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Coase-Sandor Working Paper Series in Law and
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2015
The Politics of the United States' Bilateral
Investment Treaty Program
Adam S. Chilton
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CHICAGO
COASE-SANDOR INSTITUTE FOR LAW AND ECONOMICS WORKING PAPER NO. 722
(2D SERIES)
The Politics of the United States’ Bilateral Investment
Treaty Program
Adam Chilton
THE LAW SCHOOL
THE UNIVERSITY OF CHICAGO
March 2015
This paper can be downloaded without charge at:
The University of Chicago, Institute for Law and Economics Working Paper Series Index:
http://www.law.uchicago.edu/Lawecon/index.html
and at the Social Science Research Network Electronic Paper Collection.
Electronic copy available at: http://ssrn.com/abstract=2576330
THE POLITICS OF THE UNITED STATES’
BILATERAL INVESTMENT TREATY PROGRAM
Adam Chilton*
March 10, 2015
Abstract
Scholars consistently argue that the United States has signed Bilateral Investment Treaties (BITs)
with developing countries to promote the development of international investment law and to
protect American capital invested abroad. I challenge this view of the United States’ BITs
program. I argue that the United States has used BITs as a foreign policy tool to improve
relationships with strategically important countries in the developing world, and, as a result, the
program should in part be evaluated based on whether it has produced political benefits. I
empirically test this theory in two ways. First, I test whether investment or political
considerations are better at explaining U.S. BIT signings. This analysis shows that investment
considerations do not help to explain the pattern of U.S. BIT formation, but that political
considerations do. Second, I estimate the political benefits the United States has received from
signing BITs with developing states. This analysis suggests that having signed a BIT makes
countries likely to vote similarly to the United States at the United Nations. This project thus
provides the first empirical evidence that the U.S. BITs program has been motivated by political
considerations, and that the program may have produced modest foreign policy dividends.
*
Assistant Professor of Law, University of Chicago Law School.
I would like to thank Daniel Abebe, Rachel Brewster, Britt Cramer, Tom Ginsburg, Tom
Miles, Rich Nielsen, Eric Posner, Rob Schub, Beth Simmons, Matthew Stephenson, Dustin
Tingley, Jason Yackee, and Mark Wu for helpful comments and advice. I would also like to
thank Daniel Marcin for helpful research assistance. This draft benefited from presentations at
the American Law & Economics Association 2014 conference, the American Society of
International Law 2014 conference, the Midwest Political Science Association 2014 conference,
the ASIL International Economic Law Interest Group Junior Scholars Forum, the University of
Chicago Law School Works in Progress Workshop, and the Harvard International Relations
Research Workshop.
1
Electronic copy available at: http://ssrn.com/abstract=2576330
I. INTRODUCTION
In the last sixty years, over 2,600 Bilateral Investment Treaties (BITs) have been
negotiated between pairs of countries (Salacuse 2010, 428). Taken together, these treaties create
a regime of international law that provides protections for individuals and corporations seeking
to invest their capital abroad. Although the United States ranks first in the world in both foreign
direct investment inflows and outflows (Sachs and Sauvant 2009), America was a late entrant
into the BITs regime. The United States did not express a willingness to sign BITs until 1981—
twenty-two years after Germany negotiated the world’s first BIT—and the United States did not
have its first BIT in effect until 1988 (Salacuse 2010, 433).
Despite this slow start, the United States has now signed BITs with 47 countries.1 All
U.S. BITs are based on a model treaty and, although the specific provisions of the model have
evolved over the years, the core elements of these agreements have been the same (Akhtar and
Weiss 2013, 8). First, agreements guarantee that investments made by individuals and
corporations from the other country will be treated fairly and equitably. Second, the agreements
limit expropriation of investment, and provide for compensation when expropriation does take
place. Third, the agreements provide investors the right to transfer their property out of the
foreign state freely. Fourth, the agreements place restrictions on trade-distorting performance
requirements—like local content requirements or export quotas. Fifth, if the terms of the BIT
have been violated and the national courts of the foreign country do not provide redress, the
agreements authorize investors to force the foreign state to participate in binding arbitration.
Taken together, these five provisions give assurances to capital exporters that investments made
in the market of a treaty partner will be provided with legal protection.
Perhaps unsurprisingly, as the number of BITs that the United States is party to has
proliferated, so has scholarship on these agreements (Shaffer and Ginsburg 2012, 35-38).
Although this scholarship has not included a single empirical study evaluating the motivations of
the U.S. BITs program, scholars have consistently argued that the United States signed BITs
because it hoped to influence the development of international investment law and to protect
American investments abroad (Elkins, Guzman, and Simmons 2006, 815-16; Vandevelde 2005,
171; Lang 1998, 457; Vandevelde 1998a, 201-2; Vandevelde 1988,1-2; Gann 1985, 374; Sachs
1
Appendix A provides a complete list of the BITs the United States has signed.
2
Electronic copy available at: http://ssrn.com/abstract=2576330
1984, 195). Given this belief, scholars have evaluated U.S. BITs almost entirely based on their
ability to protect and promote investment.
Although it is certainly at least partially true that the United States was concerned with
the development of international investment law and hoped that these treaties would help
American investors, there are several reasons to doubt that this investment-centric view of the
U.S. BITs program is the fully story. First, U.S. BIT negotiators have warned treaty partners that
they should not expect a wave of new investments as a consequence of these agreements
(Alvarez 2010, 621 n.69; Vandevelde 1998a, 212), which is evidence that U.S. officials
themselves are aware that the economic impact of these agreements is likely quite limited.
Second, if the United States were motivated by a desire to promote the development of
international investment law and to protect American investors, it would have entered into a BIT
with any country that would agree to its terms. This, however, was not the case (Vandevelde
1993, 169-70). Third, there is scant evidence of any pressure from American interest groups on
the United States to ratify the BITs that it has signed, suggesting that U.S. investors are not eager
to avail themselves of any new opportunities or protections that BITs may provide. Fourth,
evidence suggests that U.S. BITs do not have a positive impact on investment flows between the
United States and partner countries (Peinhardt and Allee 2012; Yackee 2008). Fifth, there is
reason to believe that BITs do not influence companies’ investment decisions (Yackee 2010),
which calls into question whether BITs are negotiated to provide increased protections for capital
exporters.
Given the limited interest in—and evidence of—the investment benefits of BITs, it is
worth reconsidering why the United States actively pursued a BITs program for three decades. I
argue that the dominant narrative misses the mark: the United States did not primarily form BITs
to promote and protect investments abroad, but instead to improve relationships with politically
important developing countries. BITs have been used in this way because they have several
features that make them an appealing foreign policy tool: they do not necessitate outlaying funds,
require the United States to make only “redundant” obligations, are easy to sell politically, and
take minimal effort to negotiate given their standardized nature. Having a BIT with the United
States is attractive politically to the governments of many developing countries as well. Potential
BIT partners are frequently eager to sign these treaties, even though they are warned that the
agreements likely will not lead to new investments, because the treaty provides domestic
3
political benefits to the country’s government. Since international relations are a repeated game,
a new treaty partner would thus likely reciprocate by extending political benefits to the United
States in order to receive favorable treatment again in the future. The implication of this theory is
that investment considerations will not explain which countries the United States has chosen to
sign BITs with, and that looking solely at the investment consequences of the treaties ignores
many of their potential benefits. Instead, it is my contention that political considerations will
better explain which countries the United States has chosen to sign BITs with, and that BITs
should be evaluated at least in part based on whether they have generated political dividends.
I empirically test this theory in two ways. First, I test what factors predict the countries
that the United States has signed BITs with over the last thirty years. To do so, I use a series of
survival models that estimate the likelihood that a BIT will be signed between the United States
and a potential treaty partner in a given year. The results of this analysis suggest that variables
that measure investment considerations—specifically a country’s level of investment risk and the
amount of investment flows from the United States—do not have a statistically significant
impact on the likelihood that the United States will sign a BIT with that country. Moreover, the
results of this analysis demonstrate that variables that measure the political importance of
developing countries—specifically whether the state received military aid or was formerly
communist—do have a positive and statistically significant impact on the likelihood that the
country would sign a BIT with the United States. These results thus lend clear support to my
theory that the United States selected BIT partners based on political, and not investment,
considerations.
Second, I examine whether signing BITs has produced political benefits for the United
States. To do so, I use a recently developed statistical method—life history matching—that helps
mitigate the problems of selection bias and post-treatment bias that have plagued most timeseries cross-sectional research designs (Nielsen, n.d.), and that has shown potential as a way to
study the effects of treaty ratification (Nielsen and Simmons 2014). I specifically use this method
to examine whether signing a BIT with the United States made the treaty partner more likely to:
(1) vote similarly to the United States in the United Nations General Assembly; (2) allow the
United States to deploy troops within its territory; or (3) support the invasion of Iraq in 2003. My
results suggest that having a BIT in effect with the United States cause the treaty partner to be
more supportive of the United States in the UN General Assembly, but likely did not alter the
4
number of U.S troop deployed on the partner’s soil or whether the partner joined the Iraq War
Coalition. In other words, this study not only shows that the United States chose which states to
pursue BITs with based on political considerations, but also that signing BITs likely produced
modest political dividends.
This project thus makes several important contributions to the literature on international
investment law. First, this project should cause commentators and scholars to change the
narrative offered to explain why the United States has pursued BITs with developing states. The
existing literature on U.S. BITs almost exclusively claims that these treaties were negotiated to
produce more favorable conditions for American investors and promote the development of proinvestor international law. After this project, this account should be replaced with the new
explanation that BITs have been negotiated as a low cost foreign policy tool. Second, this paper
is the first quantitative effort to consider directly why the United States might have chosen to
pursue BITs with specific countries. Previous efforts have focused on explaining the
proliferation of BITs from developing countries’ perspectives (Alvarez 2010; Tobin and Busch
2010; Guzman 1998), but have not flipped the question and asked why the United States—or
developed countries more broadly—would take the time to negotiate and ratify investment
treaties that have limited direct influences on capital flows. Third, this project develops a theory
that tries to explain both why the United States and developing countries would be motivated to
sign investment treaties, even if they do not promote investment, and to explain why those
treaties could still result in dividends—albeit political ones—for the United States. Finally, this
project provides evidence suggesting that the United States’ BITs program has produced benefits
that have not yet been understood or explored. This evidence should cause scholars who are
skeptical of the economic benefits of BITs to reassess the program based on the political
advantages that they may provide.
This paper proceeds as follows. Part II describes conventional explanations for the
growth of the United States BITs program, before developing a political theory of BITs
formation. Part III tests the theory by empirically assessing the factors that predict the BITs the
United States has chosen to sign, and Part IV tests the theory by empirically examining whether
BITs have produced political dividends. Part V concludes.
5
II. A POLITICAL THEORY OF THE UNITED STATES BITS PROGRAM
Although scholars have nearly universally argued that the United States BITs program
was motivated by investment considerations, I argue that the United States primarily used BITs
as a foreign policy tool. In order to make that argument, I first provide an overview of the United
States’ history with BITs. Second, I lay out the standard explanation of the United States’ BITs
program: namely, the idea that the program was motivated by a desire to protect American
investments abroad. Third, I present a range of evidence suggesting that the United States’ BITs
program cannot be explained purely as an effort to promote investment law and protect investors.
Finally, I develop the theory that the United States used BITs as a low-cost method of cultivating
relationships with politically important countries in the developing world.
A. The United States’ Experience with BITs
In 1977, twenty years after European countries first began to negotiate bilateral treaties
that regulate investments, the United States launched its BITs program (Vandevele 1993).2 The
program was a successor to the treaties of general relations—Friendship, Commerce, and
Navigation (FCN) Treaties—that included investment provisions. The United States had
negotiated FCNs for nearly two hundred years, but that had ground to a halt by the mid-1960s.3
After starting the BITs program, however, the United States spent the next four years preparing a
model treaty that could be used in negotiations. This process was delayed in party due to
extensive interagency consultations, and the transfer of primary authority over the program from
the State Department to the Office of the United States Trade Representative. In 1981, the United
States finally produced a draft model BIT to use in negotiations with other countries
(Vandevelde 1993, 627).
