq.res=loess(cafqt^2~ps,degree=1)$res

mhgc.res=loess(mhgc~ps,degree=1)$res

mhgcsq.res=loess(mhgc^2~ps,degree=1)$res

numsibs.res=loess(numsibs~ps,degree=1)$res

numsibssq.res=loess(numsibs^2~ps,degree=1)$res

d57.res=loess(d57~ps,degree=1)$res

d58.res=loess(d58~ps,degree=1)$res

d59.res=loess(d59~ps,degree=1)$res

d60.res=loess(d60~ps,degree=1)$res

d61.res=loess(d61~ps,degree=1)$res

d62.res=loess(d62~ps,degree=1)$res

d63.res=loess(d63~ps,degree=1)$res

urban14.res=loess(urban14~ps,degree=1)$res

psexp.res=loess(ps*exp~ps,degree=1)$res

psexpsq.res=loess(ps*expsq~ps,degree=1)$res

pslwage5.res=loess(ps*lwage5~ps,degree=1)$res

pslurate.res=loess(ps*lurate~ps,degree=1)$res

pslavlocwage17.res=loess(ps*lavlocwage17~ps,degree=1)$res

pslavlocwage17sq.res=loess(ps*lavlocwage17^2~ps,degree=1)$res

psavurate.res=loess(ps*avurate~ps,degree=1)$res

psavuratesq.res=loess(ps*avurate^2~ps,degree=1)$res

pscafqt.res=loess(ps*cafqt~ps,degree=1)$res

pscafqtsq.res=loess(ps*cafqt^2~ps,degree=1)$res

psmhgc.res=loess(ps*mhgc~ps,degree=1)$res

psmhgcsq.res=loess(ps*mhgc^2~ps,degree=1)$res

psnumsibs.res=loess(ps*numsibs~ps,degree=1)$res

psnumsibssq.res=loess(ps*numsibs^2~ps,degree=1)$res

psd57.res=loess(ps*d57~ps,degree=1)$res

psd58.res=loess(ps*d58~ps,degree=1)$res

psd59.res=loess(ps*d59~ps,degree=1)$res

psd60.res=loess(ps*d60~ps,degree=1)$res

psd61.res=loess(ps*d61~ps,degree=1)$res

psd62.res=loess(ps*d62~ps,degree=1)$res

psd63.res=loess(ps*d63~ps,degree=1)$res

psurban14.res=loess(ps*urban14~ps,degree=1)$res

wage.res=loess(wage~ps,degree=1)$res

#Semi-parametric Estimation of MTE: Step 2#

double.res=lm(wage.res~0+exp.res+expsq.res+lwage5.res+lurate.res+lavlocwage17.res+lavlocwag e17sq.res+avurate.res+avuratesq.res+cafqt.res+cafqtsq.res+mhgc.res+mhgcsq.res+numsibs.res+nu msibssq.res+d57.res+d58.res+d59.res+d60.res+d61.res+d62.res+d63.res+urban14.res+psexp.res+ psexpsq.res+pslwage5.res+pslurate.res+pslavlocwage17.res+pslavlocwage17sq.res+psavurate.res +psavuratesq.res+pscafqt.res+pscafqtsq.res+psmhgc.res+psmhgcsq.res+psnumsibs.res+psnumsibs sq.res+psd57.res+psd58.res+psd59.res+psd60.res+psd61.res+psd62.res+psd63.res+psurban14.res) temp.X=data.frame(exp,expsq,lwage5,lurate,lavlocwage17,lavlocwage17^2,avurate,avurate^2,cafqt ,cafqt^2,mhgc,mhgc^2,numsibs,numsibs^2,d57,d58,d59,d60,d61,d62,d63,urban14,ps*exp,ps*exps q,ps*lwage5,ps*lurate,ps*lavlocwage17,ps*lavlocwage17^2,ps*avurate,ps*avurate^2,ps*cafqt,ps*c afqt^2,ps*mhgc,ps*mhgc^2,ps*numsibs,ps*numsibs^2,ps*d57,ps*d58,ps*d59,ps*d60,ps*d61,ps*d6 2,ps*d63,ps*urban14)

wage.latent=wage-as.matrix(temp.X) %*% matrix(double.res$coef)

#Semi-parametric Estimation of MTE: Step 3#

MTE.semi.ud=locpoly(ps,wage.latent,drv=1L,bandwidth=0.32,gridsize=100L,range.x=c(0.005,0.995 ))

#Semi-parametric Estimation of MTE: Step 4#

MTE.semi=array(0,c(N,100))

MTE.semi.x=as.matrix(temp.X[,1:22]) %*% matrix(double.res$coef[23:44])

for (i in seq(1,N)){for (j in seq(1,100)){MTE.semi[i,j]=MTE.semi.x[i]+MTE.semi.ud$y[j]}}

#Plot of Semi-parametric MTE#

plot(seq(0.005,0.995,0.01),apply(MTE.semi,2,mean),type="l",xlab=expression(U[D]),ylab="Margina

l Treatment Effect",main="Semi-parametric Estimates of MTE",lwd=2.5,cex.lab=1.4)

# Semiparametric Estimation of ATE and TT#

ATE.semi.x=apply(MTE.semi*wate,1,sum)

TT.semi.x=apply(MTE.semi*wtt,1,sum)

ATE.semi=mean(ATE.semi.x)

TT.semi=sum(TT.semi.x*state)/sum(state)