Abstract
Countries choose different strategies when responding to crises. An important challenge in assessing the impact of these policies is selection bias with respect to relatively time-invariant country characteristics, as well as time-varying values of outcome variables and other policy choices. This paper addresses this challenge by using propensity-score matching to estimate how major reserve sales, large currency depreciations, substantial changes in policy interest rates, and increased controls on capital outflows affect real GDP growth, unemployment, and inflation during two periods marked by crises, 1997–2001 and 2007–11. We find that none of these policies yield significant improvements in growth, unemployment, and inflation. Instead, a large increase in interest rates and new capital controls are estimated to cause a significant decline in GDP growth. Sharp currency depreciations may raise GDP growth over time, but only with a lagged effect and after an initial contraction.
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Notes
See Fischer (2004, Chapter 3).
Although the crises in the period from 1997 to 2001 were often more regional or country-specific in nature than during the later period (except perhaps during the fall of 2008 after the collapse of LTCM), both crisis windows are periods of volatility in global capital flows punctuated by sudden stops. Claessens and others (2014) present a wide-ranging analysis and overview of financial crises, and the chapter by Claessens and Kose (2014) provides a detailed discussion of the different types of crises and patterns over time. Gourinchas and Obstfeld (2012) present an analysis of the causes and consequences of crises from 1973 to 2010.
This roughly corresponds to the tradeoffs countries face in the policy trilemma, as discussed in Obstfeld, Shambaugh, and Taylor (2010); Dominguez (2013); and Klein and Shambaugh (2013). As with the policy trilemma, we do not consider fiscal policy responses since these are less nimble and generally take longer to implement. We also do not analyze fiscal policy responses as these are discussed in detail in Chari and Henry (2015), as part of the series of papers for this conference.
In the section “An overview of propensity-score methodology,” we discuss the methodology in more detail and the differences between the propensity-score matching methodology and the standard multivariate regression analysis.
Three exceptions are Glick, Guo, and Hutchison (2006); Das and Bergstrom (2012); and Forbes, Fratzscher, and Straub (2015).
Propensity-score matching does not directly control for endogeneity. This is a potential concern for the ATT statistic of the effect of the policy on the outcome variable in the quarter in which the policy is enacted. But the ATT statistics in the six subsequent quarters consider the effect of the policy on subsequent outcomes and do not have the same potential problem with endogeneity, especially given the exclusion restriction described below.
The countries are listed in the Appendix and include all “Advanced Economies” (as defined by the International Monetary Fund as of October 2012) and all “Emerging Markets” and “Frontier Economies” (as defined by Standard & Poor’s BMI indices). Countries in this list are included in the final analysis if data on all four of the policy responses is available. Details on sources and definitions for the data are in the Appendix.
There are a variety of ways to measure reserve loss in order to obtain an indicator of a “major” change; for example, in an earlier version of this paper we considered a threshold change in reserves combined with a requirement that reserves-to-GDP meet or exceed a minimum level (there were 52 instances of large reserve losses using that method, vs. 62 with our current method). We have chosen our current approach because GDP is an appropriate variable for directly scaling reserves. But, as with any approach, there are potential concerns; for example, the percentage change in reserves-to-GDP could be large and negative (and count as a major reserve loss) if GDP growth is especially large and reserves are not repleted (this is the case in about 8 of the 62 instances of major reserve loss). Also, we would not count as a major reserve loss an instance where there is a large drop in reserves in a time when GDP growth has a large negative value (although given that we have more instances of major reserve loss with this method than with our former approach, this might not be an important concern).
The policy interest rate is the interest rate related to monetary policy for each country. If the policy rate is not available, we use the short-term interest rate. Interest rate information is from Global Insight, accessed 10/1/13.
The data on capital controls is from an expanded version of the data set in Klein (2012), and we use his approach of including changes in controls on all asset categories except foreign direct investment. This measure of capital controls (as well as most others) only captures when a new control is first added or removed, and not any subsequent modifications to the specific control.