2
There have already been a number of detailed accounts of the history of the United
States’ BITs program, so I offer only a very brief account here. For a detailed discussion of the
establishment and development of the U.S. BITs program, see Vandevelde (1993, 624-627);
Vandevelde (1992); Gann (1985, 373); Sachs (1984).
3
For a general discussion of the end of the FCN program, see Coyle (2013). Although a
number of factors contributed to the end of the program, one driving factor was that many of the
topics regulated by the agreements began to be governed by other sources of international law.
6
Figure 1: Countries That Have Signed a BIT with the United States
Figure 1 shows the countries that have signed a BIT with the United States. Countries that
signed a BIT that is currently in effect are solid, and countries that signed a BIT that is not
currently in effect are dashed.
In 1982, the United States started negotiating its first BITs with Egypt and Panama
(Sachs 1984). After this, the United States negotiated eight additional BITs in the next four years
(Vandevelde 1993, 627-28). Those treaties were with Senegal, Haiti, the Democratic Republic
of the Congo, Morocco, Turkey, Cameroon, Bangladesh, and Granada. After a hiatus, the
program was given new life by the end of the Cold War (Vandevelde 1993, 630). As Eastern
Bloc states moved towards opening their markets, the United States began negotiating a BIT
with the Soviet Union, and with several formerly communist states, such as Poland. When the
Soviet Union disintegrated, the United States quickly negotiated BITs with a number of former
Soviet Republics. At the same time, the United States also continued to negotiate BITs with
countries in Africa, Asia, and South America. As of December 2013, the United States had
signed forty-seven BITs. Of the forty-seven treaties, forty-one had been ratified by both parties
and gone into effect. A map of the countries the United States has signed a BIT with is shown in
Figure 1.
7
B. Conventional Explanations for the United States’ BITs Program
Although there have been a number of attempts to empirically examine why developing
countries choose to enter into BITs (Elkins, Guzman, and Simmons 2006; Guzman 1998), there
has been no attempt to empirically examine why the United States specifically—or even
developed countries generally—decide to negotiate and sign BITs. Despite the lack of
quantitative research on the topic, most commentators have claimed that the United States
entered into BITs to influence the development of Customary International Law by reinforcing
international legal principles on the treatment of foreign capital and to secure the rights of
American investors (Elkins, Guzman, and Simmons 2006, 815-16; Vandevelde 2005, 171; Lang
1998, 457; Vandevelde 1998a, 201-2; Vandevelde 1988,1-2; Gann 1985, 374). In other words,
these scholars contend that the United States’ motivations were straightforward: investment
treaties were negotiated to promote and protect investment.4 This explanation has been put forth
not only to explain the motivations of the United States, but also to explain the motivations of
developed countries more generally (Tobin and Busch 2010, 2; Hamilton and Rochwerger 2005,
1; Vandevelde 2005, 171; Salacuse 1990, 661).
Given the fact that commentators have consistently described BITs as treaties that
developed states use for the purpose of promoting and protecting investment, it is unsurprising
that scholarship evaluating the success of BITs has focused almost exclusively on whether the
agreements have been successful methods of attracting capital (Salacuse and Sullivan 2005).
Although there have been a few efforts to study the effects of BITs along other dimensions—for
example their effect on litigation (Simmons 2013) or the likelihood that their ratification leads to
Preferential Trade Agreements (Tobin and Bush 2010)—these studies have still conceived of
BITs as treaties created for economic reasons. The result is that scholars studying the United
4
The one exception to this narrative that this author is aware of is Vandevelde (1993).
Although Vandevelde (1993) argues that the motivations of the program have shifted over time,
and that some BITs are political, Vandevelde does not consistently make this argument in later
writing. For example, Vandevede more recently argued that “the motivation for the developed
country to conclude [BITs] was to obtain protection for its foreign investors,” and that “[i]n the
United States in particular, the decision to negotiate BITs was very much motivated by a desire
to create a network of treaties adopting the standard of prompt, adequate, and effective
compensation for expropriation . . .” (Vandevede 2005, 171). And Vendevede started his recent
book on U.S. investment law by claiming that “the principal purpose of the [U.S.] BITs
[program] has been to protect U.S. investment in foreign countries” (Vandevede 2009, 1).
8
States’ BIT program have viewed these agreements as a tool to promote investment that should
be evaluated based on how well they accomplish that goal (Gann 1985, 440-41).
C. Limits to Economic Explanations for BIT Formation
Although this conventional explanation for the growth of the United States BITs program
has been widely repeated, there is a great deal of qualitative evidence to suggest that the program
was not motivated by a desire to promote the development of international investment law or
protect American capital invested abroad. First, there is evidence that the government officials
who negotiated BITs did not expect a large increase in Foreign Direct Investment (FDI) as a
consequence of the agreements (Vandevelde 1998b, 524). In the words of one commentator, “as
veteran U.S. BIT negotiators have repeatedly pointed out, U.S. negotiators have routinely alerted
prospective BIT Partners not to expect that BITs would necessarily increase such flows from
U.S. investors . . .” (Alvarez 2010, 621 n.69). Of course, it is possible that the negotiators still
hoped that BITs would increase investment flows, or that BITs would protect existing and future
investments—even if the investments were not flowing at a higher rate. The importance of this
admission, however, is that if U.S. negotiators were skeptical that specific investment treaties
would lead to new FDI from U.S. based investors, it is plausible that the officials pursuing the
BITs were motivated by reasons other than simply increasing protections for American citizens
and corporations.
Second, if the United States were hoping simply to promote international law that is
favorable to investment and provide protections to American investors, the United States should
theoretically be willing to negotiate, sign, and ratify BITs with any state that was willing to agree
to the U.S. model BIT. This at least would be a reasonable conclusion given the twin beliefs held
by American negotiators that BITs will not impact existing investment flows (Alvarez 2010,
621) and that they require the United States to only make redundant concessions (Gann 1985,
374). As the United States’ failure to ratify the BITs it negotiated with Panama and Haiti
illustrate, however, this is far from the case. Both Panama and Haiti were among the first
countries to sign BITs with the United States, but before the Senate approved the BITs, the
governments in both countries were overthrown by regimes that the United States did not support
(Vandevelde 1993, 169-70). As a consequence, the United States did not ratify the agreements
9
with these countries because doing so was deemed inconsistent with the foreign policy objectives
of the United States. In other words, the United States cared less about the potential to develop
favorable international law while protecting American investments in Panama and Haiti—places
experiencing serious unrest where such investor protections might be thought to be uniquely
important—than it did about the politics of having the treaty in place with a government that it
did not support.
Third, it appears that there is little pressure from American interest groups on the United
States to ratify the BITs that it has signed.5 Perhaps the best evidence of this fact is it has taken
an average of 1,259 days for BITs that the United States has signed to be ratified and go into
effect, but all of the BITs that the United States Senate has ratified have been approved by
unanimous voice votes. Moreover, not only have business interests not opposed the BIT
program, but organized labor has also not opposed the program (in part because there was no
evidence that BITs would promote outward investment) (Vandevelde 2009, 26). This suggests
that the long delays that have occurred before BITs are ratified are not a result of political
opposition, but instead occur because the ratification of BITs is not a priority. This information
also makes it plausible to infer that investors do not aggressively apply pressure to the Senate to
approve BITs so that they can enjoy the increased protections that purportedly motivate the
creation of the agreement in the first place.
Fourth, BITs have not had an effect on investment flows between the United States and
the countries that it has negotiated these treaties with (Peinhardt and Allee 2012). When looking
at BITs overall, and not just the U.S. BITs program, the evidence that BITs directly increase the
flow of FDI between the two countries that have negotiated them is mixed (Shaffer and Ginsburg
2012, 36-38; Yackee 2010, 405-14). In the last several years, there have been a number of
studies showing that BITs do not have any direct positive effect on FDI (Yackee 2010; Gallagher
and Birch 2006), whereas competing studies using different methodology that focuses on total
increases in investment—and not just bilateral increases—have found that BITs do in fact have a
positive effect on overall FDI (Neumayer and Spess 2005; Salacuse and Sullivan 2005). One
5
Appendix B presents information on the Senate’s consideration of all BITs the United
States has signed. Although a detailed analysis of the Senate ratification of U.S. BITs has the
potential to provide interesting insight into the agreements more broadly, this author is unaware
of any scholarship that has closely explored the subject. A full treatment of the topic, however, is
beyond the scope of this paper.
10
recent commentary on the state of the scholarship on the topic concluded that only studies
examining bilateral “investment flows between BIT parties find that BITs have little impact,
whereas studies focusing on overall investment flows into BIT parties find that they have
positive effects” (Shaffer and Ginsburg 2012, 37). When looking solely at the U.S. BITs
program, however, the best existing evidence that this author is aware of is much clearer: U.S.
BITs have not had a statistically significant influence on investment patterns between the United
States and its treaty partners (Peinhardt and Allee 2012).
Fifth, there is evidence that BITs might not influence investment decisions. In one recent
study, Yackee (2010) compiled evidence from a number of unique sources to argue that BITs do
not impact the investment decisions of U.S. companies. Specifically, this study provided
evidence from a survey of general counsels to United States-based multinational corporations
and found that these individuals did not believe that the presence of a BIT impacted their
company’s investment decisions (Yackee 2010, 426-34). Moreover, Yackee also compiled
survey evidence from providers of political risk insurance that found that those insurers do not
factor the presence of a BIT into their underwriting decisions (Yackee 2010, 422-26). These
alternative sources of evidence suggest that American investors were not eager to take advantage
of the protections that were allegedly being negotiated for their benefit.
D. A Political Theory of BIT Formation
Taken together, this evidence suggests the United States may have had other motivations
for negotiating BITs generally, and for picking which countries to negotiate them with
specifically. My theory is that, counter to the conventional narrative, the United States’ BITs
program was not used primarily as a means of influencing the development of international
investment law and protect American investments abroad, but instead as a means of improving
relationships with politically important developing countries.
The foundation of this theory is the idea that there are four features of BITs make them a
particularly useful foreign policy tool from the United States perspective. First, BITs are
inexpensive. Unlike other tools that can be used to improve alliances—such as foreign aid—
BITs do not require the United States to outlay funds. Second, BITs require the United States to
only make “redundant” promises (or at least they were initially seen by U.S. policymakers that
way (Gann 1985, 374)). That is to say, investors with capital in the United States are already
11
given access to U.S. courts, and the government believed that it was unlikely to expropriate
foreign investment in any event.6 Thus, the promises extracted from the United States were
things the government had already pledged to do and thus created no new obligations. Third,
BITs are easy to sell domestically. To both the United States Congress and the public, these
treaties can be presented as a way to ensure that American investors are protected and given the
same legal rights abroad that America extends to foreigners. Fourth, there is a standard model in
place so that negotiating additional BITs requires relatively little effort.7
Given these attractive features, the United States should be willing to sign a BIT with a
government it wishes to support when the foreign government would like to have a BIT with the
United States. The obvious question, of course, is why the developing state would want a BIT
with the United States instead of an alternative low cost benifit—like a state visit or statements
of support—when the BIT imposed at least some obligations on the developing state. My theory
is that foreign governments were interested in signing BITs with the United States because doing
so had the potential of producing domestic political benefits in two ways. First, even though
foreign states were warned that having a BIT with the United States may not result in increased
investment, there was still uncertainty about what the actual economic impact of the agreement
would be. Foreign governments were thus able at least to argue that the agreement had the
potential to produce economic benefits, and that they were trying to take steps to improve their
countries economic conditions. Second, although BITs are a relatively low cost tool for the
United States, there are still some negotiating costs associated with them for the U.S.
government. As a result, the fact that the United States was willing to expend some effort
6
Investment Protections in U.S. Trade and Investment Agreements: Hearings Before the
Committee on Ways and means of U.S. House of Representatives, 11th Cong. 65 (2009)
[hereinafter 2009 Hearings] (testimony of Linda Menghetti, Emergency Committee For
American Trade) (noting that protections for foreigners are “somewhat redundant in that they
have very strong protections already in the U.S. law and Constitution. And when they do
challenge it, what they find is, again, the U.S. provisions form takings to due process and
transparency issues all incorporated in that dispute resolution process . . . .”).
