Trade Openness and Growth
Pursuing Empirical Glasnost
  • 1 0000000404811396https://isni.org/isni/0000000404811396International Monetary Fund
  • | 2 0000000404811396https://isni.org/isni/0000000404811396International Monetary Fund

Contributor Notes

Authors’ E-Mail Addresses: abillmeier@imf.org ; tommaso.nannicini@uc3m.es

Studies of the impact of trade openness on growth are based either on cross-country analysis-which lacks transparency-or case studies-which lack statistical rigor. We apply transparent econometric methods drawn from the treatment evaluation literature to make the comparison between treated (i.e., open) and control (i.e., closed) countries explicit while remaining within a unified statistical framework. First, matching estimators highlight the rather far-fetched country comparisons underlying common cross-country results. When appropriately restricting the sample, we confirm a positive and significant effect of openness on growth. Second, we apply synthetic control methods-which account for endogeneity due to unobservable heterogeneity-to countries that liberalized their trade regime and we show that trade liberalization has often had a positive effect on growth.

Abstract

Studies of the impact of trade openness on growth are based either on cross-country analysis-which lacks transparency-or case studies-which lack statistical rigor. We apply transparent econometric methods drawn from the treatment evaluation literature to make the comparison between treated (i.e., open) and control (i.e., closed) countries explicit while remaining within a unified statistical framework. First, matching estimators highlight the rather far-fetched country comparisons underlying common cross-country results. When appropriately restricting the sample, we confirm a positive and significant effect of openness on growth. Second, we apply synthetic control methods-which account for endogeneity due to unobservable heterogeneity-to countries that liberalized their trade regime and we show that trade liberalization has often had a positive effect on growth.

I. Introduction

The relationship between trade openness or economic liberalization on the one hand, and income or growth on the other, is one of the main conundra in the economics profession, especially when it comes to combining theoretical and policy-related with empirical findings. The theoretical advantages of trade for growth are known at least since Ricardo: international trade enables a country to specialize using its comparative advantage and benefit both statically and dynamically from the international exchange of goods.1 From a policy perspective, the continuing efforts to liberalize international trade on a multilateral basis—first under GATT and now WTO leadership—have contributed to better market access and rates of growth of international current account transactions much above worldwide economic growth. From an empirical point of view, however, the trade-growth link is still under discussion, both from a methodological angle and regarding the size and significance of the estimated effects.

Testing the empirical relevance of important theoretical predictions in macroeconomics, growth theory, and political economics builds on cross-country evidence. In the attempt to detect correlations or causal relationships between aggregate variables, usually within-country variation is not sufficiently large to estimate the parameters of interest in a significant way, or it is so peculiar to the countries under consideration that the estimates have no external validity. At the end of the day, one must use cross-country variation to make inference over macro variables.

There is, however, widespread skepticism regarding the possibility of making sound inference based on cross-country data. The empirical debate over the trade-growth nexus is a paradigmatic case. As Bhagwati and Srinivasan (2001) point out, both globalization supporters and foes rely on cross-country estimates, which dramatically suffer from specification problems, endogeneity, and measurement errors. According to them, cross-country regression estimates are completely unreliable. Robust evidence on the relationship between trade openness and growth “can come only from careful case studies of policy regimes of individual entries” (p. 19). Case studies, however, also suffer from apparent weaknesses as they lack statistical rigor and are exposed to arbitrary case selection. Instead of throwing out the baby (that is, cross-country statistical analysis) with the bath water (that is, growth regressions of any type), we propose to apply recent econometric techniques that perform data-driven comparative case studies.

In this paper, we evaluate the effect of a binary treatment—trade openness or economic liberalization—on the outcome, changes in per capita income. We first show the pitfalls stemming from applying estimators based on cross-sectional information—like Ordinary Least Squares (OLS)— to the trade-growth nexus. We use microeconometric matching estimators from the treatment evaluation literature that are based on the same identifying assumption as OLS (conditional independence; that is, the selection into treatment is fully determined by observable characteristics) to make the estimation procedure more transparent—to bring glasnost to muddied waters. In doing so, we are able to show that the country comparisons that lie behind simple cross-sectional estimates are often more than far-fetched. We argue that it is important to control for continent or macro-region dummies to make cross-country comparisons more sensible.

We also show, however, that this remedy may not be enough if open and closed countries are not evenly distributed across regions—that is, they lack common support. For example, for a prominent openness indicator from the literature, developed countries should not be used to investigate the trade-growth link as all countries in this group are open and do not provide the necessary within-group variation to estimate the counterfactual outcome in the case of no treatment. Cleaning the sample for regions with no common support between treated and control units, we confirm a significant effect of openness on growth within selected areas and after 1970.

