The Uses and Abuses of Foreign Aid

Abstract

Research shows that foreign aid promotes economic development in democracies but not in autocracies. Although explanations for this phenomenon vary, a common theme is that autocracies are more likely to misuse aid. We provide evidence of such misuse, showing that autocracies are more likely than democracies to divert development aid to the military. Theoretically, we build on “selectorate” models in which autocrats respond to aid by contracting civil liberties. Because this strategy requires military capacity, autocracies but not democracies should spend aid on the military. We support this hypothesis empirically, providing further evidence that autocracies misuse foreign aid.

Keywords

development assistance aid fungibility political institutions military spending

Between 1960 and 2010, rich countries gave poor ones more than three trillion dollars in development aid.¹ The return on this investment has been poor: on average, foreign aid has failed to promote savings, investment, and growth in recipient countries (Doucouliagos and Paldam 2009). For example, while sub-Saharan Africa received $714 billion in development aid from 1960 to 2006 (Easterly 2008, 14), its per capita income grew by less than 1 percent per year over this period,² and its poverty rate has scarcely changed (Chen and Ravallion 2004). These grim statistics beg the question: Why has development aid failed to achieve its goals?

One possible answer is that it is simply not used for its intended purpose. Research shows that aid is fungible (Feyzioglu, Swaroop, and Zhu 1998): that is, aid given for one purpose allows governments to shift resources to other uses. If these other uses do not encourage economic growth or development, neither will aid. A recent New York Times article on Uganda illustrates this point.³ Although Uganda has received considerable foreign aid designated for health care, its hospitals remain starved for resources. This is because foreign aid has allowed the government to cut its own health care spending: specifically, for each additional aid dollar received, Uganda cut its health care spending by 57 cents (IHME 2010). Although it is not clear where the budgetary savings went, a concurrent rise in military spending suggests that Uganda exploited its development aid to reallocate funds from health care to the military. If so, it is no surprise that this aid did little to improve the lives of Uganda’s people.

The Uganda example suggests that governments may, more generally, divert aid funds from developmental uses to military spending. This would be disturbing in at least two ways. First, military spending does not promote development: studies show that its impact on growth is nonexistent at best and negative at worst (Dunne and Uye 2009). Second, military resources are often used to repress domestic dissent. For example, in the “Arab Spring” of 2011, governments across the Middle East and North Africa used their armed forces to intimidate pro-democracy protesters. If development aid is generally diverted to military spending, it could thus have pernicious economic and political effects.

Whether development aid generally boosts military spending is unclear. Although Feyzioglu, Swaroop, and Zhu (1998) conclude that aid is fungible, they find no evidence that it spills over into the defense budget. Cashel-Cordo and Craig (1990) reach the same conclusion. However, both Collier and Hoeffler (2007) and Khilji and Zampelli (1994) find that development aid boosts military spending. The evidence on this question is thus inconclusive. This is unfortunate, as aid donors, and the development community more generally, have a strong interest in knowing whether aid has been grossly misused. We seek a more definitive answer to this question.

We argue that these inconclusive results reflect the fact that some governments are more likely than others to divert development aid to military spending. Because foreign aid increases government revenue, it also boosts societal demands for a revenue share. Different governments respond to these demands in different ways. Autocratic governments maintain power by channeling resources to a small group of supporters while repressing popular demands. Because repression requires costly coercive forces, this strategy requires autocrats to spend foreign aid on the military. In contrast, democratic governments stay in power by accommodating popular demands. This requires them to spend aid, not on the military, but on programs that benefit mass publics. Both types of government use aid to maintain power, but their different institutional constraints lead them to do this in different ways. Autocrats divert development aid to the military, while democrats do not.

Our argument builds on models developed by Bueno de Mesquita and Smith (2009) and Smith (2008). These models examine the impact of “free resources”—that is, nontax revenue sources such as minerals and foreign aid—on government policy. Their outcome of interest is the provision of “core” public goods such as freedom of speech and assembly. These models predict that free resources lead to increased distributional pressures, to which the government responds by either expanding or contracting core public goods. Which action the government takes depends on the size of its “winning coalition.” In small-coalition or autocratic systems, the government reduces core public goods, thus hindering mobilization by political opponents. In large-coalition or democratic systems, the government expands core public goods, thus accommodating public demands.