7
Bilateral Treaties Concerning the Encouragement and Reciprocal Protection of
Investment: Hearing Before the Senate Committee on Foreign Relations, 104th Cong. 4 (1995)
(testimony of Daniel Tarullo, Assistant Secretary of State for Economic and Business Affairs)
(“The BIT Program, I think we should take good note, is a relatively low cost . . . [because] . . .
BITs are negotiated on the basis of a prototype document and only minor changes to that
prototype language are generally accepted. As a result, the program requires only modest
negotiating resources.”).
12
negotiating a BIT and passing it through the Senate provides a signal that the U.S. government
was supportive of the foreign government. The combination of these features made many
countries in the developing world interested in forming the treaty with the United States.
Since BITs produce a benefit for the foreign government, it would be reasonable that the
United States would enjoy an improved relationship with that country in the short term after the
agreement was signed. This is because states are engaged in repeated interactions. After the
United States gave a political benefit to the foreign state, it would be prudent for the new treaty
partner to reciprocate so that the United States would provide it other forms of favorable
treatment in the future. The benefits that the treaty partner should be expected to provide to the
United States, however, would likely be relatively modest. This is because signing a BIT likely
would not produce large political benefits for the foreign government, and as a result, the foreign
government would be unlikely to pay a large price for receiving it.
The theory that the U.S. BITs program was motivated by political considerations
generates two clear testable hypothesizes. First, variables that measure the political importance
of countries in the developing world should be better predictors of which countries the United
States signed BIT with than variables that measure investment considerations. Second, signing a
BIT with a developing country should produce modest political benefits for the United States in
the short-term from the treaty partner. These hypotheses are tested in Parts III and IV.
III. TESTING THEORIES OF BIT FORMATION
To test the theory outlined in Part II, this section of the paper tests whether the set of
countries that the United States has chosen to sign BITs with is better explained by investment
considerations or political considerations. First, I explain the method used to test theories of BIT
formation. Second, I discuss the data collected for this project. Third, I report the results of a
series of statistical tests that suggest that investment considerations have not been determinants
of which countries the United States has signed BITs with, but that whether a state was
politically important was a determinate of BIT formation. Fourth, I present the results of a series
of robustness checks that support my results.
13
A. Empirical Approach
To empirically test my theory, I have constructed a time-series cross-sectional (TSCS)
dataset for every potential BIT partner for the United States. Because the United States has
exclusively signed BITs with developing states, I include an observation for every country that is
not a member of the OECD for all years between 1981—the year when the United States started
negotiating BITs—and 2009—when the U.S. signed its most recent BIT with Rwanda.8 The
dependent variable takes the value 0 if the two countries have not signed a BIT in year t, and 1 if
they have signed a BIT in year t. After a country has signed a BIT with the United States, it
drops from the dataset. The data is thus structured for a survival analysis of the likelihood of the
“onset” of a BIT.
Researchers generally, and international relations scholars specifically, have struggled
with how to model survival analyses correctly when using TSCS data (Beck et al. 1998). The
problem is that logit and probit models assume temporal independence between observations
while hazard models make an assumption that there is temporal dependence between units, and
selecting an approach based on a false assumption will lead to an incorrect estimation of standard
errors. To address this problem, I use the method suggested by Carter & Signorino (2010) and
model BIT onset using logit regression, but control for the possibility that the observations were
temporally dependent by including three variables—Time, Time2, and Time3—that account for
the time that elapsed since the beginning of the BITs program.9 Additionally, to account for
autocorrelation and heteroskedasticity, I calculate robust standard errors clustered by country.
Using this approach to model BIT formation has three advantages. First, by using logit
models, the results produced are more familiar and easier to interpret than hazard ratios, but still
account for temporal dependence. Second, using logit models makes it possible to perform a
number of robustness checks that are not available with hazard models—a fact that will be
exploited in Part III.D. Third, this approach is consistent with other recent empirical scholarship
8
The reason I exclude members of the OECD from the dataset is that OECD membership
is an excellent proxy for the wealthy, developed, industrialized nations that were not potential
BIT partners for the United States. The one country that was a member of the OECD and later
signed a BIT with the United States is Turkey. As a result, I still included Turkey within the
dataset.
9
Specifically, for the variable Time, observations in 1981 are coded as 1, 1982 as 2, etc,
whereas Time2 are the values squared and Time3 are the values cubed.
14
in international law (Verdier and Voeten 2013) and comparative law (Ginsburg and Versteeg
2014).
B. Data
As previously noted, the dependent variable in this analysis is whether a BIT was signed
between the United States and a potential treaty partner in a given year. Although by most counts
the United States has signed 47 BITs, 46 BITs are analyzed in this study because the BITs with
the Czech Republic and Slovakia were negotiated and signed with Czechoslovakia, but then
simply inherited by each successor state after their split. As a result, Czechoslovakia drops from
the dataset after signing a BIT with the United States, and does not reenter after the split.
The independent variables collected for this study are all lagged one year and fall into
three categories.10 First, two independent variables are used to test whether BITs are a product of
a desire to protect investment. The first of these variables is Investment Protection. This variable
is from a proprietary dataset of investment risks developed by the Political Risk Services Group
that has been widely used in academic research (perhaps most notably in Acemoglu et al. 2001).
The variable measures countries’ annual investment risk on a twelve-point scale from 1 (lowest
investment protection) to 12 (highest investment protection). If the U.S. BITs program was
motivated by a desire to improve the climate for American investments, then Investment
Protection should have a negative relationship with the likelihood of a BIT being signed.11 The
second variable is the natural log of the annual US FDI Outflows of foreign direct investment
from the United States to the potential partner country each year. This variable was taken from
the historical dollars of FDI data maintained by the U.S. Bureau of Economic Research, and was
converted to constant dollars.12 If the United States was motivated to improve protections for
existing investments, then US FDI Outflows should have a positive effect on the likelihood of a
BIT being signed.
Second, two independent variables are used to test whether a counties’ political
importance to the United States drove BIT formation. The first is the natural log of the amount of
10
Appendix C presents a correlation matrix of the independent variables.
11
It may be reasonable to hypothesize that there is a non-linear relationship between
Investment Protection and BIT onset. This possibility is explored in Part III.D.
12
This data is available at <www.bea.gov>.The table of inflation adjustment factors used
is available at <http://oregonstate.edu/cla/polisci/faculty-research/sahr/sahr.htm>.
15
Military Aid received from the United States in a given year. Previous research has suggested
that military aid is a strong proxy for political importance to the United States because the
recipients of military aid are perhaps the most crucial states to U.S. foreign policy objectives
(Meernik, Krueger, and Poe 1998; Poe and Meernick 1995). If the U.S. BITs program was
motivated by political considerations, Military Aid should have a positive effect on the likelihood
of a BIT being signed. The second variable that measures a country’s political importance is
whether the country was a Former Communist state.13 At the end of the Cold War, securing and
improving relationships with countries from the former Eastern Bloc was a major foreign policy
goal of the United States. In fact, in the Support for Eastern European Democracy (SEED) Act of
1989, Congress specifically urged the President to sign BITs with Poland and Hungary.14
Although the United States likely also hoped to open up these markets for investment, improving
relationships with these countries was a clear priority independent of any economic concerns. As
a result, if the U.S. BITs program was motivated by economic factors, Former Communist
should have a positive effect on the likelihood of a BIT being signed (even after conditioning on
investment considerations).
Third, a number of control variables were collected for this project to account for other
considerations that may influence the United States’ decision to sign a BIT with another
country.15 First, because it has been hypothesized that whether a country is a democracy may
influence that nation’s willingness to ratify a BIT—competing theories have been advanced that
democracies may either be more willing to ratify BITs because they already have strong
commitments to property rights, or less likely to ratify BITs because the promises are
13
This variable is coded as 0 in year t if a country is either communist or has never been
communist, but is coded as 1 in year t if a state was formerly communist but has transitioned to
be non-communist.
14
22 USC § 5401(c)(15).
15
Over the last decade, there have been a number of influential studies that have
attempted to explain BIT formation (Allee and Peinhardt 2010; Tobin and Busch 2009; Elkins,
Guzman and Simmons 2006; Guzman 1998). Instead of trying to include all of the variables that
have been used by these studies, I focus on controlling on a few widely used and theoretically
relevant variables for two reasons. First, including every possible control variable would create a
“garbage can” regression that could produce biased estimates (Achen 2005). Second, the
methodological approach used in the second half of this paper results in a dataset of 92
observations, but requires conditioning on 5 years of values for each variable. Since this severely
limits the number of covariates that can be used in the analysis, I have chosen to use a limited
number of control variables in this part of the analysis to ensure consistency across the paper.
16
redundant—I control each country’s Polity Score as a measure of democratization (Marshall and
Jaggers 2011). Polity Score is a widely used variable that places countries on a scale from -10
(most autocratic) to 10 (most democratic). Second, since a country’s level of development may
influence its attractiveness as a potential BIT partner, I control for the log of a country’s GDP
Per Capita. This variable was coded using the 2012 Penn World Tables (Heston et al. 2012).
Third, since countries that are taking steps to liberalize their economy may be more desirable
BIT partners, I control for whether a country has Open Capital Accounts as a proxy for financial
openness. I specifically use the index developed by Chinn and Ito (2008) that codes countries’
relative openness and intensity of capital account restrictions using the IMF Annual Report on
Exchange Arrangements and Exchange Restrictions. Fourth, since the United States may sign
BITs in response to the potential partner’s relationship with other countries, I control for the
number of Prior BITs that the partner country previously signed. This variable was coded based
on the ICSID database of BITs.
Finally, it is important to note that, as is typical when using variables from different
sources, there were many observations with missing values for the independent variables. Simply
dropping these observations via listwise deletion, however, would bias the results of this study
because the missing observations are likely non-random (Honaker and King 2010). To account
for this source of bias, I imputed values for the missing observations using the Amelia II package
for the R programing language (Honaker, King, and Blackwell 2011). Imputing values for
missing observations has been shown to produce more reliable results (Honaker and King 2010),
and is also consistent with the practice of recent international relations scholarship using timeseries cross-sectional data (Lupu 2013a; Lupu 2013b; Nielsen et al. 2012; Hill 2010).
C. Results
Figure 2 graphically presents the results of two logit regressions that test the influence of
investment considerations—Investment Protection and US FDI Flows—and political
considerations—Military Aid and being a Former Communist—on the likelihood that the United
States will form a BIT with a country in a given year.16 The base model includes only the four
key variables of interest, whereas the other model includes the control variables discussed in the
16
The regressions that Figure 2 is based on are Models (1) and (2) in Appendix D.
17
previous section. The results present are the simulated first differences as the key explanatory
variables moves from their minimum to their maximum value, while all other variables are held
at their means.17 Figure 2 thus reports the influence that the variable of interest has on the percent
change in likelihood that a BIT will be formed in a given year.
Figure 2: Marginal Effects on Likelihood of U.S. BIT Formation
Investment Protection
Base Model
With Controls
US FDI Flows
Base Model
With Controls
Military Aid
Base Model
With Controls
Former Communist
Base Model
With Controls
-10.0 -7.5 -5.0 -2.5
0
2.5
5.0
7.5
10.0
Marginal Effects on BIT Signing (%)
Figure 2 depicts the estimated impact of key explanatory variables on the likelihood
that the United States will sign a Bilateral Investment Treaty with a foreign state in a
given year. The results presented are the first differences as variables change from the
minimum to maximum value, with all variables held at their means. Point estimates
are represented by dots, with the lines representing 95% confidence intervals.
Statistically significant estimates are shown with solid lines, while statistically
insignificant estimates are shown with dotted lines.
17
For a defense of presenting regression results graphically using this method, see King,
Tomz, & Wittenburg (2000) and Kastellec & Leoni (2007).
18
As the results in Figure 2 clearly show, the two independent variables that measure
investment considerations do not achieve statistical significance. Investment Protection does
have the hypothesized negative effect but is not close to achieving statistical significance. The
second variable that measures investment considerations—US FDI Outflows—also does not have
a statistically significant influence on the likelihood of BIT formation. In both the base model
and the model with control variables, the effect of US FDI Outflows is negative, but the effect is
both substantively small and far from conventional levels of significance. These finding suggests
that United States has not selected BIT partners based simply on whether the country presented a
particularly risky investment climate for American capital exporters, or the amount of capital that
the United States is currently sending to the country.