In the end, we wind up with the usual statistical trade-off between internal and external validity. While dropping the country groups that show little or no variation with regard to the treatment produces more sound statistical inference (internal validity), these results cannot be extrapolated to make general statements that go beyond the sample effectively used in the estimation, reducing external validity. In other words, it is unlikely that the effect of openness on growth can be robustly estimated for a world-wide sample of countries, casting doubt on much of the cross-sectional growth literature that strives to cover an ever-increasing set of countries.

While we find the matching results instructive for a number of reasons, they are not able to deal with two major endogeneity issues of OLS estimates in the trade-growth context—unobservable country heterogeneity and reverse causality. These limitations of cross-sectional estimators further strengthen the case for using panel set-ups to investigate the openness-growth nexus as argued in the recent literature. In fact, current panel methods can overcome some of the OLS weaknesses by using within-country (i.e., time-series) information to control for unobservable time-invariant country characteristics. However, as long as these estimators still use some cross-country variation—as does, for example, the difference-in-differences estimator—they still suffer from a lack of transparency. Therefore, we apply the synthetic control method, a recent econometric tool that is close in spirit to the matching estimator mentioned above and is able to account for time-varying country unobservables, in a panel set-up to infer the openness-growth link. In this context, the treatment takes a time dimension, i.e., it coincides with trade liberalization instead of openness. The advantage of this approach lies in the transparent construction of the counterfactual outcome of the treated, namely the synthetic control—a linear combination of untreated countries. These comparison countries are selected based on their similarity to the treated before the treatment, both with respect to relevant covariates and the past realizations of the outcome. We study all episodes of trade liberalization that took place after 1965 in countries that form part of the IMF’s Middle East and Central Asia Department (MCD). We find that, for most of these countries, trade liberalization has had a positive effect on growth.

The remainder of this paper is structured as follows. In Section II, we briefly review the empirical literature related to our paper, mainly studies on trade and growth aiming at overcoming some of the OLS weaknesses and studies that apply matching estimators to cross-country data sets. In Section III, we briefly present the data sources and variables of interest. In Section IV, we introduce matching estimators and apply them to two data sets recently used in the literature. Going beyond a merely descriptive discussion of the association between openness and growth, the synthetic control method is employed in Section V to empirically explore the effect of trade liberalization on growth in MCD countries. Section VI concludes.

II. Literature Review

A. Empirical Studies on Trade Openness and Growth

Providing conclusive empirical evidence on the intuitively positive causal effect of trade on growth has been a challenging endeavor, complicated by a multiplicity of factors; see, for example, Winters (2004) for an overview. Most of the literature has used cross-country evidence that suffers from numerous shortcomings, related to both the measurement of openness and econometric modeling.

Following Barro’s (1991) seminal paper on growth regressions, several prominent cross-country studies established a positive link between trade openness and growth; these studies include Dollar (1992), Sachs and Warner (1995), and Edwards (1992, 1998). Similarly, Vamvakidis (2002) finds, in a historical context, evidence that trade is associated with growth after 1970 but not before. In a stern review of the cross-sectional literature on trade and growth, Rodriguez and Rodrik (2001) criticize the choices of openness measure and weak econometric strategies. They find little evidence that open trade policies as measured in the aforementioned contributions are significantly associated with economic growth once they correct for the weaknesses they point out. Harrison (1996) shows that most of the explanatory power of the composite openness dummy assembled in Sachs and Warner (1995) comes from the non-trade components of this measure.

From a methodological perspective, deep skepticism has been brought to bear against cross-country evidence on the trade-growth issue. In addition to the citation above, Bhagwati and Srinivasan (2002, p. 181) point out that “cross-country regressions are a poor way to approach this question” and that “the choice of period, of the sample, and of the proxies, will often imply many degrees of freedom where one might almost get what one wants if one only tries hard enough!” Pritchett (2000) also argues for detailed case studies of particular countries and growth events. Levine and Renelt (1992) and Temple (2000) apply extreme-bounds analysis to show that the results of cross-country growth regressions are not robust to even small changes in the conditioning information set (i.e., right-hand side variables).

Focusing on identification issues, cross-country studies suffer from two major weaknesses: reverse causality (that is, liberalized trade causes higher economic growth as opposed to more trade being the result of economic growth) and endogeneity (e.g., country-specific omitted characteristics affecting both openness and growth). Dealing with regressor endogeneity has triggered a substantial amount of interest in the use of instrumental variables (IV). This family of models suggests using regressors that have an impact on openness, but are uncorrelated with income. Using gravity models, Frankel and Romer (1999) and Irwin and Tervio (2002) find a positive effect running from trade to growth by isolating geographical components of openness that are assumed independent of economic growth, including population, land area, borders, and distances. But even these presumably exogenous instruments could have indirect effects on growth, thereby biasing the estimates.2 Dollar and Kraay (2003) suggest estimating the regressions in differences and using lagged openness as instrument. However, the simultaneity bias in the trade-growth context could extend over time—trade today may depend on growth tomorrow via imports for investment purposes—and using lagged variables as instruments is unlikely to fully correct for the bias. As an alternative approach to classic IV, Lee, Ricci, and Rigobon (2004) use identification through heteroskedasticity in a panel framework, and find that openness has a small, positive, but not particularly robust effect on growth. They have to rely, however, on the non-testable assumption that the structural shocks in the system of simultaneous equations are uncorrelated.