We count a control as being put in place in the third quarter of the year.
Only countries with information for all four policy responses for each year in the given crisis period are included in these figures, so that the sample of countries is constant across time within each graph (although not across graphs). As a result, the incidence of the use of each policy differs relative to Table 1(a) and (b). In these graphs, the episodes are converted from a quarterly frequency to an annual frequency.
The VXO is the Volatility Index calculated by the Chicago Board Options Exchange and is similar to the VIX (with a correlation of 99 percent), except the VIX is only available starting in 1990. The U.S. interest rate is the policy rate. The commodity price index is the Economist All-Commodity dollar index.
Capital flow data is from the data set created in Forbes and Warnock (2012) and from the IMF’s Balance of Payments. Private credit is measured by private credit by deposit money banks and other financial institutions to GDP and reported in Beck and others (2013). The commodity interaction term is defined as the product of the log of the commodity price index (defined above) multiplied by a dummy equal to 1 if a country is a major commodity exporter.
Institutions are measured using an index based on the ICRG measures of institutional quality compiled by the World Bank.
Details on the definitions and sources for all of these variables are available in the appendix.
See Heinrich, Maffioli, and Vázquez (2010). Including irrelevant variables will make it more difficult to satisfy the common-support condition, as explained below. The sensitivity analysis also reports results when the full set of covariates is included in the first-stage regression.
Even though the R 2 statistic is low in the probit explaining capital controls, statistics presented in Table 3 indicate that no variables fail the independence. If, in fact, the addition of capital controls is not correlated with other variables, then sample selection issues are less pronounced.
Propensity-score matching is discussed in Dehejia and Wahba (2002); Angrist and Pischke (2008, chapter 3); and Heinrich, Maffioli, and Vázquez (2010). Recent research in macroeconomics that has used this technique includes analyses of monetary policy (Angrist and Kuersteiner, 2011; Angrist, Jordá, and Kuersteiner, 2013; Ehrmann and Fratzscher, 2006), the effect of openness on growth (Das and Bergstrom, 2012), financial liberalization (Das and Bergstrom, 2012; and Levchenko, Rancière, and Thoenig, 2009), foreign ownership of firms (Chari, Chen, and Dominguez, 2011), the response of economies to crises (Glick, Guo, and Hutchison, 2006), fiscal policy (Jordà and Taylor, 2013) and the effects of capital controls and macroprudential measures (Forbes, Fratzscher, and Straub, 2015).
Angrist and Pischke (2008) show the full derivation of these equations. The observable outcomes are Y i =Y 0,i +(Y 1,i −Y 0,i )D i . The expected values conditional on D i are E[Y i |D i =1]=E[Y 1,i |D i =1], E[Y i |D i =0]=E[Y 0,i |D i =0], and E[(Y 1,i −Y 0,i )D i |D i =0]=0. Thus, E[Y 1,i |D i =1]−E[Y 0,j |D j =0]=E[Y 1,i −Y 0,i |D i =1]+E[Y 0,i |D i =1]−E[Y 0,i |D i =0].
In this discussion, to illustrate propensity-score matching, we focus on differences across countries and, for example, the vector X i for the ith country. Our empirical analysis focuses on differences across countries and across time, so that the appropriate vector is X i,j , representing variables’ values for the country i in year j. Thus, rather than pair a particular country with one or more other countries identified through propensity-score matching, we will pair a particular country-year observation with one or more other country-year observations.
Rubin and Thomas (1992) show that it is possible to estimate these propensity scores based on the vector of observable characteristics.