In contrast, the two variables that measure political considerations—Military Aid
received from the United States and being a Former Communist state—both have a positive and
statistically significant effect on the likelihood of BIT formation. Military Aid is statistically
significant at the 0.05 level for the base model, and the 0.10 level for the model that includes
control variables. Additionally, Former Communist states is statistically significant at the 0.001
level for both the base model and the model including control variables, and also has the largest
substantive effect of the four independent variables explored in this paper. Together, these results
lend strong support to the theory that the United States was driven to sign BITs with countries
because of political considerations.
It is also worth considering the size of these effects. Military Aid increases the chance
that the United States would form a BIT with a partner country in a given year by 1.0 percent in
the base model, and 1.1 percent in the model with control variables. This effect is even larger for
Former Communist, which increases the probability by 7.1 percent in the base model, and 6.0
percent in the model with control variables. Although the size of these effects is small, the
United States signed less than 50 BITs in 30 years, so the likelihood that a BIT would be signed
with a country in any given year is incredibly low. To put the magnitude of these effects in
perspective, it is possible to calculate a “baseline probability” that a country will sign a BIT with
the United States each year. To do so, I estimated a model that includes the two variables
measuring investment considerations and the two variables measuring political considerations, as
well as all four control variables, and then estimated the probability of a BIT being formed with
19
all variables set at their means.18 The baseline probability that the United States would sign a
BIT with a country in a given year is just 0.5 percent. As a result, increasing the probability of a
BIT signing by between roughly 1.0 and 4.0 percent, as the political variables do, is a relatively
large effect given the low baseline probability of BIT formation.
These results thus suggest that there is only weak empirical support for the idea that the
United States signs BITs with developing countries because of investment considerations, but
that the political importance of a country does have explanatory power. Although these results do
not provide definitive proof that BITs are motivated by foreign policy considerations, they at
least suggest that foreign policy considerations are better predictors of BIT formation than
investment considerations—thus lending clear support to the theory outlined in Part II.
D. Robustness Checks
The results presented in the previous section are also robust to a series of alternative
model specifications. Specifically, the results are robust to estimating both the base model and
the model with control variables using a variety of alternative specifications.19 First, one
potential concern with the analysis in the previous section is that there are only a small number
of BITs signed relative to the number of country-years analyzed. Since the analysis uses an onset
structure, countries are dropped from the dataset in the year after a BIT is signed. The result is
that there are 46 observations that take the value of “1” and nearly 3,700 observations that take
the value of “0.” When the onset of an event is “rare,” previous research has shown that it can
result in biased estimates of the probability of that event occurring (King and Zeng 2001). To
ensure that this problem did not bias my results, I estimated a Rare Events Logit model (King
and Zeng 2001). The results produced using this method are consistent with the results presented
in the previous section. The coefficients for the variables of interests are significant at the same
levels, and have substantively similar effects. It is thus reasonable to conclude that the results in
the previous section were not biased because the onset of a BIT is rare.
Second, a major concern with any TSCS analysis is that there is serial correlation and
underlying heterogeneity between the groups being analyzed—in my case, countries. Although I
use the standard approach of correcting for this possibility by calculating robust standard errors
18
This model used to estimate this baseline effect is Model (2) in Appendix D.
19
The results of these robustness checks are reported in Appendix D. 20
clustered on country, recent research has suggested that this approach may not adequately
account for heterogeneity between groups in the data (King and Roberts 2014). As a result, I
have estimated a logit model with country random effects. This approach has the advantage of
directly modeling the underlying heterogeneity, instead of simply correcting the standard errors
after the fact (Nielsen 2013). When using this method, the variables that measure investment
consideration still do not achieve statistical significance, but the variables that measure political
considerations still have a statistically significant positive effect on BIT onset.
Third, it may be reasonable to hypothesize that Investment Protection has a relationship
with BIT onset, but that it is a non-linear relationship. Specifically, it may be the case the United
States would not be interested in signing a BIT with countries that have the lowest levels of
investor protection, but also would not feel the need to sign a BIT with countries that have the
highest levels of investor protection. To test this possibility, I estimated my initial models while
also including the quadratic term for Investment Protection (Investment Protection2). Doing so
did not reveal a statistically significant relationship between either Investment Protection or
Investment Protection2, but the effect of Military Aid and Former Communist remained
statistically significant when including Investment Protection2 in the regressions.
Fourth, it may be possible to argue that treating the variable Former Communist as a
measure of a country’s political importance is inappropriate for two different reasons. First, it
may be reasonable to think that the BITs negotiated with the Eastern Bloc may have had unique
motivations, and thus it would be inappropriate to conclude that investment considerations
cannot explain the BIT program overall when these countries where include in the data. To test
this theory, I estimated the base model and model with controls after dropping states that were
formerly communist from the dataset. In both models, neither variable measuring investment
considerations achieves statistical significance, but Military Aid still has a positive effect that is
statistically significant at the 0.05 level. This result suggests that, even excluding the wave of
BITs negotiated with the Eastern Bloc in the early nineties, political considerations are a better
predictor of BIT onset than investment considerations. Second, it may be reasonable to argue that
investment considerations influenced with which Former Communist states the United States
was most likely to sign a BIT. To test this possibility, I estimated a series of regressions in which
I interacted a different explanatory variable with the Former Communist variable. In these
regressions, the interaction between Investment Protection and Former Communist—as well as
21
the interaction between US FDI Outflows and Former Communist—is not statistically
significant. There is, however, a negative relationship for the interaction between Military Aid
and Former Communist that is statistically significant in the model with control variables. This is
likely because the United States was eager to form BITs with communist states quickly after
their transition—and thus in many cases before they were large recipients of military aid.
Fifth, it could be the case that investment considerations influence which countries the
United States signs BITs with, but that the country must first be an ally before even being
considered for a BIT. To test this theory, I estimated the base model and model with controls
after dropping observations where the state that did not receive any military aid from the United
States in the prior year. In both models, neither variable measuring investment considerations
achieves statistical significance, but Former Communist still has a positive effect that is
statistically significant at the 0.001 level.
Sixth, until now this paper has analyzed the onset of BITs being signed as the dependent
variable. There are five BITs, however, that the United States has signed that have never gone
into effect.20 It might thus be the case that different factors determined the onset of BITs actually
going into effect. To test this, I estimated regressions using the onset of BITs going into effect
between the United States and partner countries as the dependent variable. The results of doing
so are consistent with the initial results.
Taken together, the results of these robustness checks lend strong support to the theory
that political considerations influenced which countries the United States was willing to sign a
BITs. The Military Aid and Former Communist variables both have a consistently statistically
significant and positive effect on the likelihood that the United States would sign a BIT with a
given country. In contrast, there is little evidence that investment considerations had any effect
on the BITs that the United States signed: Investment Protection and US FDI Flows failed to
achieve statistical significance in any of the models estimated. The results thus suggest there is
much better evidence that the United States was motivated to sign BITs with countries based on
their political importance, and not their investment profile.
20
These BITs are with Haiti, Russia, Belarus, Uzbekistan, Nicaragua, and El Salvador.
22
IV. TESTING THE POLITICAL CONSEQUENCES OF BITS
The second step to testing my theory is to examine whether BITs have produced political
dividends for the United States. This part of the paper does exactly that. First, I describe the
empirical approach that was used for this analysis—life history matching—to try to produce
credible causal estimates of the political impact of BITs. Second, I discuss the three dependent
variables that measure political support for the United States that are used for this analysis.
Third, I report the primary results of this analysis, and fourth, I discuss the results of a series of
robustness checks that support these findings.
A. Methodological Approach
The difficulty in measuring the political benefits of BITs is that it requires finding a
quantitative method that makes it possible to estimate the causal effects of BITs on state-to-state
relationships while controlling for selection effects. Roughly fifteen years ago, scholars began to
empirically study the effect of treaty ratification on state behavior (Simmons 1999; Hathaway
2002). Although these early efforts were an important step forward that improved our
understanding of international legal agreements, many of these early efforts also had flaws in
their research design (Goodman and Jinks 2003; von Stein 2005). One specific problem was that
these efforts were not adequately able to control for selection effects (Hill 2010, 1161-62). That
is to say, countries that had chosen to ratify treaties were systematically different than countries
that had not, making it impossible to attribute observed differences in behavior to the treaties.
In an effort to help correct for these problems, a second wave of empirical scholarship on
international law has employed a variety of increasingly sophisticated quantitative methods (von
Stein 2005; Simmons and Hopkins 2005; Simmons 2009; Hill 2010; Lupu 2013a; Lupu 2013b).
One method that has been particularly popular is the use of matching. Although there are a
variety of matching methods available (King et al. 2012; Ho et al. 2007), the basic intuition is
that, if two observations are paired together that are as similar as possible in every way except
that one has received a particular treatment—for example, ratified a treaty—then systematic
differences in a dependent variable of interest can be attributed to that treatment.
Although matching has allowed scholars to make considerable advances in understanding
the influence of treaties on state behavior, matching time-series cross sectional data using
23
conventional methods poses two problems that researchers have almost entirely chosen to ignore.
First, conventional matching methods do not account for trends in data (Nielsen, n.d.). The
problem is that two countries might have the same value for a variable (for example, their level
of democracy) in a given year, but the countries could be trending in opposite directions (that is,
one country could be in the process of becoming more democratic while the other is sliding
towards autocracy). Conventional matching methods simply pair countries with similar values of
a variable in a given year, and thus are unable to take these trends into account. Second,
conventional matching methods introduce post-treatment bias. The problem is that, when trying
to estimate the causal effect of a given treatment, it is inappropriate to condition on covariates
that are measured after the treatment, because doing so may block the causal pathways that allow
the treatment to influence the outcome of interest (Blackwell and Glynn, n.d.). Conventional
matching methods introduce post-treatment bias because they find matches for treated
observations using values for covariates measured the year of each observation, even if that
observation occurs several years after the treatment.
To overcome these problems, I use a recently developed method that offers a promising
way to estimate the causal effects of international agreements that both accounts for trends in
data and also avoids introducing post-treatment bias. In a forthcoming paper, Nielsen and
Simmons (2014) introduce the idea of using treaty ratification episodes as the unit of analysis.
They define these episodes as the 11-year period surrounding ratification. For example, if Poland
ratified a particular treaty in 1990, the ratification episode would be from 1985 to 1995. Nielsen
and Simmons then match each ratification episode to an equally long non-ratification episode
using a new technique—life history matching—that makes it possible to match on multiple years
of data instead of one (Nielsen, n.d.).21 Nielsen and Simmons (2014) specifically match
observations using the first five years of data from each episode, and examine the effect of the
21
Life history matching is a technique first developed in Nielsen (n.d.). The basic insight
is that for each observation that appears in a dataset, that the values of covariates for multiple
prior years are collected. For example, if a covariate of interest in a TSCS dataset is GDP Per
Capita, separate variables would be created that are: GDP Per CapitaT, GDP Per CapitaT-1,
GDP Per CapitaT-2,, etc. Then if an observation in the dataset is “Brazil 1999”, Brazil’s GDP Per
capita for 1999 would be stored in GDP Per CapitaT, Brazil’s GDP Per capita for 1998 would be
stored in GDP Per CapitaT-2, Brazil’s GDP Per capita for 1997 would be stored in GDP Per
CapitaT-3, etc. Each of these variables is then included as a separate term during standard
matching procedures.
24
dependent variable of interest in the six years during and after ratification. In the Poland
example, Poland 1985-1995 may be matched with Hungary 1985-1995 based on their values for
covariates measured in 1985 through 1989, and then differences in the dependent variable of
interest from 1990 to 1995 would be analyzed. Since observations are matched on five years of
control variables that all occur prior to a treaty being formed, this approach is able to account for
trends in the data without introducing post-treatment bias. Given the advantages of this approach,
I follow Simmons and Nielsen (2014) and use BIT Formation Episodes as my unit of analysis,
and match these episodes using life-history matching.