Our contribution is to consider these models’ implications for military spending. It is standard to assume that public goods cost money, so that their cost increases with their supply (Bueno de Mesquita et al. 2003). However, core public goods are unusual in that their restriction is actually costlier than their provision. To restrict freedom of speech and assembly, the government needs coercive forces that are costly to maintain. Hence, counterintuitively, a reduction in core public goods necessitates an increase in military spending.

This point has important implications for the debate between “aid pessimists” and “aid optimists.”⁴ Aid pessimists believe that foreign aid is useless at best and pernicious at worst: it not only fails to promote growth but also leads to rent-seeking and corruption, moral hazard, and reduced demand for democratic accountability (Djankov, Montalvo, and Reynal-Querol 2008; Hodler 2007; Morrison 2009; Moyo 2009; Svensson 2000). If these charges are true, then countries that continue to give aid are simply throwing good money after bad. On the other hand, optimists observe that aid seems to work under certain conditions. Specifically, a growing number of studies show that foreign aid promotes growth and development in democracies but not in autocracies (Dollar and Burnside 2004; Dollar and Levin 2005; Isham, Kaufmann, and Pritchett 1997; Kosack 2003; Svensson 1999). Our results are consistent with this claim and provide a possible explanation: autocrats divert aid to economically unproductive military expenditures while democrats do not. Our results thus add to the mounting evidence that aid donors—at least ones that care about development—should target aid to democracies.

Foreign Aid and Military Spending

At the United Nations Summit in 2000, world leaders pledged to help poor countries achieve a better life by 2015.⁵ Foreign aid was touted as an important means to this end. Since then, donor countries have increased official development assistance (ODA): that is, aid explicitly designated for development goals such as health care, poverty reduction, and infrastructure. From 2000 to 2009, total ODA exceeded $1 trillion, growing at an annual rate of 7 percent in real terms.⁶ Moreover, many in the development community call for even more, despite the economic travails of many donor countries. At the recent G20 Summit in France, Bill Gates argued that “the world will not balance its books by cutting back on aid, but it will do irreparable damage to global stability, to the growth of the global economy and to livelihoods of millions of poor people.”⁷ Perhaps not surprisingly, the rising prominence of ODA, along with the fiscal woes of aid donors, have prompted many to ask whether such aid actually works.

The modal answer is no. A growing number of studies concur that on average, foreign aid has failed to promote growth (Easterly 2001; Moyo 2009; Rajan and Subramanian 2008). Why this is so is not clear: perhaps the aid has simply been wasted, or perhaps it has contributed to problems such as rent-seeking, corruption, moral hazard, and reduced demand for democratic accountability (Djankov, Montalvo, and Reynal-Querol 2008; Hodler 2007; Morrison 2009; Moyo 2009; Svensson 2000). Whatever the reason, the apparent ineffectiveness of foreign aid has led many policy makers and scholars to question the value of aid programs. Research on aid effectiveness thus has potentially far-reaching policy implications.

Although scholars concur that aid has been ineffective on average, some contend that it is nonetheless effective under certain conditions. For example, Burnside and Dollar (2000) argue that aid is effective at promoting growth when given to recipients with “good policies,” while Bearce and Tirone (2010) conclude that aid is effective when given for developmental rather than strategic reasons. Perhaps the most prominent “conditional aid effectiveness” argument is that aid promotes growth in democracies but not in autocracies (Dollar and Burnside 2004; Dollar and Levin 2005; Isham, Kaufmann, and Pritchett 1997; Kosack 2003; Svensson 1999). Explanations for this phenomenon vary: perhaps it reflects lower corruption in democracies (Dollar and Burnside 2004), civic participation that improves the performance of aid projects (Isham, Kaufmann, and Pritchett 1997), the provision of public goods that increase productivity (Bueno de Mesquita and Smith 2009; Smith 2008), or something else. Whatever the reason, these results are important because they suggest both that aid can be effective and that it should be targeted selectively to countries that are likely to use it as intended.

