The Euro’s Effect on Trade
Tal Sadeh
Harold Hartog School of Government and Policy
& Department of Political Science,
Tel Aviv University
November 2013
Forthcoming in European Union Politics
ABSTRACT
This study argues that the euro area more than doubled trade among its members, but this
process was delayed and fitful. The estimates in this paper are close to those obtained by
Rose and Frankel in spite of using the methods developed by their critics. Furthermore,
the euro area has increased the trade of its Mediterranean members more than the trade of
other member states; it also raised trade with non-members by some 35 per cent. The
paper innovates mainly by using a more appropriate control group to the euro area and
better controls for the Single Market, estimating differences of trade, studying the effects
of the euro on different member states, using quantile regression, and naturally by using
more recent data.
KEYWORDS
Euro area; Single Market; Trade; Gravity Equation
Address: Department of Political Science, Tel Aviv University, P.O. Box 39040, Tel
Aviv 69978, ISRAEL.
Fax: (972) 3-640-9515.
E-mail address: [email protected]
Acknowledgements
For their useful criticisms, comments and suggestions, I thank the Editor and two anonymous
reviewers, as well as Eyal Argov, Alex Cukierman and other participants at the 2013 annual
meeting of the Israel Economic Association, Tel Aviv. Special thanks to Nizan Feldman for
sharing with me some of his data.
1 Introduction
The euro area is in crisis since 2010. As sovereign debts of member states spiral and an
increasing number of them have required bail outs critics pointed to the costs of this
project and raised doubts about the usefulness of a common currency in Europe. Many
scholars agree that the reasons for establishing Economic and Monetary Union (EMU)
have always been mainly political (Sadeh and Verdun, 2009). However, the economic
cost-benefit analysis remains important because it helps shape the political debate by
either putting a price tag on the project or showing it to pay for itself. After all, EMU
advocates have long promised economic gains from a single currency, and this promise
was important in gaining public support for the euro, at least until the current crisis. In
short, the economic cost-benefit analysis of the single currency is an important part of its
larger political-economic debate.
The costs of a single currency are mainly macroeconomic (giving up monetary
and exchange rate policy). The microeconomic benefits are expected mainly from
expanded trade. The classic Mundellian theoretical argument is that trade expands
following the elimination of the trade barrier inherent in exchange rate fluctuations and
currency conversion transaction costs. This is obvious enough as a direct effect, but there
should also be dynamic trade-enhancing effects to a currency union. First, in a globalized
world where components cross borders many times before being assembled and sold as a
final good, even a small reduction in transaction costs can increase trade flows nonlinearly. Second, by reducing collusion among competitors a currency union can
eliminate pricing mark-ups and enhance trade (Baldwin, 2006). Third, currency unions
can increase the number of firms engaged in international trade because they reduce the
2 fixed costs associated with this trade and allow smaller firms to participate, thus
increasing variety-driven trade (Melitz, 2003; Helpman et al., 2008; Baldwin, 2010).
This study focuses on the benefit side of the euro, arguing that the euro more than
doubled trade among the member states, and increased trade among the Mediterranean
countries more than among other member states; it also raised trade with non-members
by some 35 per cent. This effect is not observed in the euro’s early years, which helps
explain why it was difficult to detect so far. The estimates in this paper are compatible
with the variety trade argument, but in their magnitude are much closer to the estimates
found in the works of Andrew Rose and Jeffrey Frankel (see next section) than to the
estimates found by their critics, even when the methods developed by the critics are used.
The paper innovates over the existing literature on the euro’s trade effects by
simultaneously using a more appropriate control group to the euro area, better controls
for the Single Market (SM), controlling for trade with third parties, properly treating the
gravity equations’ omitted variables problem, and using unidirectional trade flows rather
than bilateral average flows; while different studies applied some of these measures none
have applied all of them. On top of this the study innovates by estimating differences of
trade, studying the effects of the euro on different member states, using quantile
regression, and naturally by using more recent data.
The paper proceeds as follows. The next section reviews the literature on the
euro’s trade effects. The third section lays out the research design, the fourth section
reports the results of a few techniques used to estimate merchandise trade among 22
countries during 1991-2011; these include fixed effects regression and regressing trade
differences. The fifth section explores the different euro effects on Mediterranean and
3 non-Mediterranean countries using trade differences and quantile regression. The sixth
section provides conclusions.
The long hunt for the euro’s effect
An intensive debate developed in the past decade among trade economists following
Rose’s (2000) and Frankel and Rose’s (2002) finding that currency unions triple trade
among their member states. The Rose Effect, as it became known, can be identified when
a gravity equation is run on a very large dyadic dataset with some 180 countries over the
recent 50 or 60 years.1 Large trade effects for currency unions were obtained with similar
datasets by Frankel (2010), Gil-Pareja et al. (2008), Glick and Rose (2002) and Tenreyro
and Barro (2003). Other studies based on shorter periods of data and smaller groups of
countries tended to arrive at much more modest estimates, typically finding that euro area
membership increased trade between member states by 5-15 per cent.2 Baldwin et al.
(2008, 42) could find no more than a two per cent effect.
The vast differences in these estimates resulted from a number of empirical
problems, most of which can be broadly classified as either control group problems or
1
There is no scope here to explain the theoretical background of the Gravity model. See
Baldwin et al. (2008, 10-7) for a very detailed exposition.
2
See Chintrakarn (2008), Flam and Nordström (2003; 2006) and Micco et al. (2003).
Within this group of studies Baldwin et al. (2005) produced an outlying result of as
much as 80 per cent euro’s effect by assuming a convex sensitivity of trade to exchange
rate risk.
4 endogeneity problems (See Table 1). Starting with control group problems, any estimate
of the euro’s effect depends greatly on the countries and the periods with which the euro
area is compared. Ideally scholars should measure the euro’s effect on trade by recording
trade levels in the years following the launch of the single currency and then rewinding
history and observing trade levels under separate national currencies. Because this is
impossible scholars need a control group – a group of countries that did not join the euro
area but that would have similarly responded to the launch of the euro had they joined it.
Without a properly selected control group the average treatment effect (of joining the
euro area) on the trade of randomly selected countries will differ from the average
treatment effect on the treated countries (those that actually joined the euro area), and it is
the latter that is of relevance (Baier and Bergstrand, 2009, 64).
Two other variants of the control group problem arise when the dataset is based
on either too few euro area member states (Tenreyro and Barro, 2003) or too few noneuro countries (Baldwin et al., 2008, 39-42), which leads to low external validity, trying
to infer from the experience of a few member states on a more general case.