B. Data
In addition to the data discussed in Part III.B., three additional dependent variables were
collected for this study. One difficulty of this project is finding dependent variables that measure
the strength of relationships between two states in a way that makes it possible to detect a benefit
for the developed state. That problem is that material rewards of treaty ratification are likely to
flow from developed to developing states. For example, Rwanda may expect that signing a BIT
with the United States will lead to being viewed more favorably when it is time for America to
decide how to distribute foreign aid dollars (Salacuse 2010, 442 n.75), but it would be patently
unreasonable for the United States to expect aid from Rwanda. That said, this does not mean that
the United States does not receive a political benefit from negotiating a BIT with Rwanda, it
simply means that the political benefits may be difficult to measure. The challenge is thus to find
dependent variables that capture the strength of a geopolitical relationship where the developed
state would be likely to be on the receiving end of the benefit. Three dependent variables that fit
this criterion have been identified for this study.
The first is a measure of the similarity in United Nations General Assembly voting
between the United States and the BIT partner. Voting in the UN is a public action that, although
it may often be purely symbolic, is at least possible to clearly measure as a proxy of closeness in
preferences and policies between states. Given these properties, previous international relations
scholarship has used UN voting as a way to directly measure changes in the relationships and
alliances between states over time (Voeten 2004; Voeten 2000; Gartzke 2000; Gartzke 1998).
One specific variable that has recently been developed to measure similarities between countries
25
in their UN voting is the difference in their UN Ideal Points (Baily, Strezhnev, and Voeten
2013). This variable is calculated by first using spatial modeling techniques to estimate each
country’s ideal point on votes taken in the General Assembly in a given year, and then estimating
the difference in ideal points between two countries in that year. The more similar two countries’
voting patterns are, the smaller the difference in their ideal points will be. Although there are
certainly problems with using UN Ideal Points to measure the strength of two countries’
relationship,22 the advantages of the measure still outweigh the drawbacks (Gartzke 1998, 14).
Specifically, all UN Members vote in the General Assembly in every year, which makes it
possible to look at changes in patterns over time. Moreover, UN voting occurs on a range of
topics in each year, meaning that UN voting is a broad-based measure of the similarities in
countries’ preferences. Finally, it has even previously been hypothesized that BITs may be
negotiated in part as a signal about future intentions in UN voting (Alvarez 2010, 621). As a
result, UN Ideal Points provides a promising way to measure year-to-year changes in the United
States’ strength of relationships with treaty partners that are a consequence of signing BITs. The
specific dependent variable I use is the six-year average of the difference in UN Ideal Points
between the United States and other countries.
The second dependent variable used to test whether the U.S. BITs program has produced
political dividends is the number of United States troops deployed in a country in a given year.
There has been a line of research examining the effects that the United States’ commercial
relationships with developing countries have had on the likelihood that the country will be
willing to allow U.S. troops to be deployed on their soil (Biglaiser and De Rousen 2009;
Biglaiser and De Rousen 2007). As Biglaiser and Rousen (2009) demonstrated, the United States
often must provide developing countries with economic incentives to be able to later station
troops within their borders. These incentives help to soften domestic opposition to the presence
of U.S. troops. Trade concessions are thus a strong predictor that U.S. troops will later be
22
It would be reasonable to argue that UN Voting is a somewhat crude and noisy
measure of the strength of relationships for at least four reasons. First, there are many
determinants of a country’s UN voting. Second, countries decide how to vote in the UN by
evaluating far more factors than simply whether a country with which they share a strong
relationship would prefer for them to vote one way or the other. Third, UN voting might be a
symbolic action that does not reflect other foreign policy preferences that are more important to a
country. Fourth, UN voting may be driven in part by the issues presented in that year, making
trends a function of the subject matter and not a function of changes in underlying preferences.
26
stationed within a given country. It would thus be reasonable to hypothesize that signing a BIT
with a developing country would make it more likely that that state will later allow U.S. troops
on its soil. Using data from Kane (2005), the dependent variable used to test this is the six-year
average number of troops the United States has stationed within a given country.
The third dependent variable used to test whether the U.S. BITs program has produced
political dividends is whether the partner country was a member of the Iraq War Coalition in
2003. At the time of the invasion of Iraq in March 2003, many traditional allies of the United
States in the developed world—such as Canada, France, and Germany—were not members of
the coalition supporting the war. Instead, the countries comprising the coalition were frequently
developing states. Prior research has suggested that these developing states were members of the
coalition because of their economic and strategic linkages with the United States (Newnham
2008). As a consequence, one test of whether BITs have been successful at improving
relationships with countries in the developing world is whether the prior presence of a BIT
resulted in a country being more likely to be part of the Iraq War Coalition. This dependent
variable is a dummy variable for the year 2003 only, and was based on information released by
the White House on March 27, 2003.23
C. Results
Following the procedure discussed in Part IV.A, the first step in my analysis was preprocessing the data using life history matching. The specific matching procedure I used was
nearest neighbor propensity score matching, implemented using the Matchit package for the R
programing language (Ho et al. 2009).24 BIT Formation Episodes were matched with nonformation episodes based on five years’ worth of values for all of the independent variables used
in Part III: Investment Protection, US FDI Outflows, Military Aid, Former Communist, Polity
23
Appendix E provides a complete list of the members of the Iraq War Coalition.
24
Following Nielsen and Simmons (2014), the matching produce retains all of the
treatment episodes. The treatment episodes are each matched to one control unit, and the
matching is “greedy” (which means that only control episode can only be used once). I also
follow Nielsen and Simmons (2014) by allowing for overlapping non-ratification to come from
the earlier history of the same country, but not allowing for overlapping ratification and nonratification episodes. Instead, ratification episodes take precedence. Since this allows for multiple
observations to be from the same country, I account for any non-independence between the
observations by calculating robust standard errors clustered by country.
27
Score, GDP Per Capita, Open Capital Acts, and Number of Prior BITs. A matched dataset was
created for each dependent variable, and the balance statistics from the matching procedures are
reported in Appendix F.25 The use of matching reduced the covariate imbalance between the two
groups—and thus makes it possible to produce less-biased estimates of the treatment effect of
having a BIT with the United States.
After matching, the next step was to run a series of linear regressions to estimate the
effect of BITs on the three dependent variables that measure the potential benefits the United
States may have received from the treaties. For each of the three dependent variables, a
regression was estimated using the matched dataset. To account for the possibility of any
remaining imbalance, I followed the standard procedure of including the treatment variable
(having signed a BIT with the United States) as well as all of the control variables that the
observations were matched on in the post-matching regressions (Ho et al. 2007). The results of
this analysis are reported in Figure 3. Figure 3 graphically presents the marginal effects of these
regressions for the treatment variable—having signed a BIT with the United States—with all
other variables held at their means. Given the small sample sizes, Figure 3 presents 90%
confidence intervals.26
25
The matched datasets produced for UN Ideal Points and Troop Deployment are
identical, but the matched dataset for the Iraq War Coalition is different because it excludes
observations where the focal year was after 2003.
26
Appendix G presents the results reported in Figure 3 in a standard regression table.
28
-0.50
-0.25
0
(p = 0.013)
0.25
0.50
0
0
Figure 3: Estimates of the Political Impact of BITs Signed by the United States
UN Ideal Points
Troop Deployment
Iraq Coalition
-1,500
500
0
500
(p = 0.762)
1,500
-0.50
-0.25
0
0.25
0.50
(p = 0.055)
Figure 3 depicts the estimated impact of the United States signing a Bilateral Investment Treaty
with a foreign state on three political outcomes. Each estimate is from a separate regression.
The results presented are the first differences as variables change from the minimum to
maximum value, with all other variables held at their means. Point estimates are represented by
dots, with the lines representing 90% confidence intervals. Statistically significant estimates are
shown with solid lines, while statistically insignificant estimates are shown with dotted lines.
As Figure 3 shows, having signed a BIT with the United States has a negative effect on
the difference in UN Ideal Points between the United States and the partner country that is
statistically significant at the 0.05 level. More specifically, having a BIT with the United States
makes a country vote an average of 0.33 points lower than the similar countries that comprise the
control group during the six years during and after a BIT is signed with the United States.
Obviously, it is important to put the magnitude of this effect in context. This variable is
measured on a scale of 0 to 5, with an average value of 3.10 and a standard deviation of 0.71
across the entire dataset used for this project. Or, perhaps more helpfully, between 1981 and
1991, Russia had an average difference in UN Ideal Point with the United States of 4.1, and an
average difference of 2.1 between 1992 and 2002. In other words, the end of the Cold War
resulted in a difference of roughly 2.0 and the estimated effect of a BIT is 0.32. That said, it is
worth noting that, although the size of this effect is modest, it is statistically significant at the
0.05 level despite the fact that the treatment and control groups are intentionally designed to be
as similar as possible along a number of observable relevant dimensions, with the exception that
the treatment group has signed a BIT with the United States. Given that the most recent
29
empirical study of the investment consequences of the United States BITs program (that this
author is aware of, at least) did not find even a small change in investment patterns resulting
from U.S. BITs (Peinhardt and Allee 2012), this is perhaps a surprising result.
Second, Figure 3 shows that having signed a BIT with the United States has a negative
effect on the average number of U.S. Troops deployed in the partner country. Countries that have
signed a BIT with the United States have an average of 174 troops less a year during the six year
period during and after ratification. This result, however, is far from being statistically
significant. Since the result is statistically indistinguishable from zero, little attention should be
paid to either the direction or magnitude of this effect.
Third, Figure 3 shows that having signed a BIT with the United States has a positive
effect on the likelihood that the partner country would participate in the Iraq War Coalition. In
fact, countries that have signed a BIT with the United States were 18% more likely to participate
in the Iraq War Coalition, and the result is statistically significant at the 0.1 level. Although this
result constitutes evidence of the BITs producing a major political benefit for the United States,
the result is not robust to a single one of the alternative model specifications discussed in the
next section, and as a result, it would likely be a mistake to place much faith in its validity.
D. Robustness Checks
To test the robustness of these results, I also estimated a series of regressions without
using the matching procedure employed in the previous section. The results of this analysis are
reported in Figure 4.27 Just like Figure 3, Figure 4 graphically presents the marginal effects of
having signed a BIT with the United States, with all other variables held at their means.
27
Appendix G presents the results reported in Figure 4 in a standard regression table.
30
Troop Deployment
-0.50
-0.25
0
0.25
0.50
-1,500
0
500
-0.25
0
1,500
-0.05
0.25
0.50
0
0.025
0.05
(p = 0.280)
-1,500
500
0
500
1,500
(p = 0.612)
-0.05
-0.025
0
0.025
0.05
(p = 0.294)
0
(C) Fixed Effects
-0.025
0
(p = 0.638)
(p = 0.001)
0
500
0
(B) Controls - 1 Year
0
(p = 0.001)
-0.50
Iraq Coalition
0
UN Ideal Points
0
(A) Controls - 5 Years
0
Figure 4: Robustness Checks of the Political Impact of BITs Signed by the United States
-0.50
-0.25
0
(p = 0.005)
0.25
0.50
-1,500
500
0
500
1,500
(p = 0.423)
Figure 4 depicts robustness checks estimated impact of the United States signing a Bilateral
Investment Treaty with a foreign state on three political outcomes. Each estimate is from a
separate regression. The results presented are the first differences as variables change from the
minimum to maximum value, with all other variables held at their means. Point estimates are
represented by dots, with the lines representing 90% confidence intervals. Statistically
significant estimates are shown with solid lines, while statistically insignificant estimates are
shown with dotted lines.
First, even if using matching to pre-process the data improves the balance between the
treatment and control group, one reasonable concern to have is that the matching procedure used
may bias the results because of the particular observations that were discarded. As a result, I
recreated my BIT Formation Episode research design, only did not pre-process the data by
matching. To do so, I estimated a series of regressions that included one observation for each
31
ratification episode, but also included all possible non-ratification episodes. The results of this
analysis are reported in Panel A of Figure 4. These results suggest that having signed a BIT with
the United States has a statistically significant negative effect on the difference between the
United States and the partner country’s UN Ideal Point that is nearly identical in magnitude to
the estimate produced via matching, but that is statistically significant at the 0.01 level. When
using this approach, however, having signed a BIT with the United States did not have a
statistically significant effect on either Troop Deployment or participation in the Iraq Coalition.