Our argument complements previous ones by suggesting another way in which regime type mediates the effects of aid. We build on models by Bueno de Mesquita and Smith (2009) and Smith (2008) that examine the policy consequences of “free resources” such as natural resources and foreign aid. Because we build on these models, we briefly review their main features before discussing our extensions.

These models extend the “selectorate model” developed by Bueno de Mesquita et al. (2003). In this model, policies are made by an incumbent leader who needs the support of a winning coalition (W) to stay in power. W can be large or small and is a function of regime type: democracies have large winning coalitions, while autocracies have small ones. The leader maintains power by offering coalition members private goods—which are consumed only by coalition members—and public goods, which are consumed by all citizens. In equilibrium, the politically optimal mix of private and public goods depends on the size of W. Leaders provide fewer private goods and more public goods as W grows.

Bueno de Mesquita and Smith (2009) and Smith (2008) extend this model in several ways. First, in the basic model, the leader’s survival depends solely on keeping coalition members happy: she cannot be threatened by citizens outside W. In Bueno de Mesquita and Smith (2009) and Smith (2008), the leader also faces a “revolutionary activist” who seeks to expand W to include half the population. The leader can thus be deposed, not only by members of W, but also by the currently disenfranchised masses.

Second, in Bueno de Mesquita and Smith (2009) and Smith (2008), core public goods affect the public’s ability to mobilize against the regime. Freedom of speech and assembly make it easier for the masses to organize and revolt. The supply of these goods thus affects the leader’s survival prospects not only via coalition welfare but also by affecting the likelihood of a successful revolt.

Third, in the basic model, government revenues stem solely from taxation. In Bueno de Mesquita and Smith (2009) and Smith (2008), the government also has access to “free resources” that do not require higher taxes. Such resources include natural resources (e.g., oil) and foreign aid. The model’s main contribution is to assess the impact of free resources on the provision of core public goods.

How leaders use free resources depends on the size of W: small-W leaders spend them on private goods, while large-W leaders spend them on public goods. Because free resources benefit the public only under large-W regimes, an increase in free resources increases the public’s incentive to seek a large-W system and the associated free-resource benefits. This incentive is strongest when W is small because a shift to a large W then represents a bigger change from the status quo and has a larger impact on citizen welfare. Free resources thus increase the public’s incentive to revolt against small-W regimes.

The leader can counter this revolutionary threat in two ways. First, she can provide more public goods under the current regime so that citizens have less incentive to seek revolutionary change. Second, she can restrict core public goods so that revolutionary activity becomes more difficult. Which strategy the leader adopts depends on the size of W. Large-W leaders cannot restrict public goods without alienating coalition members, whose welfare depends on such goods. Large-W leaders thus offset revolutionary threats by providing more public goods. In contrast, small-W leaders can easily compensate coalition members for any decline in public goods by providing more private goods. Moreover, coalition members prefer this outcome to a revolution that undermines their privileged position. Small-W leaders thus minimize revolutionary threats by contracting core public goods. Bueno de Mesquita and Smith (2009) provide empirical support for this hypothesis.

In both their theory and empirical analysis, Bueno de Mesquita and Smith (2009) and Smith (2008) focus on core public goods (i.e., civil liberties) but do not examine spending outcomes. This makes sense, as core public goods generally do not cost money: unlike, say, education or infrastructure, they are not financed from the government budget. In fact, providing core public goods is usually just a matter of getting the government out of the way. Conversely, restricting freedom of speech and assembly requires the active involvement of military or police forces. Because such forces are costly to maintain, a contraction of core public goods actually requires higher spending on repression. Given this, these models have important but previously unexplored fiscal implications.

If a free resource like ODA leads small-W leaders to repress civil liberties, it should also cause them to spend more on the military forces needed to accomplish this. ODA should thus lead to higher military spending in small-W systems. Conversely, ODA should have no such effect in large-W systems, where leaders should expand rather than contract public goods. We thus hypothesize that ODA leads to higher military spending in small-W systems but not in large-W systems. Because coalition size and regime type are closely related, both conceptually and empirically, we also frame our hypothesis in terms of regime type: ODA leads to higher military spending in autocracies but not in democracies.⁸

This hypothesis rests on two assumptions that warrant further discussion. First, we assume that military spending is meant to enhance domestic repressive capacity. This is debatable, as military spending also serves national security ends. This assumption is important, however, as our hypotheses depend crucially on how the military is used. If the main goal of military spending is national security—a public good—then democracies, not autocracies, should spend ODA on the military. Different assumptions about the purpose of military spending thus lead to different hypotheses about its conditional relationship with ODA.