Defining the treatment group is also important. The estimated euro’s effect is
biased when a single dummy accounts for all currency unions. Rose-type datasets involve
many tiny very poor and authoritarian countries. How relevant is their experience to rich,
modern, European democracies, with reliable trade data, and respect for individual
property rights and the principle of free trade (Egger et al., 2008, 281)? Since European
Union (EU) member states tend to have diversified economies with long-established
trade-supporting institutions and legislation they are ceteris paribus more inclined to
trade than most other countries. Including them in a dataset with many low-trading
5 countries sets a very low baseline for trade and any variable that singles them out will
have a large coefficient. Indeed when Chintrakarn (2008) and Persson (2001) used
matching techniques to mimic a controlled experiment they estimated the currency
unions’ trade effect to be respectively 8 per cent or nil.
Then there are longitudinal control group problems. These involve using a dataset
dominated by distant eras, when trade levels were lower ceteris paribus (Frankel, 2010).
And it is hard to believe that the gravity equation’s coefficients should have remained
stable over such a long and eventful period, which was characterized by accelerated
technological change. Many studies are also disadvantaged with too few post-euro years
in the dataset, or too few pre-euro years.
Nearly all studies also failed to control for trade between members and nonmembers of a currency union. In such studies the null group consists not only of trade
between non-member countries, but also of trade with third parties; the euro’s effect is
thus under estimated.
Turning to the endogeneity problem in studies of the euro’s effect on trade, one
source of endogeneity lies with gravity-related variables that are either hard to measure or
hard to instrument and are therefore often omitted. Thus, many studies tried to reduce
endogeneity with Country-Pair Fixed Effects (CPFE), Country Fixed Effects (CFE)
and/or Year Fixed Effects (YFE).3 CPFE have the advantage of capturing the effect of all
time-invariant country-pair characteristics, such as distance (which can easily be
measured) and bilateral political relations (which cannot). CFE and YFE control
3
See Berger and Nitsch (2005) Pakko and Wall (2001) Rose and van Wincoop (2001).
6 respectively for time-invariant national factors and universal annual effects. However,
such fixed effects do not control for important time-varying exporter- and importerspecific gravity variables, such as the price index of the importing economy, which
affects its purchasing power, and the global market access of the exporting country,
which affects its producer price index and its sales potential (the importer prices and the
exporter market access make up what Anderson and Van Wincoop (2003) referred to as
multilateral trade resistance); those can be controlled for with Exporter-Year and
Importer-Year Fixed Effects (EYFE and IYFE). Unfortunately with the exceptions of
Baldwin and Taglioni (2006) and Baldwin et al. (2008, 39-42) all studies of the euro’s
trade effect failed to specify such particular fixed effects.4
Another source of endogeneity could arise from the relations between currency
dummies and trade. Currency unions should promote trade but they may also be
established by countries that already trade much with each other (De Nardis and
Vicarelli, 2003; Tenreyro and Barro, 2003). It is of course unlikely that a pair of countries
would adopt a common currency between them merely because they trade, but
controlling for the effect of the EU’s Single Market on trade can reduce much of this
endogeneity.
4
Gil-Pareja et al. (2008) came close with Country-Year Fixed Effects but did not
distinguish exporters from importers. See Baier and Bergstrand (2007) for use of such
fixed effects in studies of the effect of trade agreements on trade.
7 Table 1: A summary and critique of the literature
Problem
Consequences
Control group includes
inappropriate countries
Upward estimation bias
Too few euro countries
Too few non-euro
countries
Very old data
Limited external validity
Limited external validity
Too few post-euro
years
Unpredicted estimation
bias
No control for trade
between euro area
member states and
non-euro member
states
Downward estimation
bias if the euro increases
such trade
No Exporter-Year,
Importer-Year and
Country-Pair Fixed
Effects (EYFE, IYEF
and CPFE)
Endogeneity (in OLS),
omitted variables
Inappropriate control
for SM
Upward bias if SM raises
trade
Averaging the twoway bilateral flows
Imprecise estimates due
to unnecessarily
aggregated data
Inappropriate
treatment of zero trade
Heteroskedasticity and
unpredicted estimation
bias
spuriously significant
estimates
Regressing stationary
vars. with nonstationary vars.
Upward estimation bias
Studies finding that the euro
increased trade by less than 15%
Control group problems
De Nardis and Vicarelli (2003);
Pakko and Wall (2001)
Baldwin et al. (2008); De Nardis
and Vicarelli (2003)
Berger and Nitsch (2005); Bun and
Klaassen (2007); Pakko and Wall
(2001); Persson (2001)
Baldwin et al. (2008); Baldwin and
Taglioni (2006); Berger and Nitsch
(2005); Bun and Klaassen (2007);
Chintrakarn (2008); De Nardis and
Vicarelli (2003); Flam and
Nordström (2003, 2006); Micco et
al. (2003); Pakko and Wall (2001);
Persson (2001)
Baldwin and Taglioni (2006);
Berger and Nitsch (2005); Bun and
Klaassen (2007); Chintrakarn
(2008); De Nardis and Vicarelli
(2003); Persson (2001)
Endogeneity problems
Berger and Nitsch (2005); Bun and
Klaassen (2007); Chintrakarn
(2008); De Nardis and Vicarelli
(2003); Flam and Nordström (2003,
2006); Micco et al. (2003); Pakko
and Wall (2001); Persson (2001)
All studies
Technical problems
Berger and Nitsch (2005); Bun and
Klaassen (2007); Chintrakarn
(2008); Micco et al. (2003);
Persson (2001)
Pakko and Wall (2001); Persson
(2001)
All studies
Studies finding that the euro increased
trade by more than 15%
Frankel (2010); Frankel and Rose
(2002); Gil-Pareja et al. (2008); Glick
and Rose (2002); Rose (2000); Rose
and van Wincoop (2001)
Tenreyro and Barro (2003)
Tenreyro and Barro (2003)
Frankel (2010); Frankel and Rose
(2002); Gil-Pareja et al. (2008); Glick
and Rose (2002); Rose (2000); Rose
and van Wincoop (2001); Tenreyro and
Barro (2003)
Baldwin et al. (2005); Frankel and
Rose (2002); Gil-Pareja et al. (2008);
Glick and Rose (2002); Rose (2000);
Rose and van Wincoop (2001);
Tenreyro and Barro (2003)
Frankel (2010); Frankel and Rose
(2002); Rose (2000); Gil-Pareja et al.