In our analysis, we consider the change in a variable (for example, GDP growth) before and after the treatment. For example, if G w,I,z =GDP growth for the ith observation which is either treated (w=1) or untreated (w=0), either after (z=After) or before (z=Before) the policy, we consider E[G 1,i,After −G 1,i,Before |D i =1]−E[G 0,i,After −G 0,i,Before |D i =0]. Following the algebra in Equation (2), and using matching to generate a probability function p(X) in order to select the untreated observations to compare with the treated observations, we can show that ATT=E[G 1,i,After |D i =1]−E[G 0,i,After |p(X),D i =1]−{E[G 1,i,Before |D i =1]−E[G 0,i,Before |p(X),D i =1]}. The term in curly brackets does not equal 0, even if GDP growth is one of the elements used in the p(X) function, because p(X) is matching country-year observations based on the likelihood of treatment, not the commonality of the outcome variable before the treatment (and, of course, the selection is for the same country-year observations for both the Before and After periods). Thus, in our analysis, the ATT consists of differences between GDP growth between the treated and control observations for both the periods before and after the treatment.
All these methods use the propensity score of each treated observation and propensity scores of untreated (control) observations. Nearest-neighbor selects the single control observation with the closest propensity score, and “without replacement” refers to the fact that any control observation can be matched to only one treated observation. Five-nearest neighbors uses more observations from the control group and allows replacement. The radius method includes all nearest neighbors within a maximum radius (referred to as the caliper). The kernel and local-linear matching algorithms each calculate a weighted average of all observations in the control group and assign higher weights (which differ between these two methods) to control observations closer to the treated observation. Nearest neighbor is straightforward, easy to implement, and minimizes bad matches with control observations that have little in common with the treated observation. It is also straightforward to check which country is matched as the nearest neighbor in a control group. But this method ignores useful information from other countries in the control group. Radius, kernel, and local-linear matching use more information and therefore tend to have lower variances, but at the risk of including bad matches. Radius matching is less sophisticated than kernel and local-linear matching since it does not place greater weight on closer matches. Local-linear matching has several advantages over kernel matching, such as a faster rate of convergence near boundary points and greater robustness to different data design densities.
Angrist and Pischke (2008, Chapter 3) and Imbens (2014) present excellent discussions of the similarities and differences between regression analysis and propensity-score matching, including their relative advantages.
This is one reason why propensity-score matching has been more widely adopted in labor economics, where papers often have larger samples of individuals that provide more degrees of freedom for effective matching.
Most papers using propensity-score matching have focused on the cross-section effects of policies and not included a time-dimension.
We apply these matching algorithms with the Stata module PSMATCH2, developed by Leuven and Sianesi (2003). The number of treated observations is lower than reported in Table 1(a) and (b) because data is not available for all of the covariates needed to estimate propensity scores for all observations.
The numbers in the treated group are less than the numbers in Table 1(a) and (b) because not all of the variables used in the logit regressions are available for all countries for all years.
As a robustness check, we also consider the ATT of GDP growth without reference to the pretreatment values; see the “Sensitivity tests: Real GDP growth without reference to pretreatment values.”. These results are very similar to the base case results presented in this section.
See Lechner (2002) for the appropriate methodology. We use 500 repetitions for the bootstrap.
Claessens and Kose (2014) discusses similarities and differences across crises.
Details on sources and definitions for the data are in the Appendix.
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Additional information
Supplementary information accompanies this article on the IMF Economic Review website (www.palgrave-journals.com/imfer)
The authors thank Rajeev Dehejia, Pierre-Olivier Gourinchas, Ayhan Kose, Jeffrey Sachs, anonymous reviewers at the IMF, and conference participants at the IMF for helpful comments. Patrick O’Halloran provided excellent research assistance.
*Kristin J. Forbes is the Jerome and Dorothy Lemelson Professor of Management and Global Economics at the Massachusetts Institute of Technology’s Sloan School of Management and a Research Associate at the National Bureau of Economic Research. Michael W. Klein is the William L. Clayton Professor of International Economic Affairs at the Fletcher School, Tufts University.
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Forbes, K., Klein, M. Pick Your Poison: The Choices and Consequences of Policy Responses to Crises. IMF Econ Rev 63, 197–237 (2015). https://doi.org/10.1057/imfer.2015.2
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DOI: https://doi.org/10.1057/imfer.2015.2