Another strand in the trade and growth literature seeks to improve upon cross-country regressions by employing panel methods, geared at controlling for time-invariant unobservable country effects. An early example is Harrison (1996), who uses fixed-effect estimators and finds a stronger impact of various openness indicators in a panel set-up compared to standard cross-country regressions. Wacziarg and Welch (2003) further the discussion in the literature in three directions: they update, expand, and correct the trade openness indicator in Sachs and Warner (1995); they show that the Sachs and Warner (1995) results of a positive effect of trade on growth break down if extended to the 1990s in a cross-sectional set-up; and they provide evidence in a panel context that, even in the 1990s, there is a positive effect of trade on growth when the analysis is limited to within-country effects.3 Slaughter (2001) uses a difference-in-differences approach to infer the effect of four very specific trade liberalization events on income growth dispersion, and finds no systematic link between trade liberalization and per capita income convergence. Giavazzi and Tabellini (2005) also apply a difference-in-differences approach to study the interactions between economic and political liberalizations. They find a positive and significant effect of economic liberalization on growth, but they claim that this effect cannot be entirely attributed to international trade, as liberalizations tend to be accompanied by other policy improvements.

B. Empirical Studies Applying Matching Estimators to Macro Data

A limited, but growing, strand of aggregate empirical literature—particularly in political economics—apply microeconometric estimators developed in the treatment evaluation literature to cross-country data, in order to overcome the weaknesses of OLS in cross-sectional set-ups. Persson and Tabellini (2005) use propensity-score matching methods to estimate the effects of political institutions (proportional against majoritarian electoral rule; presidential against parliamentary regime) on a set of relevant economic variables. Edwards and Magendzo (2003) apply matching estimators to analyze the macroeconomic record of dollarized economies. Atoyan and Conway (2006) use matching estimators to evaluate the impact of IMF programs.

All these studies point to the fact that non-parametric (or semi-parametric) matching estimators allow the OLS linearity assumption to be relaxed. This is not their only merit, however, since the linearity assumption can be also relaxed in the OLS set-up by specifying a fully saturated model. The major advantage of matching techniques is that they allow the researcher to carefully check for the existence of a common support in the distributions of treated and control units across covariates. This advantage can be even greater in a small sample of countries, since the “matched” treated and control units can be easily identified. The “transparency” attribute of matching estimators is described and exploited in Section IV with respect to the estimated effect of trade openness on growth.

III. Data and Variables of Interest

Under the trade and growth umbrella, a whole set of relationships have been analyzed in the literature. As the dependent variable, GDP levels, changes, GDP per capita, and relative incomes (or dispersion thereof) have been used as outcome measures, mainly to distinguish between level, growth, and convergence effects. We employ the difference of (log) per capita GDP, as we are interested in the dynamic impact of trade openness over time, not only in its one-off effects on the individual income level.

For trade and openness, two major groups of indicators have emerged in the literature, addressing somewhat different questions. On the one hand, some studies use simple measures of trade volumes that are particularly subject to endogeneity problems (especially if normalized by GDP), and have in fact been used especially within an IV framework (e.g., Frankel and Romer, 1999). On the other hand, there have been repeated efforts to identify the impact of trade policy and lower trade barriers on economic growth. To this end, a variety of indicators have been constructed, the most notable among them being the binary indicator by Sachs and Warner (1995), extended, updated, and revised by Wacziarg and Welch (2003); short SWWW.4 According to this indicator, a country is considered closed to international trade in any given year if at least one of the following conditions is satisfied: (i) average tariffs exceed 40 percent; (ii) non-tariff barriers cover more than 40 percent of its imports; (iii) it has a socialist economic system; (iv) the black market premium on the exchange rate exceeds 20 percent; and (v) much of its exports are controlled by a state monopoly. A country is open if none of these conditions applies. As our binary indicator of openness—or economic liberalization in the language of Giavazzi and Tabellini (2005)—we use the SWWW trade openness policy dummy. In Section V, while applying synthetic control methods in a panel set-up, in line with Giavazzi and Tabellini (2005), we refer to the “treatment” as the event of becoming open, after being closed in the preceding year according to this indicator. Our treatment thus intends to capture policy changes that reduce the constraints on market operations below a critical threshold along these five dimensions.5

To anchor our results in the existing literature, we draw on two data sets used recently in a related context. Vamvakidis (2002) presents historical evidence of the connection between openness and growth over the period 1870-1990; we focus on the post-1950 part of his data set.6 The data set consists of repeated country cross-sections for the periods 1950-70, 1970-90, and 1990-98. Besides the average GDP per capita growth and the openness dummy, the data set contains information on the initial GDP, investment share, population growth, secondary school enrollment, inflation, and black market premium.