(2008); Glick and Rose (2002); Rose
and van Wincoop (2001); Tenreyro and
Barro (2003)
Baldwin et al. (2005); Frankel (2010);
Frankel and Rose (2002); Gil-Pareja et
al. (2008); Glick and Rose (2002);
Rose (2000); Rose and van Wincoop
(2001); Tenreyro and Barro (2003)
All studies
Frankel (2010); Frankel and Rose
(2002); Glick and Rose (2002); Rose
(2000); Rose and van Wincoop
(2001); Tenreyro and Barro (2003);
Frankel (2010); Frankel and Rose
(2002); Glick and Rose (2002); Rose
(2000); Tenreyro and Barro (2003)
All studies
Shaded studies estimated the euro’s effect directly; other studies inferred it from studying many other currency unions.
8 Two specific processes related to the Single Market may have biased estimates of
the euro’s effect. First, VAT fraud may have caused intra-EU imports to be significantly
underreported in the run up to the euro’s introduction, and attempts to deal with this
problem overlapped the 1999-2002 euro-introduction period. So part of the rise in official
trade numbers after the lunch of the euro had to do with better enforcement of the VAT
system. Second, the introduction of the Pan-European Cumulation System (PECS) in
1997, which simplified rules of origin in the EU, also broadly coincided with the launch
of the euro (Baldwin, 2006).
The task of separating the euro’s effect from the Single Market’s effect is
especially difficult in datasets with too few post-euro observations or too few non-euro
EU member states (Chintrakarn, 2008). In addition, the Single Market’s effect on trade is
dynamic because of the continuous EU legislation and the different speed of transposition
of directives in different member states (Baier and Bergstrand, 2007, 80). However,
legislation and transposition in the EU are hard to control for because they may be
endogenous to trade (i.e. member states may be more or less interested in pursuing them
depending on their trade performance). Various studies tried to capture the Single
Market’s dynamism but ended with an implausibly small and insignificant Single Market
effect (Baldwin et al., 2008, 34-42; Berger and Nitsch, 2005; Gil-Pareja et al., 2008). .
In addition to control group and endogeneity problems there are technical
problems in studying the euro’s effect on trade. One such problem is that many studies
took the average of the two-way bilateral trade flow for their dependent variables instead
of using the unidirectional trade flow. This unnecessary aggregation led to loss of
information and made estimates less accurate. Many of these studies also used the
9 logarithmic transformation of the average flow rather than average the logarithmic
transformation of each flow as would be consistent with the gravity equation’s theory
(Baldwin et al., 2008, 15; Pakko and Wall, 2001). Another technical problem is the
dropping of zero trade observations (up to 30 per cent of observations in Rose-type data
sets) by some scholars (Santos-Silva and Tenreyro, 2006; Tenreyro, 2010). Finally, none
of the studies seemed to be concerned about specifying stationary variables (such as
EYFE and IYFE) with non-stationary variables (such as trade) and time-invariant
variables (such as distance) in a single regression, which can result in spuriously
significant estimates and exaggerated R2.
Research design
Based on the insights of the previous section the chosen dataset period is 19912011. This period includes the latest reliable trade data, balances between pre-euro and
post-euro years, and starts after the break in the trade series that followed German
unification. Selecting countries for the euro group (the treatment group) and for the
control group is more complicated. Countries with a population of less than one million
(including for example Cyprus, Luxembourg and Malta) are not included in this study
because their economies are not sufficiently diversified and their trade data may be
distorted by a small number of major transactions (but Luxembourg’s data is aggregated
with Belgium’s). This leaves us with 145 countries The euro group obviously includes
the countries that have adopted the single currency, but not Estonia, Slovakia and
Slovenia because they have been members of the euro area for only a few years, and
because their trade data is affected by the major political and economic restructuring that
10 they underwent in the 1990s, in a way that sets them apart from other euro area member
states. This leaves eleven euro area member states to be matched by eleven non-euro
countries (the control group).
The control group is constructed using the Propensity Score Matching (PSM)
method. However, rather than matching country-pairs, as done in Persson (2001) and
Chintrakarn (2008), each euro area country is matched with a non-euro country. The
reason for this is that PSM involves a logit regression (see below) and in a dyadic dataset
with a euro area membership dummy as a dependent variable, the observations are not
independent of one another (if countries A, B and C are all members in a currency union
then the B-C observation is dependent on the A-B and A-C observations).5 PSM seems
appropriate because the treatment group is fixed (there are only eleven euro area
countries) and cannot be enlarged by applying other matching methods at the cost of
poorer covariate balance between the treated and control groups (King et al., 2011).
Persson (2001, 439, 447) and Chintrakarn (2008) select for the control group
country-pairs that “…in the absence of a common currency would on average trade with
the same intensity”; thus, they use the conventional gravity variables. However, their
dyadic variables (such as distance) cannot be used to select from a panel of countries.
Output, another gravity variable, can be measured on a national basis of course, but
output varies greatly among the euro area member states so does not characterize them.
5
This problem does not exist when the dependent variable is membership in a Free Trade
Area (but does exist in customs unions).
11 There is no conventionally agreed theory as to why the euro area in particular was
established (Sadeh and Verdun, 2009). This has led Eichengreen (2010) to conclude that
the euro area is Sui Generis. Thus, rather than trying to explain the euro area this study
selects for the control group countries that if subject to the same treatment (joining the
euro area) would on average trade with the same intensity as the actual euro area member
states. In other words, we are seeking criteria that can affect the euro’s trade effect, not
necessarily the base level of trade. Crucially, these criteria must be exogenous to
membership in the euro area.
The eleven countries in the treatment group are characterized by being members
of the EU’s Single Market, committed to the principle of free trade (as reflected in their
long standing membership in GATT/WTO), and not having a legacy of Communism and
transition to a market economy; they are rich but not extremely rich and have no
dominant oil sector. The particular range of non-oil income per capita that characterizes
euro countries is relevant because it is associated with a certain capital intensity of their
economies, which in turn is associated with comparative advantage in distinct industries;
their particular range of income also affects the type of products consumed. Another
common feature of the euro countries is low women fertility, which is associated with
great participation in the labour market, high education and a sophisticated civil society.
