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This work was initiated as part of the Western Hemisphere Department’s Cluster Report on Trade Integration in Latin America and the Caribbean (IMF, 2017) led by Valerie Cerra. We are very grateful to Valerie Cerra and Martin Kaufman for continued support, and to Andrew Berg, Rupa Duttagupta, Stefania Fabrizio, Davide Furceri, Rahul Giri, Alessandro Giustiniani, Grace Li, Wojciech Maliszewski, Ali Mansoor, Brad McDonald, Neil Meads, Jacques Alain Miniane, Chris Papageorgiou, Cemile Sancak and Alasdair Scott for helpful comments and discussions. All remaining errors are ours.
Strategy, Policy, and Review Department.
Institute for Capacity Development.
The original results in Frankel and Romer (1999) were based on a limited dataset from 1985. In particular, the bilateral trade data underlying the construction of the instrument contained only 63 economies, and they used the estimated coefficients from this smaller sample to predict trade openness for the remaining countries. The same dataset seems to have been re-used in the subsequent literature (Hall and Jones, 1999; Rodriguez and Rodrik, 2001; Rodrik, Subramanian and Trebbi, 2004). Noguer and Siscart (2005) extended the country coverage to 97 economies, but still utilized only the 1985 cross section. In contrast, our bilateral trade data contain 147-173 countries depending on the year, and we only use a country in our income and inequality regressions if we have its reported bilateral trade flows.
Relatedly, Autor, Dorn and Hanson (2013) show that imports from China had large differential employment effects across U.S. commuting zones, where employment declined more in zones whose industries were more exposed to import competition from China. Note that this finding does not imply that trade integration was responsible for an increase in overall income inequality in the United States. To determine the aggregate inequality effects, one has to take into account the initial position of the affected workers in the income distribution.
Since the construction of the instrument relies on some time-invariant geographical characteristics, we can only use cross-sectional variation to identify the effects of trade.
To be precise, the problem of including internal trade lies in the fact that the concept is not as unambiguously defined as that of international trade. Every cross-border sale is international trade. Measuring internal trade requires some convention – it could be defined e.g. as all sales across domestic sectors as defined in input-output matrices, or all sales by firms (a superset of the sales considered in the input-output measure), etc. To the extent that domestic trade includes trade in intermediate inputs, these measures will differ and the choice of the unit of analysis (sector, firm, etc.) will thus be crucial.
Given the negative correlation between a country’s size and its proximity to other countries, the inclusion of a size measure Si in the estimation as in (4) is essential for Pi to be a valid instrument.
For our results where openness in goods and services is considered (using the goods-only instrument based on DOTS data), we rely on balance of payments data from the World Economic Outlook database.
This range of point estimates falls well within typical estimates found in the literature. For example, in their meta-analysis covering 1,467 estimates from 103 papers, Disdier and Head (2008) find a mean estimated elasticity of −0.9.
One should be cautious in interpreting changes in the estimated coefficients as generally the differences are not statistically significant. Moreover, the figures also show that the sample of countries changes over time because of data availability constraints. It is worth noting that the fall in the estimated coefficient towards the end of the sample period can be explained by cyclical developments. Countries with lower predicted trade openness tended to be less affected by the GFC (see e.g. exhibit 2 in Bernanke, 2009), so their relative income position improved. This effect appears to start fading towards the end of our sample in 2015.
Note that our openness measure is expressed in decimal form (for example, 20% openness is expressed as 0.2). Thus, an estimated coefficient
Since we always reject the null of underidentification, we do not report these statistics in the tables.
This is consistent with our discussion of Figure 8, where we concluded that gravity-predicted openness is very weakly correlated with the rule of law. Because of this weak association, the strength of the trade instrument does not change if we include the rule of law as an additional exogenous regressor.
Hall and Jones (1999) argue that distance from the equator is a good instrument for “social infrastructure” because it is correlated with the extent of Western European influence, which leads to good institutions. As we discussed earlier, distance from the equator is not a valid excludable instrument if it has a direct effect on economic performance through climate. Interestingly, Acemoglu, Johnson and Robinson (2001) find that “distance from the equator does not have an independent effect on economic performance, validating the use of this variable as an instrument in the work by Hall and Jones (1999)” (page 1373). In any case, our specification controls for the direct effect of climate through the inclusion of temperature, which greatly diminishes this concern. We note that even after controlling for size and temperature, the cross country partial correlation of distance from the equator and the rule of law is 0.33 (using 2013 values).
The results of the weak instrument tests with distance to the equator are overall similar to the case when we use settler mortality as an instrument for institutions. In most cases we can reject that the actual size of the t-test is bigger than 25%.