The other data set we use has been analyzed in Giavazzi and Tabellini (2005) and Persson and Tabellini (2006). Of this very rich panel data set covering about 180 countries over the period 1960–2000, we use annual observations only for a few variables that are related to the question at hand: the updated SWWW, the log change in per capita GDP, and the same control variables mentioned above (with the only two exceptions that inflation is not reported, while a democracy dummy is present). In the context of synthetic control methods (see Section V), we extend the outcome variable (GDP per capita) to 2005 where available, drawing on the International Monetary Fund’s World Economic Outlook database. By doing so, we gain a few more observations to compare outcomes in treated and control countries, which is particularly important for countries that only liberalized recently, such as the transition economies.

IV. Cross-Country Analysis and Matching Estimators

A. Methodology

The common aim of most of the empirical studies reviewed in Section II is to assess whether a pro-openness trade policy has a causal effect on either the level or growth rate of GDP. This problem of inference involves “what if” statements and thus counterfactual outcomes. Hence, it can be translated into a treatment-control situation and analyzed within Rubin’s (1974) potential-outcome framework for causal inference. The essential feature of this approach is to define the causal effect of interest as the comparison of the potential outcomes for the same unit measured at the same time: Y(0) = (the value of GDP growth Y if the country is exposed to treatment T = 0, i.e., if it is closed to trade), and Y(1) = (the value of GDP growth if the same country is exposed to treatment T = 1, i.e., it is open to trade). Only one of these two potential outcomes can be observed—specifically, the one corresponding to the treatment the country received—but the causal effect is defined by their comparison, i.e., Y(1) – Y(0). This highlights that the estimation of the causal relationship between T and Y is hampered by a problem of missing data—i.e., the counterfactual outcomes Y(0) for open countries and Y(1) for closed countries.

In this setting, the aim of statistical analysis is usually that of estimating some features of the distribution of Y(1) – Y(0), like

E[Y(1)Y(0)],(1)

which is called the Average Treatment Effect (ATE). Alternatively, one can be interested in the average treatment effect for the subpopulation of the treated observations:

E[Y(1)Y(0)|T=1],(2)

which is called the Average effect of Treatment on the Treated (ATT). In the present context, the ATE corresponds to the counterfactual question: what would have been the growth rate of the countries in our sample, had they decided to switch their trade regime? On the contrary, the ATT focuses on the counterfactual question for treated units only: what would have been the growth rate of open countries, had they decided to close their economies?

Problems for the identification of these average treatment effects may arise from the existence of country-specific unobservables affecting both the two potential outcomes (or just one of them) and the treatment indicator. The fact that the treatment might be endogenous reflects the idea that the outcomes are jointly determined with the treatment, or that there are omitted confounders related to both the treatment and the outcomes. One of the assumptions that allows the identification of the ATE is the “unconfoundedness” condition, also referred to as “selection on observables” or “conditional independence assumption,” which is the rationale behind common estimation strategies such as regression modeling and matching.7 This assumption considers the conditioning set of all relevant pre-treatment variables X and assumes that:

Y(1),Y(0)T|X(3)
0<Pr(T=1|X)<1.(4)

That is, conditioning on observed covariates X, the treatment assignment is independent of potential outcomes.8 Unconfoundedness says that treatment assignment is independent of potential outcomes after accounting for a set of observable characteristics X. In other words, exposure to treatment is random within cells defined by the variables X.

Under unconfoundedness, one can identify the ATE within subpopulations defined by X:

E[Y(1)Y(0)|X]=E[Y(1)|T=1,X]E[Y(0)|T=0,X],(5)

and also the ATT as:

E[Y(1)Y(0)|T=1,X]=E[E[Y(1)|T=1,X]E[Y(0)|T=0,X]|T=1],(6)

where the outer expectation is over the distribution of X in the subpopulation of treated units. In other words, thanks to unconfoundedness, one can use the observed outcome of treated (control) units, conditional on X, to estimate the counterfactual outcome of control (treated) units.

An implication of the above results is that, if we could divide the sample into cells determined by the exact values of the variables X, then we could just take the average of the within-cell estimates of the average treatment effects. Often the variables X are continuous, so that smoothing techniques are needed; under unconfoundedness several estimation strategies can serve this purpose. Regression modeling and matching are viable alternatives, which thus rely on the same identification condition. The main advantage of matching with respect to linear regression is that the latter obscures information on the distribution of covariates in the two treatment groups. In principle, one would like to compare countries that have the same values of all covariates; unless there is a substantial overlap on the two covariates distributions, with a regression model one relies heavily on model specification—i.e., on extrapolation—for the estimation of treatment effects. It is thus crucial to check how much the distributions of the treated and control units overlap across covariates, and which is the region of common support for the two distributions.