Accordingly, the following three variations of a logistic regression were run on a crosssection of 145 countries with a population exceeding one million6:
6
The dataset is cross-sectional because the timing of the launch of EMU had little to do
with income and fertility, or any other national-specific variable (other than Germany
12 Table 2: Matching parameters for euro area member states
(1)
Single Market
9.72 ***
(3.25)
GDP per Capita
1.18 *
(0.51)
-0.02
(1.13)
GDP per Capita squared
(2)
0.93 ***
(0.51)
-0.02 ***
(1.13)
Ln GDP per Capita
Fertility
Constant
Wald Chi2 test
Log pseudo-likelihood
Observations
Pseudo R2
(3)
-9.63 *
(5.42)
-16.5 *
(9.12)
-5.54 **
(2.32)
-9.01 **
(3.61)
2.14 ***
(0.58)
-5.36 **
(2.70)
-4.95 ***
(1.63)
15.75 ***
-4.64
12.24 ***
-13.56
14.17 ***
-18.05
145
0.88
145
0.65
145
0.54
* .05 < p ≤ .10. ** .01 < p ≤ .05. *** p ≤ .01.
where Single Market is a dummy for membership in that club, GDP per capita excludes
the oil sector and is in thousands of current US dollars, and Fertility is the natural
logarithmic transformation of the average number of children per women (all based on
the World Bank’s development indicators and averaged for the 1991-2011 period).7 The
negative coefficient of the square of GDP per capita implies that the likelihood of being a
euro area member state peaks at a non-oil income level of 25,554 US Dollars in Column
perhaps); fertility anyway varies very little with time, as does income in each country
relative to the others.
7
A communist/transition legacy could not be specified in the regression because it
perfectly predicts membership in the euro area. Membership in the Single Market does
not perfectly predict membership in the euro area because Austria and Finland joined it
only in 1994 (see more below).
13 (1), or 26,802 Dollars in Column (2), and decreases for higher or lower levels of income.
The regression in Column (1) is chosen for fitting propensity scores because of its high
pseudo R2 but the regression in Column (2) shows how strong the other criteria are in
characterizing membership in the euro area, and the one in Column (3) shows that a
simpler logarithmic relationship between income and euro membership is inferior in
characterizing the euro countries.8
Next, the fitted values for each of the 145 countries are taken as their propensity
scores. Then, the absolute value of the difference in propensity scores is calculated
between each of the 134 non-euro counties and each of the 11 euro area countries. All of
these 1,474 (=11*134) pairs are sorted by this absolute difference. The eleven countries
selected for the control group (Australia, Canada, Denmark, Japan, South Korea, New
Zealand, Norway, Singapore, Sweden, the United Kingdom and the Unites States) were
those with the smallest differences, skipping countries with a Communist/transition
legacy.9 Among these 22 countries there are 462 country pairs. Hence there are a total of
9,702 observations (none are missing).
In order to demonstrate the usefulness of a properly selected control group of
countries a smaller dataset restricted to the EU member states is also used. Some scholars
justify such a small dataset on the grounds that EU membership may have very complex
8
Compare this pseudo R2 with 0.70 in Baier and Bergstrand (2004), 0.49 in Persson
(2001, 440), and no more than 0.41 in Egger et al. (2008, 286).
9
The null hypothesis of similar means in the control and treatment groups can be rejected
only at p = 0.33 for income and at p = 0.13 for fertility.
14 and unquantifiable trade effects beyond membership of the Single Market (Baldwin et al.,
2008, 21). The EU and the euro area may be Sui Generis, incomparable to other
experiences.
The dependent variable is the natural logarithmic transformation of annual
nominal USD merchandise exports from one country to another, taken from the UN’s
ComTrade database (in each observation an average is calculated between the values
reported by the exporter and the importer countries). Since there are no zero trade values
in this dataset the euro’s effect can be estimated using a linear regression with ExporterYear Fixed Effects (EYFE), Importer-Year Fixed Effects (IYFE) and Country-Pair Fixed
Effects (CPFE). The standard errors in all of the tests that are reported in the next section
are adjusted for clustering on country pairs (De Benedictis and Taglioni, 2011).
A simple dummy flags country pairs consisting of two members of the Single
Market and another one flags pairs of two members in the euro area. For each of these
two blocks another dummy controls for trade with third parties by flagging observations
with one member state of the block and one non-member country. Thus, for each block
the default case consists of observations of two non-member states.
The euro area and Single Market dummies have the advantage of reducing the
endogeneity problem discussed above by being exogenous to judgment and time-varying
trade but they lack dynamism and are insensitive to the evolution of integration in these
clubs. Their coefficients should be interpreted as period averages.
As a further robustness check a Single Market index is also used to account for its
dynamism. In each year this index is the logarithmic transformation of the number of
active Single Market directives with a transposition deadline falling in any of the
15 previous years. The lowest number of such active directives in the dataset is 264 (in
1991), and the highest (for 2011) is 1302.10 This index is interacted with each of the three
Single Market dummies and thus returns zero in observations with no Single Market
member states.
The Single Market is interpreted broadly to represent EU trade integration in
general; hence it is regarded as having existed even before 1992, when it was already
more than a customs union. However, the coding of the Single Market dummy is
sensitive to the establishment of the European Economic Area (EEA) in 1994, when
Norway, Austria, Finland and Sweden joined the Single Market (the latter three joined
the EU a year later). Likewise, the coding of the euro area dummy is sensitive to Greece’s
entry in 2001.
The euro more than doubled its members’ trade
Table 3 presents results from a simple specification that is common to many euroeffect studies. The first two columns are based on the entire dataset, in Column (1)
controlling for the Single Market’s effect on trade with dummies, and in Column (2)
controlling for it with the log of the Single Market index (hence the coefficients of this
index are estimates of its trade elasticity). The last two columns are based on a dataset
restricted to 14 EU member states. Since almost all of the dataset’s countries were EU
and Single Market member states throughout the period the Single Market dummies
10
See at
http://ec.europa.eu/internal_market/score/docs/relateddocs/list-dir/im-directives_en.pdf
16 would come close to forming a linear combination with the Country-Pair Fixed Effects
and thus are dropped in the third column.
Table 3: The euro and Single Market average effects on merchandise trade
(1)
Dummy for pairs of two
euro area member states
Dummy for pairs of euro
member with nonmember
Dummy for pairs of two
SM member states
Dummy for pairs of SM
member with nonmember
SM index in pairs of two
SM member states
SM index in pairs of SM
member with nonmember
Constant
0.65
(0.07)
0.34
(0.04)
1.40
(0.16)
0.71
(0.09)
R2
Obs.
(2)
***
(4)
1.49 ***
(0.12)
0.70 ***
(0.07)
-0.26
(0.17)
-0.18 *
(0.09)
20.4 ***
(0.11)
0.20 ***
(0.02)
0.10 ***
(0.01)
20.6 ***
(0.13)
21.1 ***
(0.09)
0.15 ***
(0.02)
0.07 ***
(0.01)
21.4 ***
(0.08)
0.83
9,702
0.83
9,702
0.90
3,816
0.90
3,816
***
0.28 **
(0.13)
0.15 **
(0.07)
(3)
***
***
Note: Results from a linear regression with EYFE, IYFE and CPFE. Entries are
coefficient estimates, clustered standard errors in parentheses. * .05 < p ≤ .10. ** .01 < p ≤
.05. *** p ≤ .01. The dependent variable is the natural logarithmic transformation of
annual nominal USD exports of merchandise. Column (1)-(2) are based on a dataset of 22
countries, Column (3)-(4) are based on the smaller dataset of 14 EU member states. The data
period is 1991-2011.