We acknowledge that military spending serves various ends, some public-spirited and others less so. Whether it is largely repressive in nature is thus an empirical question, and we offer an empirical response. First, in our empirical analysis, we control for security-related determinants of military spending: involvement in wars, military spending in neighboring countries, alliance ties, and so on. These controls should help account for spending on national security, with the unexplained remainder more likely to be used for domestic repression. Second, previous studies (e.g., Fordham and Walker 2005) have found that democracies spend less on the military than autocracies. Within the selectorate framework, this is consistent with the claim that the military provides repression rather than the public good of national security. Finally, we replicate this finding with our own data; hence this claim seems appropriate for our sample.⁹ These points suggest that with appropriate controls, it is reasonable to treat military spending as an instrument of repression. Of course, if this assumption is wrong, we should obtain the opposite of the hypothesized results.

Second, although we hypothesize that aid generally increases military spending in autocracies, the models of Bueno de Mesquita and Smith (2009) and Smith (2008) imply this relationship only in the presence of a revolutionary threat. Without such a threat, autocrats have no need to restrict core public goods, and hence no need for increased spending on repression. The general nature of our hypothesis thus reflects an implicit assumption that autocrats always face revolutionary threats. Although we relax this assumption in our empirical analysis—examining the conditional effects of ODA in “low threat” and “high threat” subsamples—we believe that our baseline assumption of ubiquitous threat is useful for several reasons.

One reason is pragmatic: it is difficult to measure revolutionary threat, defined as pressure for regime change that must be accommodated or deterred. Bueno de Mesquita and Smith (2009) use the change in various measures of unrest as a proxy for the degree of threat. However, as these authors acknowledge, this captures only overt protest and misses cases where citizens would like regime change but have been successfully deterred. These cases are important, however: as recent events in the Middle East illustrate, the quiet that precedes a revolution may conceal latent revolutionary threats.¹⁰ Because we do not wish to exclude such cases, we assume that some threat always exists. To the extent that this assumption is wrong, this should weaken our results.

Perhaps more importantly, there are good theoretical and empirical reasons to believe that autocracies generally do face latent revolutionary threats. Theoretically, as Smith (2008, 788) notes, the public’s desire for regime change should increase with “the difference between their welfare under the current institutions relative to the welfare they expect under postrevolutionary institutions.” Because most citizens are better off under democracy than under autocracy, the masses should be most supportive of revolutionary change when the regime is undemocratic. Empirically, Bueno de Mesquita and Smith (2010) show that mass unrest tends to unseat autocratic leaders but not democratic ones. Their explanation (2010, 943) is that democratic citizens “have little incentive to rebel since they already enjoy the large coalition institutions which they might hope to create via revolution. . . . In contrast . . . citizens in small coalition systems have incentives to rebel.” Intuitively, it seems reasonable to assume that most people living under autocracy would prefer democracy.

This does not mean that these people will always take revolutionary action. The incentive to take such action depends not only on the benefits from regime change but also on the likelihood of revolutionary success and the costs of failure. Although the benefits of regime change are high under autocracy, would-be revolutionaries face low chances of success and high costs for failure. Autocrats can reduce the chances of success by contracting core public goods—thus making revolutionary activity more difficult—and can increase the costs of failure by punishing rebels harshly. The first policy reduces the expected benefits of revolutionary action, while the second increases the expected costs; hence both reduce the incentive to rebel.

Although these “autocratic deterrents” seem to contradict our assumption that revolutionary threats are ever-present, they are in fact consistent with our argument. Both deterrents—restricting civil liberties and punishing dissenters—require investment in repressive capacity. When the public’s potential gain from regime change rises—as it does when autocracies gain free resources—autocrats need to spend even more on repressive capacity to keep the incentive to revolt low. The autocrat’s efforts to deter revolution are thus central to our argument that ODA leads to increased military spending.¹¹

Finally, we note that building a repressive apparatus takes time. An autocrat that waited until revolution was imminent before undertaking this task would probably not survive long. Forward-looking autocrats should thus invest in repression preemptively, behaving “as if” they faced ongoing revolutionary threats. This implies spending ODA on the military.