Differently from other studies that apply the propensity-score version of matching to macro data—see, e.g., Persson and Tabellini (2003)—we implement the above strategy by using the “nearest neighbor” algorithm for covariate matching.9 Matching estimators impute the country’s missing counterfactual outcome by using average outcomes for countries with “similar” values of the covariates. The nearest neighbor algorithm uses the following simple approach to estimate the pair of potential outcomes. The potential outcome associated to the treatment that country A received is simply equal to the observed outcome of A. The potential outcome associated to the treatment that country A did not receive is equal to the outcome of the nearest country that received the opposite treatment (country B), where “nearest” means that the vector of covariates of B shows the smallest distance from the vector of covariates of A according to some predetermined distance measure.

Formally, define ǁxǁV = (x′Vx)1/2 as the vector norm with positive definite weight matrix V, and let ǁxzǁV be the distance between vectors x and z.10 Let d(i) be the smallest distance from the covariates of country i, Xi, with respect to the covariates of all other countries with the opposite treatment. Allowing for the possibility of ties, define J(i) as the set of indices for the countries that are at least as close to country i as its nearest neighbor:

J(i)={k=1,,N|Tk=1Ti,||Xk  Xi||V=d(i)}.(7)

The pair of potential outcomes for country i are estimated as:

Y^i(l)=Yiif Ti=l(8)
Y^i(l)=1#J(i)kJ(i)Ykif Ti=1l,(9)

where #J(i) is the numerosity of the set J(i). The ATE and ATT are thus estimated as:

τATE=1Ii=1I[Y^i(1)Y^i(0)](10)
τATT=1ITi:Ti=1[YiY^i(0)],(11)

where I and It are the sample size and the number of treated countries, respectively. These nearest-neighbor matching estimators both allow for the identification of the ATE and ATT under unconfoundedness and are very transparent, as the list of country matches underlying the results can be displayed in small samples (see the next two subsections).

Summing up, the application of matching estimators to (small) cross-country samples comes with a disadvantage and an advantage. The disadvantage is that unconfoundedness is very unlikely to hold, since it is often implausible to assume that country-specific unobservable characteristics do not play a role in treatment assignment. The advantage is that it allows one to transparently check for the existence of common support. Consequently, matching estimators are not used in this section as a magic bullet able to produce more reliable estimates than regression, since both estimation strategies rest on the same identification condition and are therefore subject to the same specification problems. They are used to highlight the country comparisons that lie behind cross-sectional results, to assess their plausibility, and to check whether the treated and control countries share a common support. After these steps, the cross-sectional results are improved by restricting the estimates to the region of common support. Even though these refined results must also rely on the conditional independence assumption, its plausibility can be further assessed by a careful inspection of the new country matches produced by the nearest neighbor algorithm.

B. The Unbearable Lightness of Cross-Country Estimates

We now turn to the data sets introduced in Section III and apply matching estimators to shed light on the country comparisons underlying the coefficient estimates. In this subsection, we analyze the data sets in a cross-sectional fashion.

Table 1 presents results for the Vamvakidis (2002) data set. We confirm his results that openness—as represented by the Sachs-Warner (1995) dummy—has a significant effect on growth after 1970, but not before. The coefficients indicate that an open country grows, on average, by 1.5–2.0 percentage points per year faster than a closed economy. The results for both types of matching estimates, ATE and ATT, are qualitatively and quantitatively similar to the standard OLS results.11 The estimates are robust to the introduction of regional dummies among control variables. Unfortunately, the data set comes with several drawbacks: (i) the data are pooled for 20-year intervals; (ii) the information stops in 1998, too early to meaningfully capture the countries of the former Soviet Union territory; and (iii) the sample size is very small—mainly OECD and Latin American countries—in the 1950s and 1960s.

Table 1.

Openness and Growth, Cross-Country Evidence (I), 1950-98

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Data: Vamvakidis (2002). Dependent variable: real GDP per capita growth. Treatment: trade openness dummy (Sachs and Warner, 1995). Control variables as understood in Vamvakidis (2002): initial GDP per capita, secondary school enrollment, population growth, investment share, black market premium, and inflation for 1990-98 and 1970-90; initial GDP per capita, illiteracy rate, population growth, and investment share for 1950-70. Area dummies refer to Africa, Asia, Latin America, Middle East, OECD, and transition economies. ATE and ATT stand for Average Treatment Effect and Average Treatment effect on the Treated, respectively. *** 1% significance level; ** 5% significance level; * 10% significance level.

In Table 2, we repeat the exercise switching to the Persson and Tabellini (PT) data set. This data set contains more countries over the whole sample and extends until 2000, using the Wacziarg and Welch (2003) update of the Sachs-Warner dummy. Although the data is in a panel format, we first produce a pooled estimate by decades for the whole data set. Again, the matching results are very similar to the OLS results, and we find a significant effect of trade on growth for the 1990s and 1970s. In these decades, open countries grew on average by 1.5–2.0 percentage points faster than closed countries, whether we control for regional dummies or not. The growth effect of openness is not significantly different from zero in the 1980s and 1960s.