Table 3 demonstrates how much the estimated euro effect depends on the choice
of dataset and on the choice of control method for the Single Market trade effect. The
euro’s effect is very strong and clear in both datasets if the Single Market index is not
used. The coefficient in the upper row in Column (1) suggests that on average across
member states and over the euro’s 13 years, trade between two participating member
17 states (i.e. exports from any one of them to any other) was 92 per cent higher than it
would have been without the euro. In the small dataset (Column (3)) the effect rises to
344 per cent. With the Single Market index the euro’s effect in the large dataset is
estimated at 32 per cent in Column (2) and disappears altogether in Column (4). Table 3
also demonstrates that without a properly selected control group of countries (i.e. in the
small EU14 dataset) the euro effect is prone to exaggeration in either direction. The
euro’s effect on trade with third parties is roughly one half the magnitude of its effect on
trade among the member states.
The Single Market index is a more sophisticated variable than a plain Single
Market dummy but using it along with a dummy for euro area membership may lead to
an underestimation of the euro’s trade effect, because the euro’s effect on trade is
assumed to be fixed over time, and all of the dynamism in European integration is
captured by the Single Market index. In order to arrive at correct estimates of the euro’s
effect on trade, some dynamism must be allowed in monetary integration too. In addition,
trade is a non-stationary variable, as are the dummies for membership in the euro area,
the dummies for membership in the Single Market, and the Single Market index; no
country has left either of the blocks and the number of regulations only rises with time.
Thus, it is possible that the estimates reported in Table 3 are spuriously significant.
In order to correct these problems table 4 runs the differences of the log of trade
on the differences of both euro area membership dummies (with members and with nonmembers). The membership differences have a value of 1 only in 1999 (2001 for Greece)
and zero in all other years. Thus, the coefficients of these differences reflect the changes
to trade as a result of the entry to the euro area. Seven lags to the differenced euro
18 dummies are specified, each showing the trade effect in a particular year following entry
to the euro area. For example the 7th lag represents the effect on trade in 2006 (2008 for
Greece). Further lags were not possible because specifying each lag omits one year from
the beginning of the dataset and specifying an 8th lag would omit the crucial year 1999. In
order to find out whether the coefficients merely reflect the members pre-existing
tendency to trade, rather than a causal effect of the euro, a lead was specified as well.
The four columns in Table 4 correspond to the four columns in Table 3. Columns
(1) and (3) do not control for the Single Market because differencing its dummies is
meaningless (the years before 1999 are omitted and no country in the datasets has joined
or left the Single Market since). Columns (2) and (4) control for the Single Market with
differenced Single Market index. The estimates for the coefficients of the Single Market
index differences, which reflect a second derivative (the acceleration in trade associated
with Single Market regulation), are not reported in the table to save space. The EYFE and
IYFE are included in all four columns, but the regression is run with random effects,
because the CPFE are constant over time and should not affect annual changes in trade
for a given pair.
The coefficients for the leads are always negative but are statistically significant
only in the small dataset. These results do not support a claim that euro membership is
caused by greater trade; if any they suggest that the euro area was formed by countries
that tended to trade below their potential. This means that any positive coefficient of a
euro area membership dummy under-estimates the true euro effect. The same
interpretation is suggested for the coefficients in the No-lead-or-lag row, when the tradeenhancing effect of the euro is not yet observed. The euro’s trade effect does not begin to
19 kick in until 2001 in all four columns but by 2006 it adds up to a coefficient of 0.61-0.73
(84-107 per cent) in the large dataset or 0.74 (100 per cent) in the small dataset for pairs
with two members of the euro area.11 The euro’s effect on trade with non-members is
roughly 0.30 (35 per cent). On the technical level Table 4 demonstrates that estimating
the differences of trade rather than its levels reduces the sensitivity of the euro effect to
the choice of dataset and to the choice of control method for the Single Market.
Interestingly the euro’s effect over the years follows an uneven pattern,
alternating from significant to insignificant coefficients. This can perhaps be explained by
the euro area’s macroeconomic effects, such as its business cycle, which the euro
dummies inevitably capture along with the euro’s microeconomic effect on trade. While
the microeconomic effect can be expected to build up steadily, euro-related slowing of
economic activity can mitigate it (or enhance it in boom years). Of course what matters in
the practical world is the sum of these effects, which Table 4 measures, because one
cannot enjoy the euro’s microeconomic effects without being exposed to its
macroeconomic effects.
11
These numbers are calculated by adding the coefficients of the different years for pairs
of two Euro area member states since 2000, ignoring coefficients with p > .10.
20 Table 4: The euro’s differenced effects on merchandise trade by year
(1)
(2)
(3)
Differenced dummy for pairs of two
euro area member states
1 period lead (1998)
No lead or lag (1999)
1 period lag (2000)
2 period lag (2001)
3 period lag (2002)
4 period lag (2003)
5 period lag (2004)
6 period lag (2005)
7 period lag (2006)
Differenced dummy for pairs of euro
member with nonmember
1 period lead (1998)
No lead or lag (1999)
1 period lag (2000)
2 period lag (2001)
3 period lag (2002)
4 period lag (2003)
5 period lag (2004)
6 period lag (2005)
7 period lag (2006)
-0.17
(0.15)
-0.16
(0.12)
-0.05
(0.09)
0.45
(0.07)
0.05
(0.08)
-0.23
(0.09)
0.02
(0.10)
0.27
(0.10)
0.24
(0.12)
-0.03
(0.11)
-0.08
(0.07)
-0.01
(0.05)
0.22
(0.04)
0.02
(0.04)
-0.12
(0.05)
-0.00
(0.05)
0.14
(0.05)
0.13
21 ***
**
***
**
***
**
**
*
-0.32
(0.32)
-0.24
(0.23)
-0.06
(0.09)
0.33
(0.08)
-0.00
(0.08)
-0.17
(0.08)
-0.00
(0.10)
0.22
(0.10)
0.23
(0.12)
-0.11
(0.18)
-0.11
(0.12)
-0.02
(0.05)
0.16
(0.04)
-0.00
(0.05)
-0.09
(0.05)
-0.01
(0.05)
0.12
(0.06)
0.12
***
**
**
**
***
*
**
*
-0.26
(0.06)
-0.17
(0.07)
-0.07
(0.06)
0.41
(0.06)
0.07
(0.04)
-0.06
(0.05)
0.02
(0.07)
0.16
(0.08)
0.18
(0.05)
***
-0.17
(0.05)
-0.07
(0.04)
-0.06
(0.04)
0.19
(0.04)
0.02
(0.03)
-0.03
(0.03)
-0.03
(0.04)
0.07
(0.04)
0.06
***
**
***
**
***
*
*
***
*
**
(4)
-0.26
(0.06)
-0.17
(0.07)
-0.07
(0.06)
0.40
(0.06)
0.07
(0.04)
-0.06
(0.05)
0.02
(0.07)
0.16
(0.08)
0.18
(0.05)
***
-0.17
(0.05)
-0.07
(0.04)
-0.06
(0.04)
0.19
(0.04)
0.02
(0.03)
-0.03
(0.03)
-0.03
(0.04)
0.07
(0.04)
0.06
***
**
***
**
***
*
***
*
**
(0.07)
(0.07)
(0.03)
(0.03)
Constant
0.11 ***
(0.03)
0.10 ***
(0.03)
0.14 ***
(0.03)
0.59 ***
(0.21)
R2
Obs.