Second, another possible concern with the empirical approach that I have used is that
choosing to condition on five years’ worth of data for all of the control variables may have
biased the results. To account for this possibility, I instead use a seven-year BIT Formation
Episode, where I condition on one year of data, and then analyze the impact of BITs in the six
years during and after BIT formation. As with the previous robustness check, I include one
observation for each BIT Formation Episode, and all possible non-BIT Formation Episodes. The
results of this analysis are reported in Panel B of Figure 4. These results are nearly identical to
the results reported in Panel A: having signed a BIT with the United States has roughly the same
statistically significant, negative effect on the difference in UN Ideal Points, but does not have a
statistically significant effect on either of the other two dependent variables.
Third, another concern with the approach that I have used is that my estimates may be
biased due to failure to account for variables that influenced both the treatment and dependent
variable. Since it is certainly possible that both unobserved and observed factors are influencing
my results (after all, perhaps the greatest flaw of using matching to account for selection effects
is that it is possible to match observations only on observables), I also employ a standard
regression model that estimated the impact of having signed a BIT with the United States while
controlling for country and year fixed effects.28 This model employs a standard TSCS design,
where every country year in the dataset is included, and instead of the dependent variable being a
six-year average, the dependent variable is simply measured in the year of each observation. This
approach has the advantage of ensuring that there are not observed features of the countries that
signed the BITs or years in which they were signed that are driving the results. The results of this
28
The downside of this approach is that it does not allow controlling for variables that
vary over time—like Polity Score or GDP Per Capita—because their inclusion would introduce
post-treatment bias. As a result, the regressions reported in Panel C include country and year
fixed effects, but do not include any control variables.
32
analysis are reported in Panel C of Figure 4.29 Once again, having signed a BIT with the United
States has a negative and statistically significant effect on the difference in UN Ideal Points. The
magnitude of this effect is actually slightly larger than the size of the effect estimated using other
methods. Also, as with the other models estimated, the effect of the treatment on U.S. Troop
Deployment on the foreign country’s soil remains statistically insignificant.
Fourth, these results were all estimated by examining the political benefits the United
States has received from signing a BIT with a partner country. It is also worth considering
whether these results would be the same if the treatment variable was a BIT actually going into
effect. I thus re-estimated the results produced in Figure 3 and Figure 4, but the treatment
variable is a BIT between the United States and a partner country going into effect.30 The results
of this analysis reveal that there is not a statistically significant relationship between a BIT going
into effect and any of the three dependent variables (the one exception is the UN Ideal Point is
statistically significant at the 0.1 level in a single model). This suggests that any political
closeness the United States may receive from a BIT—as measured by the countries’ difference in
UN Ideal Points—occurs when the BIT is signed, but dissipates over time. Because the political
benefits occur after the treaty is signed, but not after it goes into effect, these results lend support
to my theory that the United States is motivated to sign BITs because doing so generates political
benefits independent of any increase in investment or investor protection.
In light of these robustness checks, the results in this part of the paper suggest that having
signed a BIT with the United States was associated with countries voting more similarly to the
United States in the United Nations, but likely did not make those countries more likely to have
U.S. Troops on their soil or to have been a member of the Iraq War Coalition. It may then fair to
say that the U.S. BITs program has produced modest political benefits, but (perhaps
unsurprisingly) has not radically altered the national security policy of partner countries.
29
Since the Iraq War Coalition dependent variable is measured in only 2003, the
structure of the data is not time-series cross-sectional. It is thus impossible to estimate a model
for this dependent variable while including country or year fixed effects, and as a consequence,
Panel C only includes results for the other two dependent variables.
30
Appendix H presents these results in a standard regression table.
33
V. CONCLUSION
Scholars studying the United States’ BITs program have consistently argued that it was
motivated by a desire to help promote the development of international law that is friendly to
investment, and to help protect American investments abroad. This paper challenges that view of
the U.S. BITs program. Instead, I argue that BITs have been a foreign policy tool that the United
States has used when it wanted a low cost way to signal that it would like to improve its
relationship with a specific developing country. As a result, political considerations should help
to explain the countries with which the United States signed BITs; and if the BIT program has
been effective, BITs should have produced political benefits. This paper rigorously tested that
theory by both showing that political considerations are better than investment considerations at
predicting BIT formation, and that BITs are associated with at least modest political benefits.
Of course, a few caveats are in order. First, although the results presented in this paper
suggest that investment considerations did not have a statistically significant impact on the
likelihood of BIT onset, this does not mean that investment considerations did not play a role in
specific cases. Instead, the results simply suggest that political considerations are better
predictors of BIT onset on average. Second, the same is true of the change in UN Ideal Points
after a BIT is signed. The result of this paper should not be taken to mean that a change occurred
in every case, or that a change would occur with any country the United States signed a BIT with
in the future. Third, these results should not be interpreted strictly causally. Although the results
in this paper results show that having a BIT with the United States in effect is associated with a
statistically significant decrease in the difference between the United States and the treaty
partner’s UN Ideal Point, this might not be caused by the formation of the BIT. The point of
using matching and linear regression is to try to account for other factors that may have caused
the change in the dependent variable, but it is always possible that there are other variables that
were not controlled for in the model—and which may not even be observable—that are in part
driving the results. Demonstrating that signing a BIT is associated with a change in political
outcomes, even if it is not causal, does lend support to the overall argument advanced by this
paper that the United States used BITs with the goal of improving relationships.
With that said, these findings still show that commentators should alter the way they
describe, discuss, and evaluate the United States’ BITs program. Not only do the results of this
34
paper suggest that the narrative that the United States signed BITs to protect and promote
investment be modified, but they also suggest that looking solely at the effect of BITs on FDI
flows and investor protections may be the wrong way to measure their effectiveness. Instead, this
paper demonstrates that it is time to acknowledge the political motivations of the program, and to
start evaluating the program at least partially on political dividends that may it have produced.
35
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40
APPENDIXES
Appendix A: Bilateral Investment Treaties Signed by the United States
BIT Partner
Signed
Into Effect
BIT Partner
Signed
Into Effect
Panama†
10/27/82
05/30/91 Ecuador
08/27/93
05/11/97
Senegal
12/06/83
10/25/90 Belarus
01/15/94
NA
Haiti
12/13/83
NA Jamaica
02/04/94
03/07/97
D.R. Congo
08/03/84
07/28/89 Ukraine
03/04/94
11/16/96
Morocco
07/22/85
05/29/91 Georgia
03/07/94
08/17/97
Turkey
12/03/85
05/18/90 Estonia
04/19/94
02/16/97
Cameroon
02/26/86
04/06/89 Trinidad & Tobago
09/26/94
12/26/96
Egypt
03/11/86
06/27/92 Mongolia
10/06/94
01/01/97
Bangladesh
03/12/86
07/25/89 Uzbekistan
12/16/94
NA
Grenada
05/02/86
03/03/89 Albania
01/11/95
01/04/98
Rep. Congo
02/12/90
08/13/94 Latvia
01/13/95
12/26/96
Poland
03/21/90
08/06/94 Honduras
07/01/95
07/11/01
Tunisia
05/15/90
02/07/93 Nicaragua
07/01/95
NA
Sri Lanka
09/20/91
05/01/93 Croatia
07/13/96
06/20/01
Czech Republic
10/22/91
12/19/92 Jordan
07/02/97
06/12/03
Slovakia
10/22/91
12/19/92 Azerbaijan
08/01/97
08/02/01
Argentina
11/14/91
10/20/94 Lithuania
01/14/98
11/22/01
Kazakhstan
05/19/92
01/12/94 Bolivia
04/17/98
06/06/01
Romania
05/28/92
01/15/94 Mozambique
12/01/98
03/03/05
Russia
06/17/92
NA El Salvador
03/10/99
NA
Armenia
09/23/92
03/29/96 Bahrain
09/29/99
05/30/01
Bulgaria
09/23/92
06/02/94 Uruguay
11/04/05
11/01/06
Kyrgyzstan
01/19/93
01/12/94 Rwanda
02/19/08
01/01/12
Moldova
04/21/93
11/25/94
- This table lists all BITs signed by the United States as of 12/31/2013.
- “NA” is used for BITs that have been signed but have not gone into effect.
- † an amended BIT was signed June 1, 2000 and went into effect May 14, 2001.
- Source: <http://www.state.gov/e/eb/ifd/bit/117402.htm#7> (last visited 12/31/2013).
41
Appendix B: Senate Consideration of Bilateral Investment Treaties
Country
Introduced
Passed
Country
Introduced
D.R. Congo
3/25/1986
10/20/88 Jamaica
9/19/1994
Morocco
3/25/1986
10/20/88 Belarus
9/23/1994
Senegal
3/25/1986
10/20/88 Estonia
9/26/1994
Turkey
3/25/1986
10/20/88 Ukraine
9/26/1994
Cameroon
5/28/1986
10/20/88 Mongolia
6/26/1995
Bangladesh
5/30/1986
10/20/88 Georgia
7/10/1995
Egypt
6/2/1986
10/20/88 Latvia
7/10/1995
Grenada
6/3/1986
10/20/88 Trinidad & Tobago
7/11/1995
Panama
3/25/1986
10/28/90 Albania
11/6/1995
Poland
6/19/1990
10/28/90 Uzbekistan
2/28/1996
R. Congo
2/19/1991
8/11/92 Bahrain
5/23/2000
Tunisia
5/17/1991
8/11/92 Bolivia
5/23/2000
Sri Lanka
8/20/1991
8/11/92 Croatia
5/23/2000
Czech Republic
6/2/1992
8/11/92 El Salvador
5/23/2000
Slovakia
6/2/1992
8/11/92 Honduras
5/23/2000
Russia
7/28/1982
8/11/92 Jordan
5/23/2000
Kazakhstan
9/7/1993
10/21/93 Mozambique
5/23/2000
Romania
8/3/1992
11/17/93 Lithuania
9/5/2000
Argentina
1/19/1993
11/17/93 Azerbaijan
9/12/2000
Bulgaria
1/19/1993
11/17/93 Uruguay
4/4/2006
Armenia
9/8/1993
11/17/93 Rwanda
11/20/2008
Kyrgyzstan
9/8/1993
11/17/93 Haiti
3/26/1986
Moldova
9/8/1993
11/17/93 Nicaragua
6/26/2000
Ecuador
9/10/1993
11/17/93
- This table lists all BITs signed by the United States as of 12/31/2013.
- “NA” is used for BITs that have been signed but have not gone into effect.
- The date “Introduced” is the date that the treaty was introduced to the Senate.
- The “Passed” date is the date that each BIT was approved by the Senate.
- All BITs were passed by voice votes.
42
Passed
6/27/96
6/27/96
6/27/96
6/27/96
6/27/96
6/27/96
6/27/96
6/27/96
6/27/96
10/18/00
10/18/00
10/18/00
10/18/00
10/18/00
10/18/00
10/18/00
10/18/00
10/18/00
10/18/00
9/12/06
9/26/11
NA
NA
US FDI
Outflow
Military Aid
Former
Communist
Polity Score
GDP Per Capita
Open Capital
Accounts
Prior BITs
Investment Protection
US FDI Outflow
Military Aid
Former Communist
Polity Score
GDP Per Capita
Open Capital Accounts
Prior BITs
Investment
Protection
Appendix C: Correlation Matrix For Survival Analysis
1.00
0.21
0.12
-0.11
0.23
0.44
0.37
0.23
1.00
0.07
-0.14
0.25
0.45
0.21
0.32
1.00
0.04
0.31
-0.07
0.02
0.12
1.00
0.08
-0.08
-0.07
0.08
1.00
0.17
0.05
0.14
1.00
0.40
0.17
1.00
0.11
1.00
43
Appendix D: Regression Results - Part 1
(1)
Investment Protect.
US FDI Outflows
Military Aid
Former Communist
Polity Score
GDP Per Capita
Open Capital Acts.