Table 2.

Openness and Growth, Cross-Country Evidence (II), 1961-2000

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Data: Persson and Tabellini (2006). Dependent variable: real GDP per capita growth. Treatment: trade openness dummy (Sachs and Warner, 1995; Wacziarg and Welch, 2003). Control variables: initial GDP per capita, secondary school enrollment, population growth, and investment share. Area dummies refer to Africa, Asia, Latin America, Middle East, OECD, and transition economies. ATE and ATT stand for Average Treatment Effect and Average Treatment effect on the Treated, respectively. *** 1% significance level; ** 5% significance level; * 10% significance level.

So far, matching does not add anything to OLS results, since the estimates are very similar and based on the same identification assumption. We now turn to the transparency advantage of the nearest neighbor matching estimator to reveal the country comparisons underlying the estimates from the PT data set. Tables 3, 5, 7, and 9 display the full list of treated (i.e., open to trade for more than half of the decade) countries and their nearest neighbors in the ATE estimation for the 1990s, 1980s, 1970s, and 1960s, respectively. Tables 4, 6, 8, and 10 display the full list of control (i.e., closed) countries and their nearest neighbors in the ATE estimation for the 1990s, 1980s, 1970s, and 1960s, respectively. In all of these tables, the first column (Country) indicates the country under consideration; the second column (Baseline) shows the nearest neighbor used to estimate the counterfactual outcome of the country in the first column for the ATE estimation without area dummies; the third column (Area) shows the nearest neighbor used to estimate the counterfactual outcome of the country in the first column for the ATE estimation with area dummies. For example, the Baseline matches in Tables 3 and 4 for the 1990s are the country comparisons underlying the 1.505 coefficient in Table 2 (i.e., the effect of openness on growth without controlling for area dummies), while the Area matches in the same tables lie behind the 1.318 coefficient in Table 2 (i.e., the effect of openness after controlling for area dummies).

Table 3.

Cross-Country Matches, Treated Countries, 1991-2000

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Data: Persson and Tabellini (2006). Baseline and Area refer to the nearest-neighbor match without and with area dummies, respectively (see Table 2). Refined refers to nearest-neighbor match without Latin America and OECD (see Table 11). C.A.R. and P.N.G. stand for Central African Republic and Papua New Guinea, respectively.
Table 4.

Cross-Country Matches, Control Countries, 1991-2000

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Data: Persson and Tabellini (2006). Baseline and Area refer to the nearest-neighbor match without and with area dummies, respectively (see Table 2). Refined refers to nearest-neighbor match without Latin America and OECD (see Table 11). C.A.R. and P.N.G. stand for Central African Republic and Papua New Guinea, respectively.
Table 5.

Cross-Country Matches, Treated Countries, 1981-90

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Data: Persson and Tabellini (2006). Baseline and Area refer to the nearest-neighbor match without and with area dummies, respectively (see Table 2). Refined refers to nearest-neighbor match without Latin America and OECD (see Table 11).
Table 6.

Cross-Country Matches, Control Countries, 1981-90

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Data: Persson and Tabellini (2006). Baseline and Area refer to the nearest-neighbor match without and with area dummies, respectively (see Table 2). Refined refers to nearest-neighbor match without Latin America and OECD (see Table 11). C.A.R. and P.N.G. stand for Central African Republic and Papua New Guinea, respectively.
Table 7.

Cross-Country Matches, Treated Countries, 1971-80

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Data: Persson and Tabellini (2006). Baseline and Area refer to the nearest-neighbor match without and with area dummies, respectively (see Table 2). Refined refers to nearest-neighbor match without Latin America and OECD (see Table 11).
Table 8.

Cross-Country Matches, Control Countries, 1971-80

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Data: Persson and Tabellini (2006). Baseline and Area refer to the nearest-neighbor match without and with area dummies, respectively (see Table 2). Refined refers to nearest-neighbor match without Latin America and OECD (see Table 11). C.A.R. and P.N.G. stand for Central African Republic and Papua New Guinea, respectively.
Table 9.

Cross-Country Matches, Treated Countries, 1961-70

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Data:Persson and Tabellini (2006). Baseline and Area refer to the nearest-neighbor match without and with area dummies, respectively (see Table 2). Refined refers to nearest-neighbor match without Latin America and OECD (see Table 11).
Table 10.

Cross-Country Matches, Control Countries, 1961-70

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Data: Persson and Tabellini (2006). Baseline and Area refer to the nearest-neighbor match without and with area dummies, respectively (see Table 2). Refined refers to nearest-neighbor match without Latin America and OECD (see Table 11). C.A.R. and P.N.G. stand for Central African Republic and Papua New Guinea, respectively.