0.49
5,544
0.49
5,544
0.70
2,184
0.70
2,184
Note: Results from a linear regression with EYFE and IYFE. Entries are coefficient
estimates, clustered standard errors in parentheses. Coefficients for differenced SM index
in Columns (2) and (4) are not reported. * .05 < p ≤ .10. ** .01 < p ≤ .05. *** p ≤ .01. The
dependent variable is the differenced natural logarithmic transformation of annual
nominal USD exports of merchandise. Column (1)-(2) are based on a dataset of 22
countries, Column (3)-(4) are based on the smaller dataset of 14 EU member states. The
data period is 1999-2010.
These results imply an even greater cumulative trade effect than the one reported
in Table 3. This could be explained perhaps by some fall in trade during the crisis years
since 2008, for which year-specific coefficients are not estimated in Table 4. Or it could
mean that the euro’s effect is stronger when measured against non-members’
performance during its time, than when measured relative to the pre-euro’s years (recall
that the years 1991-1998 are dropped in Table 4). The exception is Column (3) where the
sum of coefficients in Table 4 is about one half of the corresponding coefficient in Table
3. This is further evidence that the euro’s effect measured in Table 3 Column (3) is
spurious, but so probably is the effect of the Single Market in Columns (2) and (4) of
Table 3, which ‘robbed’ the euro of its effect.
That any integration project takes time to result in enhanced trade should come as
no surprise (Baier and Bergstrand, 2007, 80). Trade integration often has delayed effects
because firms and households take time to adjust to its evolving measures. Trade ties may
be characterized by persistence and stickiness as a result of the costs of setting up
distribution and service networks in the partner country (De Nardis and Vicarelli, 2003).
Firms that want to take advantage of the reduced costs that a single currency offers need
22 time to reorganize; and perhaps the practical preparations in 2001 for the changeover to
euro notes and coins was more important than previously thought in convincing firms to
engage in cross-border trade.
The euro increased trade in the Mediterranean more than elsewhere
The issuing of notes and coins made the euro more tangible for everyone, but
must have been especially important in reducing the fixed costs of cross-border trade for
small firms, which tend to conduct a larger share of their transaction in cash compared
with large firms; it was similarly important for anyone preferring cash over other means
of payments. This suggests that the euro may have asymmetrically affected the
economies of the different member states according to the share that small firms make up
of their production, and the tendency of their consumers to transact in cash.
Thus, in this study’s last set of tests, the trade effects of the euro are allowed to
vary among two groups of member states: the Mediterranean countries (Greece, Italy,
Portugal and Spain) plus Ireland (henceforth referred to simply as the Meds), and the
other member states of the euro area (Austria, Belgium, Finland, France, Germany and
the Netherlands – the non-Meds). The Mediterranean economies are especially
characterized by small businesses and cash transactions and thus can be expected to gain
much from the introduction of the euro. Identifying the trade effects of the euro in the
member states that received bail-outs is also interesting in light of these great efforts to
keep them in the euro area. From an economic point of view, is it worth it? Hence Ireland
is included in the Meds group.
23 Table 5 breaks down the results from Table 4 according to these groups of
member states. In order to save space the estimates for the coefficients of the Single
Market index differences are again not reported as well as the coefficients for the
differenced dummies for pairs of Euro member with non-member states (they are all
similarly broken down by country groups). Across the two different datasets and the two
different methods to control for the Single Market’s effects Table 5 shows that the euro
increased trade among the Meds more than it increased trade among the non-Meds. The
sum of coefficients for pairs of two non-Meds member states varies between 0.52 and
0.16 (-0.10 if the small dataset is considered);12 for Meds-non-Meds trade it varies
between 0.67 and 0.49 (0.24 if the small dataset is considered); and for Meds-Meds trade
it varies between 0.81 and 1.02 (125-177 per cent). Indeed with the exception of column
(2) the euro’s positive effect on trade among non-Meds is significant only in 2003.
Another method to control for different effects of the euro on the two groups of
countries is quantile regression. Quantile regression estimates the coefficients so as to
minimize errors around specified quantiles in the distribution of the dependent variable,
rather than around its average as is the case with conventional regression. Thus, quantile
regression can estimate the distinct set of coefficients and euro effect for observations
with large trade flows and for those with small trade flows.
12
As in the interpretation of results in Table 4 this calculation ignores coefficients with p
> .10 and starts from the 1 period lag.