Prior BITs
(2)
(3)
(4)
(5)
(6)
Base
Base
Rare
Events
Rare
Events
Random
Effects
Random
Effects
-0.038
(0.075)
0.082
(0.069)
0.059**
(0.024)
2.529***
(0.420)
-0.079
(0.085)
0.027
(0.078)
0.049*
(0.027)
2.354***
(0.442)
0.030
(0.028)
0.027
(0.159)
0.079
(0.138)
0.033**
(0.017)
-0.039
(0.083)
0.081
(0.072)
0.057**
(0.024)
2.522***
(0.396)
-0.079
(0.095)
0.027
(0.080)
0.046*
(0.025)
2.326***
(0.419)
0.028
(0.027)
0.027
(0.175)
0.082
(0.136)
0.035**
(0.017)
-0.005
(0.103)
0.083
(0.095)
0.082**
(0.036)
3.357***
(0.801)
-0.033
(0.120)
0.040
(0.106)
0.077*
(0.040)
3.407***
(0.967)
0.040
(0.039)
-0.111
(0.294)
0.178
(0.206)
0.052*
(0.028)
3,735
3,735
Observations
3,735
3,735
3,735
3,735
- Robust standard errors clustered on country in parentheses.
- All modes include Time, Time2, and Time3.
- *p<0.1, **p<0.05,****p<0.01.
44
Appendix D: Regression Results - Part 2
Investment Protect.
US FDI Outflows
Military Aid
Former Communist
(7)
(8)
Invest
Squ.
Invest
Squ.
0.216
(0.438)
0.079
(0.071)
0.057**
(0.024)
2.578***
(0.437)
0.177
(0.446)
0.023
(0.081)
0.047*
(0.028)
2.404***
(0.455)
0.031
(0.028)
0.030
(0.161)
0.089
(0.133)
0.033*
(0.017)
-0.023
(0.038)
Polity Score
GDP Per Capita
Open Capital Acts.
Prior BITs
Investment Protect.2
-0.023
(0.037)
(9)
(10)
Drop
Drop
Form.
Form.
Communist Communist
-0.026
(0.101)
0.046
(0.083)
0.099**
(0.040)
-0.060
(0.110)
-0.002
(0.106)
0.097**
(0.043)
(12)
Drop No
Military
Aid
-0.026
(0.090)
0.079
(0.071)
-0.073
(0.093)
0.024
(0.081)
2.265***
(0.472)
2.110***
(0.489)
0.016
(0.031)
0.030
(0.184)
0.167
(0.145)
0.031
(0.020)
2,247
2,247
0.013
(0.033)
0.043
(0.198)
0.098
(0.158)
0.025
(0.019)
Observations
3,735
3,735
3,452
3,452
- Robust standard errors clustered on country in parentheses.
- All modes include Time, Time2, and Time3.
- *p<0.1, **p<0.05,****p<0.01.
45
(11)
Drop No
Military
Aid
Appendix D: Regression Results - Part 3
Investment Protect.
US FDI Outflows
Military Aid
Former Communist
(13A)
Interact
Model
(13B)
Interact
Model
(13C)
Interact
Model
(14A)
Interact
Model
(14B)
Interact
Model
(14C)
Interact
Model
0.011
(0.102)
0.080
(0.068)
0.063**
(0.025)
3.072***
(0.798)
-0.038
(0.075)
0.066
(0.079)
0.060**
(0.024)
2.319***
(0.794)
-0.007
(0.082)
0.070
(0.072)
0.097**
(0.039)
3.465***
(0.724)
-0.028
(0.108)
0.024
(0.078)
0.053*
(0.028)
2.935***
(0.818)
0.030
(0.028)
0.023
(0.159)
0.082
(0.140)
0.034**
(0.017)
-0.079
(0.085)
0.011
(0.089)
0.049*
(0.028)
2.134***
(0.821)
0.030
(0.028)
0.029
(0.158)
0.077
(0.139)
0.033*
(0.017)
-0.047
(0.093)
0.007
(0.081)
0.094**
(0.042)
3.480***
(0.759)
0.028
(0.028)
0.038
(0.166)
0.096
(0.141)
0.040**
(0.017)
Polity Score
GDP Per Capita
Open Capital Acts.
Prior BITs
Invest. Protect * Form. Com.
US FDI Outflows* Form. Com.
-0.105
(0.141)
-0.113
(0.140)
0.045
(0.148)
Military Aid* Form. Com.
0.047
(0.154)
-0.097*
(0.054)
Observations
3,735
3,735
3,735
- Robust standard errors clustered on country in parentheses.
- All modes include Time, Time2, and Time3.
- *p<0.1, **p<0.05,****p<0.01.
46
-0.117**
(0.055)
3,735
3,735
3,735
Appendix D: Regression Results - Part 4
Investment Protect.
US FDI Outflows
Military Aid
Former Communist
(15)
DV is BITs
in Effect
(16)
DV is BITs
in Effect
0.042
(0.088)
0.080
(0.063)
0.095***
(0.032)
2.262***
(0.386)
-0.007
(0.104)
-0.011
(0.077)
0.067*
(0.039)
1.955***
(0.455)
0.046
(0.036)
-0.253
(0.196)
0.394**
(0.160)
0.054***
(0.015)
Polity Score
GDP Per Capita
Open Capital Acts.
Prior BITs
Observations
3,971
3,971
- Robust standard errors clustered on country in parentheses.
- All modes include Time, Time2, and Time3.
- *p<0.1, **p<0.05,****p<0.01.
47
Appendix E: Members of the Iraq War Coaltion
Afghanistan
Hungary
Poland
Albania
Iceland
Portugal
Angola
Italy
Romania
Australia
Japan
Rwanda
Azerbaijan
Kuwait
Singapore
Bulgaria
Latvia
Slovakia
Colombia
Lithuania
Solomon Islands
Czech Republic
Macedonia
South Korea
Denmark
Marhall Islands
Spain
Dominican Republic
Micronesia
Tonga
El Salvador
Mongolia
Turkey
Eritrea
Netherlands
Uganda
Estonia
Nicaragua
Ukraine
Ethipia
Palau
United Kingdom
Georgia
Panama
United States
Honduras
Philippines
Uzbekistan
- Members of the Iraq War Coalition reported by the White House on 3/27/2003.
- Source: <http://georgewbushwhitehouse.archives.gov/infocus/iraq/news/
20030327-10.html> (last visited April 6, 2013).
48
Appendix F: Balance Statistics for the Matched Samples
Sample Size
Treatment Units
Control Units
Mean Distance – Treated
Mean Distance – Control
Balance Improvement
UN
Ideal Points
Full
Matched
Sample
Sample
2,361
78
39
39
2,322
39
0.127
0.127
0.015
0.112
86%
49
Troop
Deployment
Full
Matched
Sample
Sample
2,361
78
39
39
2,322
39
0.127
0.127
0.015
0.112
86%
Iraq
Coalition
Full
Matched
Sample
Sample
2,795
88
44
44
2,751
44
0.176
0.176
0.013
0.139
77%
Appendix G: Regression Results Reported in Figure 4 and Figure 5
Figure 4 - Matching
Prior BIT
Controls
Fixed Effects
N
(A) Five Years of Controls
Prior BIT
Controls
Fixed Effects
N
(B) One Year of Controls
Prior BIT
Controls
Fixed Effects
N
(C) Fixed Effects
Prior BIT
UN
Ideal Points
(1)
Troop
Deployment
(2)
Iraq
Coalition
(3)
-0.331**
(0.130)
-173.953
(572.088)
0.182*
(0.093)
5-Years
No
78
(4)
5-Years
No
78
(5)
5-Years
No
88
(6)
-0.302***
(0.091)
-203.200
(431.450)
0.002
(0.006)
5-Years
No
3,671
(7)
5-Years
No
2,613
(8)
5-Years
No
164
(9)
-0.338***
(0.096)
-231.190
(454.181)
0.006
(0.006)
1-Year
No
3,671
(10)
1-Year
No
2,613
(11)
1-Year
No
164
-0.429***
(0.149)
-294.220
(366.008)
-
Controls
No
No
Fixed Effects
Country; Year
Country; Year
N
4,308
3,347
- Robust standard errors clustered on country in parentheses.
- Controls Include: Investment Protection; US FDI Flows; Military Aid; Former Communist;
Polity Score; GDP Per Capita; Open Capital Acts; Prior BITs.
- *p<0.1, **p<0.05,****p<0.01.
50
Appendix H: Regression Results Reported in Figure 6
(A) Matching
Prior BIT
Controls
Fixed Effects
N
(B) Five Years of Controls
Prior BIT
Controls
Fixed Effects
N
(C) One Year of Controls
Prior BIT
Controls
Fixed Effects
N
(D) Fixed Effects
Prior BIT
UN
Ideal Points
(1)
Troop
Deployment
(2)
Iraq
Coalition
(3)
-0.064
(0.178)
-2,933.215
(1,934.050)
0.134
(0.111)
5-Years
No
74
(4)
5-Years
No
74
(5)
5-Years
No
76
(6)
-0.125
(0.095)
-115.111
(354.291)
0.001
(0.009)
5-Years
No
3,907
(7)
5-Years
No
2,813
(8)
5-Years
No
164
(9)
-0.166*
(0.099)
99.161
(317.583)
0.006
(0.008)
1-Year
No
3,907
(10)
1-Year
No
2,813
(11)
1-Year
No
164
-0.162
(0.118)
-683.883
(470.206)
-
No
No
Controls
Country; Year
Country; Year
Fixed Effects
N
4,308
3,347
- Robust standard errors clustered on country in parentheses.
- Controls Include: Investment Protection; US FDI Flows; Military Aid; Former Communist;
Polity Score; GDP Per Capita; Open Capital Acts; Prior BITs.
- *p<0.1, **p<0.05,****p<0.01.
51
Readers with comments should address them to:
Professor Adam Chilton
[email protected]
Chicago Working Papers in Law and Economics
(Second Series)
For a listing of papers 1–600 please go to Working Papers at
http://www.law.uchicago.edu/Lawecon/index.html
601.
602.
603.
604.
605.
606.
607
608.
609.
610.
611.
612.
613.
614.
615.
616.
617.
618.
619.
620.
621.
622.
623.
624.
625.
626.
627.
628.
629.
630.
631.
632.
633.
634.
635.
636.
637.
638.
639
640.
David A. Weisbach, Should Environmental Taxes Be Precautionary? June 2012
Saul Levmore, Harmonization, Preferences, and the Calculus of Consent in Commercial and Other
Law, June 2012
David S. Evans, Excessive Litigation by Business Users of Free Platform Services, June 2012
Ariel Porat, Mistake under the Common European Sales Law, June 2012
Stephen J. Choi, Mitu Gulati, and Eric A. Posner, The Dynamics of Contrat Evolution, June 2012
Eric A. Posner and David Weisbach, International Paretianism: A Defense, July 2012
Eric A. Posner, The Institutional Structure of Immigration Law, July 2012
Lior Jacob Strahilevitz, Absolute Preferences and Relative Preferences in Property Law, July 2012
Eric A. Posner and Alan O. Sykes, International Law and the Limits of Macroeconomic
Cooperation, July 2012
M. Todd Henderson and Frederick Tung, Reverse Regulatory Arbitrage: An Auction Approach to
Regulatory Assignments, August 2012
Joseph Isenbergh, Cliff Schmiff, August 2012
James Melton and Tom Ginsburg, Does De Jure Judicial Independence Really Matter?, September
2014
M. Todd Henderson, Voice versus Exit in Health Care Policy, October 2012
Gary Becker, François Ewald, and Bernard Harcourt, “Becker on Ewald on Foucault on Becker”
American Neoliberalism and Michel Foucault’s 1979 Birth of Biopolitics Lectures, October 2012
William H. J. Hubbard, Another Look at the Eurobarometer Surveys, October 2012
Lee Anne Fennell, Resource Access Costs, October 2012
Ariel Porat, Negligence Liability for Non-Negligent Behavior, November 2012
William A. Birdthistle and M. Todd Henderson, Becoming the Fifth Branch, November 2012
David S. Evans and Elisa V. Mariscal, The Role of Keyword Advertisign in Competition among
Rival Brands, November 2012
Rosa M. Abrantes-Metz and David S. Evans, Replacing the LIBOR with a Transparent and
Reliable Index of interbank Borrowing: Comments on the Wheatley Review of LIBOR Initial
Discussion Paper, November 2012
Reid Thompson and David Weisbach, Attributes of Ownership, November 2012
Eric A. Posner, Balance-of-Powers Arguments and the Structural Constitution, November 2012
David S. Evans and Richard Schmalensee, The Antitrust Analysis of Multi-Sided Platform
Businesses, December 2012
James Melton, Zachary Elkins, Tom Ginsburg, and Kalev Leetaru, On the Interpretability of Law:
Lessons from the Decoding of National Constitutions, December 2012
Jonathan S. Masur and Eric A. Posner, Unemployment and Regulatory Policy, December 2012
David S. Evans, Economics of Vertical Restraints for Multi-Sided Platforms, January 2013
David S. Evans, Attention to Rivalry among Online Platforms and Its Implications for Antitrust
Analysis, January 2013
Omri Ben-Shahar, Arbitration and Access to Justice: Economic Analysis, January 2013
M. Todd Henderson, Can Lawyers Stay in the Driver’s Seat?, January 2013
Stephen J. Choi, Mitu Gulati, and Eric A. Posner, Altruism Exchanges and the Kidney Shortage,
January 2013
Randal C. Picker, Access and the Public Domain, February 2013
Adam B. Cox and Thomas J. Miles, Policing Immigration, February 2013
Anup Malani and Jonathan S. Masur, Raising the Stakes in Patent Cases, February 2013
Arial Porat and Lior Strahilevitz, Personalizing Default Rules and Disclosure with Big Data,
February 2013
Douglas G. Baird and Anthony J. Casey, Bankruptcy Step Zero, February 2013
Oren Bar-Gill and Omri Ben-Shahar, No Contract? March 2013
Lior Jacob Strahilevitz, Toward a Positive Theory of Privacy Law, March 2013
M. Todd Henderson, Self-Regulation for the Mortgage Industry, March 2013
Lisa Bernstein, Merchant Law in a Modern Economy, April 2013
Omri Ben-Shahar, Regulation through Boilerplate: An Apologia, April 2013
641.