Browsing through the above tables, one can see that a few Baseline matches appear to work reasonably “well”—for example in the 1990s for Bulgaria and Egypt, which are matched with Ukraine and Algeria, respectively. Arguably, this intuitive appreciation is based on the implicit assumption that there are region-specific unobservable effects; for example a common language, colonization, level of development, geographic proximity, or legal origin. For others—e.g., Albania and Sri Lanka, which are matched with Central African Republic and Algeria, respectively—the matches are somewhat less meaningful. In particular, all (treated) developed countries give rise to very poor matches (e.g., Italy and UK with Russia, or US and Canada with China). In other words, most of the baseline matches do not appear robust to area-specific unobservables.

Therefore, we construct country groups that may capture some of these area-specific unobservables. We divide the world into six groups: Africa, Asia, Latin America, Middle East, OECD, and transition economies (where OECD participation takes precedence over geographic region).12 The matches underlying the estimation with these area dummies are reported in the Area column. For Albania and Sri Lanka in the 1990s, this step appears to work reasonably well, as they are now matched with Belarus and Pakistan, which are certainly perceived as more similar than the baseline nearest neighbors. There are, however, certain surprising findings: for example, all OECD members are matched with Iceland! A similar result obtains for Latin America, where Venezuela is the only control that is picked to be a match. This is due to the fact that Iceland and Venezuela are, according to the SWWW classification, the only closed economies in the OECD group and Latin America in the 1990s.13 In other words, there is no common support between treated and control countries in those two regions. Introducing area dummies is not enough to control for area-specific unobservables, unless there is a sufficient overlap of treated and untreated units in all areas.

Summing up, the matches listed in the Baseline and Area columns of Tables 3 through 10 show that country comparisons underlying cross-country analysis are often more than far-fetched. This unbearable lightness of cross-country analysis extends from matching to other cross-sectional estimators that rely on the unconfoundedness assumption, such as plain regression modeling. This is due to the fact that OLS estimates are based either on the same implicit but far-fetched country comparisons or—even worse—on parametric extrapolation beyond the region of common support. In fact, if treated and control countries are very different from each other with respect to covariates, the OLS estimate of the counterfactual outcome of the treated is constructed by linearly extrapolating the observed outcome of control units, and vice versa.

C. Refined Evidence in Selected Regions

The above discussion shows that—as long as we want to control for area-specific unobservable characteristics—we should restrict the analysis of the trade-growth nexus to regions with enough treatment variation. In other words, to improve the quality of the country matches underlying the results, we should drop regions with no common support between treated and control units.

In Table 11, we re-estimate the pooled specification eliminating countries that lack common support with respect to regional affiliation. As shown in the Appendix, this is true in the 1990s for the OECD and Latin America. The same holds for other regions and other decades, however: in the 1980s, almost all OECD countries are already open. In the 1970s and 1960s, almost all African economies (except Mauritius in the 1970s) are closed according to the SWWW dummy. The OECD is a borderline case in both decades, with 4 out of 25 countries in the sample closed in the 1970s and 5 out of 26 countries closed in the 1960s. For both decades, we show estimates with and without the OECD.

Table 11.

Openness and Growth, Refined Evidence (I), 1961-2000

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Data: Persson and Tabellini (2006). Dependent variable: real GDP per capita growth. Treatment: trade openness dummy (Sachs and Warner, 1995; Wacziarg and Welch, 2003). Control variables: initial GDP per capita, secondary school enrollment, population growth, investment share, and area dummies (as indicated). The two numbers in parenthesis after each area refer to the number of treated and control countries, respectively. Samples restricted to certain areas to meet the common-support condition. ATE and ATT stand for Average Treatment Effect and Average Treatment effect on the Treated, respectively. *** 1% significance level; ** 5% significance level; * 10% significance level.

Dropping the above regions does not appear to systematically reduce the explanatory power of the models (as measured by the adjusted R-square). Table 11 reports matching estimates—of both the ATE and ATT—restricted to countries that meet the common-support condition for geographic areas. Comparing these estimates to the previous ones for the unrestricted sample (Table 2), the coefficients appear to be slightly more significant and also larger in magnitude in the 1990s and 1970s. Moreover, we now find stronger evidence of a marginally significant positive effect of openness on growth in the 1980s, especially for the countries that were open to trade (ATT estimate). All the estimated effects lie in the 1.5–2.5 percentage points range. For the 1960s, again, the coefficients are never significantly different from zero. The Refined column in Tables 3 through 10 reports the country matches underlying these results. Counter-intuitive matches are now considerably reduced.

We conclude from this exercise that it is important to check for the existence of common support. In fact, in small samples of countries, the advantage of matching estimators lies in the guidance for appropriately restricting the analysis to specific subsamples. Unlike the estimates in Table 2—which replicate common results from growth regressions in the literature—the estimates presented in Table 11 fully control for area-specific unobservables and are based on more intuitive country comparisons. There is no free lunch, however, as the external validity of the estimates is now reduced. The results recommend refraining from commenting on the effect of trade openness on growth in developed countries, Africa in the 1960s and 1970s, and Latin America in the 1990s.