24 Table 5: The euro’s differenced effects on merchandise trade by year
(1)
(2)
(3)
Differenced dummy for pairs of two
non-Med euro area member states
No lead or lag (1999)
1 period lag (2000)
2 period lag (2001)
3 period lag (2002)
4 period lag (2003)
5 period lag (2004)
6 period lag (2005)
7 period lag (2006)
Differenced dummy for pairs of nonMed & Med euro area member states
No lead or lag (1999)
1 period lag (2000)
2 period lag (2001)
3 period lag (2002)
4 period lag (2003)
5 period lag (2004)
6 period lag (2005)
7 period lag (2006)
Differenced dummy for pairs of two
Med euro area member states
No lead or lag (1999)
-0.16 ***
(0.05)
-0.04
(0.06)
-0.01
(0.06)
-0.06
(0.05)
0.16 ***
(0.05)
0.06
(0.05)
-0.01
(0.05)
0.09
(0.05)
0.24
(0.19)
0.32 *
(0.19)
0.19
(0.19)
0.04
(0.08)
0.20 **
(0.08)
0.02
(0.07)
-0.01
(0.05)
0.02
(0.06)
0.06
(0.04)
-0.09 **
(0.04)
-0.15 ***
(0.04)
-0.06
(0.06)
0.16 ***
(0.05)
0.04
(0.06)
0.03
(0.04)
0.04
(0.07)
0.07
(0.05)
-0.11 **
(0.05)
-0.17 ***
(0.05)
-0.07
(0.06)
0.18 ***
(0.06)
0.05
(0.06)
0.00
(0.05)
0.04
(0.07)
-0.17
(0.06)
-0.03
(0.06)
0.23
(0.05)
0.00
(0.05)
-0.06
(0.05)
0.06
(0.05)
0.12
(0.05)
0.14
(0.06)
0.19
(0.16)
0.19 *
(0.11)
0.36 ***
(0.11)
0.06
(0.06)
-0.01
(0.06)
0.01
(0.06)
0.12 **
(0.06)
0.11
(0.07)
-0.07
(0.05)
-0.06
(0.04)
0.13
(0.04)
0.00
(0.04)
0.03
(0.04)
0.03
(0.05)
0.08
(0.05)
0.09
(0.04)
-0.02
(0.05)
-0.07
(0.05)
0.16 ***
(0.04)
0.01
(0.04)
0.04
(0.04)
0.04
(0.05)
0.09 *
(0.05)
0.12 **
(0.05)
-0.13
25 (4)
***
***
**
**
0.15
*
***
*
**
-0.15 **
-0.11
1 period lag (2000)
2 period lag (2001)
3 period lag (2002)
4 period lag (2003)
5 period lag (2004)
6 period lag (2005)
7 period lag (2006)
(0.12)
-0.05
(0.09)
0.45
(0.07)
0.07
(0.07)
-0.20
(0.09)
0.05
(0.10)
0.29
(0.10)
0.27
(0.12)
***
**
***
**
(0.21)
0.06
(0.11)
0.48 ***
(0.10)
0.07
(0.09)
-0.14
(0.09)
-0.00
(0.10)
0.28 ***
(0.11)
0.26 **
(0.12)
(0.07)
-0.06
(0.07)
0.41
(0.07)
0.08
(0.04)
-0.04
(0.05)
0.02
(0.07)
0.18
(0.08)
0.20
(0.05)
***
*
**
***
(0.08)
-0.01
(0.08)
0.41 ***
(0.08)
0.07
(0.06)
-0.03
(0.05)
0.08
(0.08)
0.21 ***
(0.08)
0.22 ***
(0.07)
Constant
0.13 ***
(0.01)
0.18 ***
(0.02)
0.11 ***
(0.01)
1.35 ***
(0.26)
R2
Obs.
0.46
6,006
0.47
6,006
0.68
2,360
0.68
2,360
Note: See note to Table 4. In addition, coefficients for differenced dummies for pairs of
euro member with non-member states are not reported to save space.
However, there are two technical difficulties in applying quantile regression to
this study. First, applying quantile regression to pooled cross-section time series is not
obvious; Stata package runs quantile regression only on cross-sectional data. Thus, the
dataset is transformed into a cross-section by defining the dependent variable for each
pair in two forms: Once as the average value of the log of trade during 1999-2011, and
again as the difference in the log of trade between 1999 and 2011.
The second technical problem is that quantile regression is relevant as a measure
of the different euro effects in Med and non-Med countries only to the extent that the
different groups of pairs of countries tend to occupy different ranges in the distribution of
trade; for example, if pairs of non-Meds trade significantly more than pairs of Meds. This
might not be the case for non-Med countries that trade relatively less because they are
26 small and distant from many other countries (Finland), or Med countries that trade
relatively more because they are large and proximate to many other countries (Italy).
Thus, distinguishing Meds from non-Med countries merely by the size of their observed
nominal trade flow might be noisy.
Table 6: Tests for differences in means of trade between Med and non-Med pairs
Group 1
Pairs of
two nonMed
euro area
member
states
Group 2:
Pairs of
Med &
non-Med
euro area
member
states
Group 3:
Pairs of
two Med
euro area
member
states
Group 4
(in large
dataset):
Pairs with
at least
one noneuro area
country
Group 4
(in small
dataset):
Pairs with
at least one
non-euro
area
country
Trade defined as the average value of the log of trade during 1999-2011
Mean
Standard deviation
Observations
t statistic with Group 1
t statistic with Group 3
23.0
0.29
30
5.61 ***
21.9
0.21
60
4.88 ***
2.69 ***
21.1
0.40
20
5.61 ***
21.3
0.10
352
14.2 ***
1.26
22.1
0.16
72
4.64 ***
3.95***
Trade defined as the difference in the log of trade between 1999 and 2011
Mean
Standard deviation
Observations
t statistic with Group 1
t statistic with Group 3
0.83
0.06
30
3.73 ***
0.59
0.05
60
4.68 ***
0.01
0.59
0.07
20
3.73 ***
0.74
0.03
352
2.84 ***
4.75***
0.56
0.03
72
6.52 ***
0.66
In order to mitigate this noise problem Table 6 tests for similarity of means of
trade flows among four mutually exclusive groups of pairs of countries – the three groups
identified in Table 5 and the default group (pairs with at least one non-euro country). The
statistics for the default group are provided separately for the large dataset of 22 countries
27 and for the small EU14 dataset (the statistics for the other three groups are identical in the
two datasets of course).
Table 6 shows that not all tests clearly reject the null hypothesis of similar means
between the groups. For trade levels in the large dataset the null cannot be rejected when
comparing Med pairs (group 3) with non-euro pairs (Group 4). In other words the trade
flows of these two groups occupy a similar range on the distribution of trade and so are
hard to distinguish. The same is true for trade differences between Med pairs and Mednon-Med pairs (Group 2), and in the small dataset when comparing non-Med pairs and
non-euro pairs. However, in the small dataset the means of trade levels of Med and nonMed pairs are clearly distinguishable of each other as well as of other groups of pairs.
Conveniently the mean for Group 1 (pairs of non-Med countries) is the highest of all
groups and the mean for Group 3 (pairs of Med countries) is the lowest of all groups.
Table 7 runs simultaneous quantile regressions with the average value of the log
of trade during 1999-2011 as a dependent variable using the small EU14 dataset. Each
two columns boxed together show results from a single regression targeting two
symmetric quantiles. The first two columns target tertiles, the next two columns target the
two extreme quartiles and the last two columns target the two extreme deciles. These are
cross-section regressions so there are no fixed effects, hence the gravity equations’
bilateral variables are specified. Exporter Country and Importer Country Fixed Effects
replace respectively the EYFE and IYFE that are specified in the previous regressions.