Analysis

We test our hypothesis on aid and military spending using all countries and years for which data are available: 109 countries from 1961 to 2004. Our dependent variable, ΔMilitary Expenditure/GNI_i,t, is the annual change in country i’s military spending as a percentage of gross national income (GNI) from year t − 1 to t. We divide military spending by GNI to permit meaningful comparisons across countries and over time, and log the measure before differencing because the untransformed variable is heavily right-skewed.¹²

Our key independent variable, Aid/GNI, is country i’s net inflows of ODA as a percentage of gross national income. Aid, like military expenditure, is logged to reduce right skew. Because both aid and military spending are logged, the aid coefficients can be interpreted as elasticities. As we discuss below, we estimate an error-correction model and thus include first differences and lags of aid and all other independent variables.¹³

Because we expect aid’s impact on military spending to depend on recipient regime type, we interact aid with Democracy. Because there is some debate about how best to measure regime type, we use three measures. The first (W) is Bueno de Mesquita and Smith’s (2010) measure of winning coalition size. This measure ranges from 0 to 1 in intervals of .25, with higher values indicating larger coalitions. The second (Polity) is the 21-point Polity index, which ranges from −10 for full autocracies to +10 for full democracies. The third (UDS) is the Unified Democracy Score developed by Pemstein, Meserve, and Melton (2010), which synthesizes 10 different measures of democracy. The UDS ranges continuously from −2 to 2, with higher values indicating greater democracy. To facilitate interpretation of our results, we recode the Polity and UDS measures to range from 0 to 1.¹⁴

To estimate the impact of aid at different degrees of democracy, we include Aid/GNI*Democracy, the product of aid and regime type. If our hypothesis is correct, the coefficient on Aid/GNI should be positive, indicating that aid increases military spending in autocracies. The coefficient on the interaction term should be negative, indicating that this effect is smaller in more democratic recipients.¹⁵

As noted above, it is crucial to control for security threats, both because such threats are important drivers of military spending and because we wish to measure the impact of aid on military spending that is not motivated by legitimate security concerns. Because security threats are most pronounced during periods of active warfare, we include Interstate Conflict and Domestic Conflict to control for participation in both types of conflict. Both variables are ordinal and are coded 0 for no armed conflict, 1 for minor armed conflict, 2 for intermediate conflict, and 3 for outright war.¹⁶ We expect both variables to be positively signed.

Security threats arise not only from active warfare but also from an increase in the military strength of potential enemies. If the latter increase their military capabilities, governments may feel the need to respond in kind. Following Collier and Hoeffler (2007), we include Neighbor Military Expenditure/GNI, the log of neighbor military expenditures as a percentage of neighbor GNI. States are considered neighbors if they are separated by a land border or no more than 24 miles of water. We focus on neighbor military expenditures because most developing countries are threatened primarily by their neighbors and because geographic proximity is exogenous to home-country military spending (Collier and Hoeffler 2007).¹⁷

Governments counter security threats not only through military spending but also by forming defensive alliances. For example, many countries are explicitly protected by U.S. security guarantees, which may reduce their need to build up their own militaries. We thus include US Defense Pact, a dummy coded 1 if a country has a defense pact with the United States and 0 otherwise.¹⁸ Defense pacts obligate signatories to provide active military support to each other in the event of a military attack. If countries protected by defense pacts with the United States spend less on their militaries, this variable will be negatively signed.