642.
643.
644.
645.
646.
647.
648.
649.
650.
651.
652.
653.
654.
655.
656.
657.
658.
659.
660.
661.
662.
663.
664.
665.
666.
667.
668.
669.
670.
671.
672.
Anthony J. Casey and Andres Sawicki, Copyright in Teams, May 2013
William H. J. Hubbard, An Empirical Study of the Effect of Shady Grove v. Allstate on Forum
Shopping in the New York Courts, May 2013
Eric A. Posner and E. Glen Weyl, Quadratic Vote Buying as Efficient Corporate Governance, May
2013
Dhammika Dharmapala, Nuno Garoupa, and Richard H. McAdams, Punitive Police? Agency
Costs, Law Enforcement, and Criminal Procedure, June 2013
Tom Ginsburg, Jonathan S. Masur, and Richard H. McAdams, Libertarian Paternalism, Path
Dependence, and Temporary Law, June 2013
Stephen M. Bainbridge and M. Todd Henderson, Boards-R-Us: Reconceptualizing Corporate
Boards, July 2013
Mary Anne Case, Is There a Lingua Franca for the American Legal Academy? July 2013
Bernard Harcourt, Beccaria’s On Crimes and Punishments: A Mirror of the History of the
Foundations of Modern Criminal Law, July 2013
Christopher Buccafusco and Jonathan S. Masur, Innovation and Incarceration: An Economic
Analysis of Criminal Intellectual Property Law, July 2013
Rosalind Dixon & Tom Ginsburg, The South African Constitutional Court and Socio-economic
Rights as “Insurance Swaps”, August 2013
Maciej H. Kotowski, David A. Weisbach, and Richard J. Zeckhauser, Audits as Signals, August
2013
Elisabeth J. Moyer, Michael D. Woolley, Michael J. Glotter, and David A. Weisbach, Climate
Impacts on Economic Growth as Drivers of Uncertainty in the Social Cost of Carbon, August
2013
Eric A. Posner and E. Glen Weyl, A Solution to the Collective Action Problem in Corporate
Reorganization, September 2013
Gary Becker, François Ewald, and Bernard Harcourt, “Becker and Foucault on Crime and
Punishment”—A Conversation with Gary Becker, François Ewald, and Bernard Harcourt: The
Second Session, September 2013
Edward R. Morrison, Arpit Gupta, Lenora M. Olson, Lawrence J. Cook, and Heather Keenan,
Health and Financial Fragility: Evidence from Automobile Crashes and Consumer Bankruptcy,
October 2013
Evidentiary Privileges in International Arbitration, Richard M. Mosk and Tom Ginsburg, October
2013
Voting Squared: Quadratic Voting in Democratic Politics, Eric A. Posner and E. Glen Weyl,
October 2013
The Impact of the U.S. Debit Card Interchange Fee Regulation on Consumer Welfare: An Event
Study Analysis, David S. Evans, Howard Chang, and Steven Joyce, October 2013
Lee Anne Fennell, Just Enough, October 2013
Benefit-Cost Paradigms in Financial Regulation, Eric A. Posner and E. Glen Weyl, April 2014
Free at Last? Judicial Discretion and Racial Disparities in Federal Sentencing, Crystal S. Yang,
October 2013
Have Inter-Judge Sentencing Disparities Increased in an Advisory Guidelines Regime? Evidence
from Booker, Crystal S. Yang, March 2014
William H. J. Hubbard, A Theory of Pleading, Litigation, and Settlement, November 2013
Tom Ginsburg, Nick Foti, and Daniel Rockmore, “We the Peoples”: The Global Origins of
Constitutional Preambles, April 2014
Lee Anne Fennell and Eduardo M. Peñalver, Exactions Creep, December 2013
Lee Anne Fennell, Forcings, December 2013
Stephen J. Choi, Mitu Gulati, and Eric A. Posner, A Winner’s Curse?: Promotions from the Lower
Federal Courts, December 2013
Jose Antonio Cheibub, Zachary Elkins, and Tom Ginsburg, Beyond Presidentialism and
Parliamentarism, December 2013
Lisa Bernstein, Trade Usage in the Courts: The Flawed Conceptual and Evidentiary Basis of
Article 2’s Incorporation Strategy, November 2013
Roger Allan Ford, Patent Invalidity versus Noninfringement, December 2013
M. Todd Henderson and William H.J. Hubbard, Do Judges Follow the Law? An Empirical Test of
Congressional Control over Judicial Behavior, January 2014
Lisa Bernstein, Copying and Context: Tying as a Solution to the Lack of Intellectual Property
Protection of Contract Terms, January 2014
673.
674.
675.
676.
677.
678.
679.
680.
681.
682.
683.
684.
685.
686.
687.
688.
689.
690.
691.
692.
693.
694.
695.
696.
697.
698.
699.
700.
701.
702.
703.
704.
705.
706.
707.
708.
Eric A. Posner and Alan O. Sykes, Voting Rules in International Organizations, January 2014
Tom Ginsburg and Thomas J. Miles, The Teaching/Research Tradeoff in Law: Data from the
Right Tail, February 2014
Ariel Porat and Eric Posner, Offsetting Benefits, February 2014
Nuno Garoupa and Tom Ginsburg, Judicial Roles in Nonjudicial Functions, February 2014
Matthew B. Kugler, The Perceived Intrusiveness of Searching Electronic Devices at the Border:
An Empirical Study, February 2014
David S. Evans, Vanessa Yanhua Zhang, and Xinzhu Zhang, Assessing Unfair Pricing under
China's Anti-Monopoly Law for Innovation-Intensive Industries, March 2014
Jonathan S. Masur and Lisa Larrimore Ouellette, Deference Mistakes, March 2014
Omri Ben-Shahar and Carl E. Schneider, The Futility of Cost Benefit Analysis in Financial
Disclosure Regulation, March 2014
Yun-chien Chang and Lee Anne Fennell, Partition and Revelation, April 2014
Tom Ginsburg and James Melton, Does the Constitutional Amendment Rule Matter at All?
Amendment Cultures and the Challenges of Measuring Amendment Difficulty, May 2014
Eric A. Posner and E. Glen Weyl, Cost-Benefit Analysis of Financial Regulations: A Response to
Criticisms, May 2014
Adam B. Badawi and Anthony J. Casey, The Fannie and Freddie Bailouts Through the Corporate
Lens, March 2014
David S. Evans, Economic Aspects of Bitcoin and Other Decentralized Public-Ledger Currency
Platforms, April 2014
Preston M. Torbert, A Study of the Risks of Contract Ambiguity, May 2014
Adam S. Chilton, The Laws of War and Public Opinion: An Experimental Study, May 2014
Robert Cooter and Ariel Porat, Disgorgement for Accidents, May 2014
David Weisbach, Distributionally-Weighted Cost Benefit Analysis: Welfare Economics Meets
Organizational Design, June 2014
Robert Cooter and Ariel Porat, Lapses of Attention in Medical Malpractice and Road Accidents,
June 2014
William H. J. Hubbard, Nuisance Suits, June 2014
Saul Levmore & Ariel Porat, Credible Threats, July 2014
Douglas G. Baird, One-and-a-Half Badges of Fraud, August 2014
Adam Chilton and Mila Versteeg, Do Constitutional Rights Make a Difference? August 2014
Maria Bigoni, Stefania Bortolotti, Francesco Parisi, and Ariel Porat, Unbundling Efficient Breach,
August 2014
Adam S. Chilton and Eric A. Posner, An Empirical Study of Political Bias in Legal Scholarship,
August 2014
David A. Weisbach, The Use of Neutralities in International Tax Policy, August 2014
Eric A. Posner, How Do Bank Regulators Determine Capital Adequacy Requirements? September
2014
Saul Levmore, Inequality in the Twenty-First Century, August 2014
Adam S. Chilton, Reconsidering the Motivations of the United States? Bilateral Investment Treaty
Program, July 2014
Dhammika Dharmapala and Vikramaditya S. Khanna, The Costs and Benefits of Mandatory
Securities Regulation: Evidence from Market Reactions to the JOBS Act of 2012, August 2014
Dhammika Dharmapala, What Do We Know About Base Erosion and Profit Shifting? A Review
of the Empirical Literature, September 2014
Dhammika Dharmapala, Base Erosion and Profit Shifting: A Simple Conceptual Framework,
September 2014
Lee Anne Fennell and Richard H. McAdams, Fairness in Law and Economics: Introduction,
October 2014
Thomas J. Miles and Adam B. Cox, Does Immigration Enforcement Reduce Crime? Evidence
from 'Secure Communities', October 2014
Ariel Porat and Omri Yadlin, Valuable Lies, October 2014
John Bronsteen, Christopher Buccafusco and Jonathan S. Masur, Well-Being and Public Policy,
November 2014
David S. Evans, The Antitrust Analysis of Rules and Standards for Software Platforms, November
2014
709.
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E. Glen Weyl and Alexander White, Let the Best 'One' Win: Policy Lessons from the
New Economics of Platforms, December 2014
Lee Anne Fennell, Agglomerama, December 2014
Anthony J. Casey and Aziz Z. Huq, The Article III Problem in Bankruptcy, December
2014
Adam S. Chilton and Mila Versteeg, The Inefficacy of Constitutional Torture
Prohibitions, December 2014
Lee Anne Fennell and Richard H. McAdams, The Distributive Deficit in Law and
Economics, January 2015
Omri Ben-Shahar and Kyle D. Logue, Under the Weather: Government Insurance and the
Regulation of Climate Risks, January 2015
Adam M. Samaha and Lior Jacob Strahilevitz, Don't Ask, Must Tell—and Other
Combinations, January 2015
Jonathan S. Masur and Eric A. Posner, Toward a Pigovian State, February 2015
Lee Fennell, Slicing Spontaneity, February 2015
Steven Douglas Smith, Michael B. Rappaport, William Baude, and Stephen E. Sachs,
The New and Old Originalism: A Discussion, February 2015
Adam S. Chilton and Eric A. Posner, The Influence of History on States’ Compliance
with Human Rights Obligations, March 2015
Saul Levmore and Ariel Porat, No-Haggle Agreements, March 2015
Saul Levmore and Ariel Porat, Rethinking Threats, March 2015
Adam Chilton, The Politics of the United States’ Bilateral Investment Treaty Program,
March 2015