The Single Market dummies are not specified as all countries were member states
throughout the period (and the Single Market index collapses into a Single Market
28 dummy in cross-section). The dummies for the euro area are similar to those used in
Table 3.
Table 7: The euro and Single Market average effects on merchandise trade
q33
q67
q25
q75
q10
q90
Dummy for pairs of two
euro area member states
1.88 ***
(0.43)
0.75
(0.62)
1.91 ***
(0.61)
1.29
(0.87)
1.51 *
(0.83)
0.93
(0.93)
Dummy for pairs of euro
member with nonmember
0.71 *
(0.39)
-0.29
(0.53)
0.79 *
(0.43)
0.28
(0.68)
0.55
(0.63)
0.11
(0.44)
Log of distance
-0.47 ***
(0.14)
-0.73 ***
(0.15)
-0.29 **
(0.15)
-0.68 ***
(0.16)
-0.38 **
(0.16)
-0.59 ***
(0.17)
Dummy for contiguity
0.50 **
(0.25)
0.38 *
(0.22)
0.42
(0.28)
0.48 **
(0.23)
0.30
(0.24)
0.64 ***
(0.22)
Dummy for common
official language
Dummy for common
language to populations
Dummy for a historical
colonial link
Constant
0.49
(0.61)
-0.45
(0.54)
0.45
(0.61)
21.5 ***
-1.37 **
(0.69)
1.30 **
(0.63)
0.78
-1.38
0.48
-0.38
(0.66)
(0.88)
(0.75)
(1.26)
-0.72
(0.61)
1.64 **
(0.76)
0.61
(0.59)
24.5 ***
20.0 ***
1.41 *
(0.79)
1.54 **
(0.67)
23.7 ***
-0.60
1.08
(0.72)
(1.16)
0.90
0.55
(0.71)
(1.22)
20.9 ***
24.1 ***
(1.13)
(1.29)
(1.36)
(1.41)
(1.65)
(1.15)
Pseudo R2
0.83
0.81
0.84
0.81
0.86
0.81
Obs.
182
182
182
182
182
182
Note: Results from a quantile regression with ECFE, ICFE. Entries are coefficient
estimates, standard errors in parentheses. * .05 < p ≤ .10. ** .01 < p ≤ .05. *** p ≤ .01. The
dependent variable is the average of annual natural logarithmic transformations of
nominal USD exports of merchandise during 1999-2011.
Table 7 shows a euro effect on trade between pairs of euro area countries, which
is stronger at the low tail of the distribution of trade compared with the high tail (see top
row), although inter-quantile regressions (not shown) confirmed that these differences are
statistically significant only in some of the columns. The magnitude of the euro effect in
the low quantiles is much larger than that estimated in Table 5 and Table 3. Even when
29 the regression targets the median of trade the coefficient of the dummy for pairs of two
euro area member states is 1.64 and highly significant (not shown in Table 7). This
magnitude of the euro effect is less reliable than other estimates in this study because it is
based on a cross section and on trade levels. However, the striking differences in Table 7
between the euro effect on low and high traders, and the identification in Table 6 of the
Meds with low trade and the non-Meds with high trade supports the trends identified in
Table 5. Furthermore, while the estimates in Table 5 are limited to 2006, the use of
quantile regression confirms the results for the entire 1999-2011 period.
Conclusions
This study finds that the euro’s introduction provided little stimulus to trade before its
notes and coins were introduced, but that later it at least doubled trade among its users,
even when the crisis years after 2008 are considered. The euro also increased trade with
third parties. The lack of a euro’s effect before the euro started to circulate is compatible
with Baldwin’s argument that the euro mainly enhances variety-driven trade by lowering
the fixed costs of cross-border trade, rather than lower transaction costs. Since consumers
and small businesses handle cash relatively more than large firms, for many of them the
euro was not a reality before they began preparing for the introduction of its notes and
coins in 2002. The findings also explain why it was so far so hard to properly detect the
euro’s effect: it was much more gradual and fitful than anticipated. Region-sensitive
estimation shows that the euro area stimulated trade among all of its member states, but
especially among the Mediterranean countries. This finding provides further support to
Baldwin’s argument, given that these economies are characterized by small firms.
30 On a technical level this study demonstrates the importance of selecting the
appropriate countries and years for the dataset when estimating the euro’s effect, the
importance of controlling for trade with third parties, proper treatment of the gravity
equations’ omitted variables problem, proper control for the effects of the Single Market,
and the use of unidirectional trade flows rather than bilateral average flows. While some
studies of the euro’s effect considered some of these issues, none have treated them
simultaneously. This study makes additional improvements to the exiting literature on the
trade effects of the euro by estimating differences of trade, by studying the separate
effects of the euro on different member states and by using quantile regression.
The results of this study are evidence that micro-economically the euro works in
spite of its macro-economic difficulties. To the extent the euro remains a politically
desirable project the results of this study strengthen the case for saving it. However,
important questions remain. First, the intermittent pattern of the euro’s effect over the
years deserves further study. The existing literature has provided mostly microeconomic
explanations for the euro effect, but the microeconomic benefits of a currency cannot be
enjoyed without being exposed to its macroeconomic effects; scholars interested in the
former must better control for the latter. Second, if the euro was launched by countries
that had a tendency to trade less than their potential according to the gravity model, as
suggested in the small EU14 dataset in Table 4, then the estimates in this study of the
euro’s effect on trade represent a floor; further analysis is required to distill the full trade
effect of the euro.
Third, if the euro is especially beneficial for the Mediterranean countries what are
the implications for the distribution of monetary power in Europe (the ability to shift the
31 external adjustment burden onto other countries)? The greater trade among the
Mediterranean countries does not support the notion that the euro empowered mostly the
Coordinated Market Economies (CME) (Vermeiren, 2013). If any, the stimulus that it
provided for small business should strengthen Mediterranean mixed market economies.
Some of the enhanced Mediterranean trade was arguably driven by looser credit in the
2000s but that effect was global, not euro-specific, and Table 7 shows that the Med trade
effect is evident even when the crisis years (when the credit was withdrawn) are taken
into account. Of course the findings of this study in themselves are not sufficient to reject
the CME-domination argument but the literature on the Varieties of Capitalism should
consider them.
Fourth, further research is needed into the domestic political economy of the
euro’s effect on trade. If small firms are the great winners from the euro can we expect
‘big business’ to be less influential? Will this have implications for the balance of
political influence among regions in Europe? A sense that the euro is in the long term
spreading prosperity may enhance political support for it by public opinion, which is a
crucial element for the long run sustainability of EMU. Unfortunately the domestic
political economy of the euro’s effect on trade is beyond the scope of this study but it
certainly deserves a serious study.
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