Trade Openness and Financial Development in the New EU Member States: Evidence from a Granger Panel Bootstrap Causality Test

ABSTRACT

The goal of this paper is to investigate the causality between trade openness and financial development in 11 new member states in the European Union. We employ a Granger bootstrap panel approach based on seemingly unrelated regressions, which accounts for cross-sectional dependence and slope heterogeneity among the countries in the panel. The main findings are as follows. First, the test results of the finance-trade nexus are country specific. Second, statistically significant causality is found from trade to finance in eight countries (Bulgaria, Estonia, Hungary, Latvia, Lithuania, Poland, Romania, and Slovenia). As the regression coefficients are predominantly negative, the demand-following hypothesis on the finance-trade nexus is not supported in the majority of the countries. Third, finance is found to be a statistically significant Granger cause of trade in six countries (Croatia, Estonia, Latvia, Lithuania, Poland, and the Slovakia), and in four of them (the smaller ones: Croatia, Estonia, Latvia, Lithuania), the regression coefficients take positive signs, which support the supply-leading hypothesis.

KEYWORDS:

• Bootstrap panel-data approach
• financial development
• Granger causality
• trade-finance nexus
• trade openness

JEL CLASSIFICATION:

• E44
• F40
• C33

Acknowledgments

The authors thank the participants in the twelfth Professor Aleksander Zelias International Conference on Modeling and Forecasting of Socio-Economic Phenomena, Zakopane, May 8–11, 2018, and in the Workshop on Macroeconomic Research, Cracow, June 26–27, 2018, for their useful comments and suggestions on a draft of this paper.

Disclosure statement

No potential conflict of interest was reported by the authors.

Notes

1. The Monte Carlo experiment carried out by Pesaran (2006) shows the importance of testing for cross-sectional dependence in a panel-data study and illustrates substantial bias and poor control over the type I error rate when cross-sectional dependence is ignored. To put it differently, it is highly likely that any causality testing that ignores cross-sectional dependence is unreliable.

2. In practice, the assumption that the slope coefficients are homogeneous is unlikely to hold because the stage of development differs across countries. Furthermore, in a panel causality analysis, imposing homogeneity among the slope coefficients over the entire panel is a strong null hypothesis (Granger 2003), which can mask the country-specific characteristics.

3. Pesaran (2004) shows that the CD test has a mean of zero for fixed $T$ and $N$ and is robust to heterogeneous dynamic models, including multiple breaks in slope coefficients and/or error variances, so as long as the unconditional means of the dependent and independent variables are time invariant and their innovations have symmetric distributions. However, the $CD$ test lacks power in certain situations in which the population average pair-wise correlations are zero, but the underlying individual population pair-wise correlations are non-zero (Pesaran, Ullah, and Yamagata 2008).

4. Cross-sectional dependence tests rejected the null hypothesis at 10% for two of them.

5. This is important because using the levels of the variables directly in the empirical analysis can play a crucial role in determining causal linkages because differencing variables to make them stationary can lead to a loss in the trend dynamics of the series (Clarke and Mirza 2006).

6. According to Estima (2018): “Despite there being quite a few usages of this in the literature, it is simply bad statistics. In short, it tests for causality by adding an ‘extra’ lag to a VAR and then tests zero restrictions which don’t include those added lags. This does provide a test which (under the null) will have the correct asymptotic distribution since it doesn’t test all the lags of the non-stationary variable. However, it’s not a test of Granger causality (which requires testing all lags). By adding extra lags and then not testing them, the bad behavior is shifted onto the untested lags. It will suffer badly from lack of power since, if the coefficients aren’t, in fact, zero, the ‘causality’ will get shifted fairly easily to the untested lag(s) since an integrated process is so highly autocorrelated.”

7. $p_i$ (for $i=1,\dots 6$) in Equations (11) and (12) denotes number of lags.

8. These equations, described in Equations (11)–(12), are not the VAR (Vector Autoregression Model) but the SUR systems (Kónya 2006).

9. In many studies that employ Konya’s method, the optimum number of lags is selected guided by the AIC (Akaike Information Criterion) or BIC (Bayesian Information Criterion). These studies typically consider countries with a considerably longer available time series. This data-rich environment allows authors to fully investigate the number of lags. In our case, if we wanted to include three lags, we would have models with more parameters than data. Taking two lags brings the total number of parameters below the number of data points, making models theoretically estimable but barely. These models would be plagued with collinearity issues and ill-conditioned matrices. A possible solution to these issues would be to use regularized estimation techniques, e.g., Lasso or Ridge estimators. Both would make models with two or three lags estimable. We would get parameter estimates but lose the ability to test statistical hypotheses, as these methods have unknown properties in this regard.