The estimates in Table 11 control for the existence of common support with respect to a set of covariates that we deem important to capture unobservable regional characteristics associated to geography, level of development, culture, or legal origins—that is, area dummies for Africa, Middle East, Asia, Latin America, transition economies, and OECD. The common support, however, should be checked also for other covariates. In principle, we would like to match countries that are very similar with respect to all covariates, but this is impossible if treated and control units are not evenly distributed across all the ranges of variation of covariates. Figures 1 through 8 show that, for example, this condition is not often met for investment share and secondary school enrollment. These figures report the kernel density of treated and control countries over the ranges of variation of these two variables. For instance, Figure 5 shows that the common support for investment share in the 1970s ranges from 0.11 to 0.39, with 27 (control) countries below this region and 1 (treated) country above. To meet the common-support condition, these 28 countries should be dropped from the estimation sample.

Figure 1.
Figure 1.

Common support for investment share, 1991-2000

Data: Persson and Tabellini (2006). Treated countries: 87. Control countries: 26. All countries in common support.

Citation: IMF Working Papers 2007, 156; 10.5089/9781451867206.001.A001

Figure 2.
Figure 2.

Common support for secondary school enrollment, 1991-2000

Data: Persson and Tabellini (2006). Treated countries: 87. Control countries: 26. Common support: (0, 104). Countries above common support: 14 treated.

Citation: IMF Working Papers 2007, 156; 10.5089/9781451867206.001.A001

Figure 3.
Figure 3.

Common support for investment share, 1981-90

Data: Persson and Tabellini (2006). Treated countries: 43. Control countries: 66. Common support: (0.05, 0.26). Countries above common support: 10 treated. Countries below common support: 6 controls.

Citation: IMF Working Papers 2007, 156; 10.5089/9781451867206.001.A001

Figure 4.
Figure 4.

Common support for secondary school enrollment, 1981-90

Data: Persson and Tabellini (2006). Treated countries: 43. Control countries: 66. Common support: (11, 96). Countries above common support: 11 treated. Countries below common support: 11 controls.

Citation: IMF Working Papers 2007, 156; 10.5089/9781451867206.001.A001

Figure 5.
Figure 5.

Common support for investment share, 1971-80

Data: Persson and Tabellini (2006). Treated countries: 33. Control countries: 74. Common support: (0.11, 0.39). Countries above common support: 1 treated. Countries below common support: 27 controls.

Citation: IMF Working Papers 2007, 156; 10.5089/9781451867206.001.A001

Figure 6.
Figure 6.

Common support for secondary school enrollment, 1971-80

Data: Persson and Tabellini (2006). Treated countries: 33. Control countries: 74. Common support: (23, 85). Countries above common support: 11 treated. Countries below common support: 38 controls.

Citation: IMF Working Papers 2007, 156; 10.5089/9781451867206.001.A001

Figure 7.
Figure 7.

Common support for investment share, 1961-70

Data: Persson and Tabellini (2006). Treated countries: 31. Control countries: 75. Common support: (0.11, 0.35). Countries above common support: 4 treated. Countries below common support: 32 controls.

Citation: IMF Working Papers 2007, 156; 10.5089/9781451867206.001.A001

Figure 8.
Figure 8.

Common support for secondary school enrollment, 1961-70

Data: Persson and Tabellini (2006). Treated countries: 31. Control countries: 75. Common support: (15, 77). Countries above common support: 5 treated. Countries below common support: 45 controls.

Citation: IMF Working Papers 2007, 156; 10.5089/9781451867206.001.A001

Table 12 reports matching estimates for samples restricted to the regions of common support identified in Figures 1 through 8. This evidence is consistent with the one described in Table 11. When carefully matching only countries that lie in the common support, cross-sectional estimates detect a positive and significant association between openness and growth in the 1970s, 1980s, and 1990s, but not in the 1960s.

Table 12.

Openness and Growth, Refined Evidence (II), 1961-2000

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Data: Persson and Tabellini (2006). Restricted samples to meet the common-support condition for investment share (A), secondary school enrollment (B), or both (C). See Figures 1 through 8 for the numbers of treated and control countries dropped because outside of common supports. Dependent variable: real GDP per capita growth. Treatment: trade openness dummy (Sachs and Warner, 1995; Wacziarg and Welch, 2003). Control variables: initial GDP per capita, secondary school enrollment, population growth, investment share, and area dummies. ATE and ATT stand for Average Treatment Effect and Average Treatment effect on the Treated, respectively. *** 1% significance level; ** 5% significance level; * 10% significance level.
Table 13.

Economic Growth Predictor Means in the Pre-Treatment Period

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