Besides security concerns, economic development may influence military spending. Some scholars argue that wealthy states have more resources to protect and greater means to provide protection (Sandler and Hartley 1995), which implies that they should spend more on the military. However, because security is a necessity, poor states may devote a disproportionately large share of their resources to the military (Collier and Hoeffler 2007), which implies the opposite relationship between development and military spending. Although there is no conventional wisdom on the effects of development, its potential importance leads us to include the log of Real GDP Per Capita.¹⁹

Finally, we include country fixed effects to control for unobservable country-specific influences. We employ robust standard errors clustered by country to correct for serial correlation and other forms of panel heteroskedasticity. We estimate an error-correction model of the following form:

\begin{matrix} Δ Military Expenditures / {GNI}_{i, t} = β_{0} + β_{1} Military Expenditures / {GNI}_{i, t - 1} \\ + γ Δ X_{i, t} + λ X_{i, t - 1} + ε_{i, t}, \end{matrix}

where Military Expenditures/GNI_i,t−1 is the one-year lag of military spending, ΔX_i,t is a vector of annual changes in all right-hand-side variables, X_i,t−1 is a vector of one-year lags in all right-hand-side variables, and γ and λ are vectors of coefficients for the first-differenced and lagged variables, respectively.²⁰

We use an error-correction model because it imposes fewer assumptions than other time-series estimators regarding the timing of the independent variables’ effects (De Boef and Keele 2008). A government that receives sector-specific aid might transfer resources from the targeted sector into other sectors, but it might not do so immediately. Error-correction models are useful because they allow us to estimate both the immediate and the lagged effects of right-hand-side variables. The immediate effects are given by γ, the coefficients on the first-differenced variables. The lagged effects are given by λ, the coefficients on the lagged variables. The total effects—that is, the sum of all immediate and lagged effects—are given by the long-run multipliers (LRMs), which are calculated by dividing each independent variable’s coefficient by the coefficient on the lagged dependent variable. To obtain correct standard errors for the LRMs, we employ the Bewley (1979) transformation suggested by De Boef and Keele (2008).

Results of our baseline analysis are presented in Table 1. Columns 1 and 2, 3 and 4, and 5 and 6 show results for the W, Polity, and UDS democracy measures, respectively. Columns 1, 3, and 5 show the immediate and lagged effects of all variables, while columns 2, 4, and 6 report the corresponding LRMs. Because we are interested in the total effects of aid, our discussion focuses on the LRMs, although not surprisingly, these parallel the immediate and lagged effects.

Table 1.

Development Aid, Regime Type, and Military Spending.

	Democracy Measure
	W		Polity		UDS
Explanatory Variable	(1) Coefficient	(2) LRM	(3) Coefficient	(4) LRM	(5) Coefficient	(6) LRM
First differences
ΔAid/GNI	.119**		.074*		.179**
ΔAid/GNI	(.043)		(.038)		(.061)
ΔAid/GNI *Democracy	−.152**		−.058		−.269**
ΔAid/GNI *Democracy	(.072)		(.063)		(.136)
ΔDemocracy	.227*		.004		.303
ΔDemocracy	(.136)		(.121)		(.255)
ΔDomestic Conflict	.043**		.042**		.043**
ΔDomestic Conflict	(.013)		(.014)		(.013)
ΔInterstate Conflict	.034**		.022		.029**
ΔInterstate Conflict	(.014)		(.014)		(.014)
ΔNeighbors’ Mil.Exp./GNI	.102**		.106**		.103**
ΔNeighbors’ Mil.Exp./GNI	(.024)		(.023)		(.023)
ΔUS Defense Pact	.031		.063		.033
ΔUS Defense Pact	(.026)		(.049)		(.050)
ΔGDP per capita	−.495**		−.488**		−.454**
ΔGDP per capita	(.102)		(.100)		(.092)
One-year lags
Aid/GNI	.056**	.216**	.054**	.202**	.084**	.317**
Aid/GNI	(.024)	(.088)	(.019)	(.068)	(.029)	(.107)
Aid/GNI *Democracy	−.057	−.220	−.039	−.149	−.097*	−.367*
Aid/GNI *Democracy	(.036)	(.141)	(.010)	(.107)	(.057)	(.218)
Democracy	.030	.116	−.017	−.064	−.003	−.011
Democracy	(.080)	(.307)	(.060)	(.226)	(.116)	(.436)
Domestic Conflict	.039**	.149**	.037**	.142**	.036**	.135**
Domestic Conflict	(.009)	(.033)	(.010)	(.038)	(.010)	(.036)
Interstate Conflict	.031**	.118**	.018	.068	.027*	.102*
Interstate Conflict	(.013)	(.054)	(.012)	(.047)	(.013)	(.052)
Neighbors’ Mil.Exp./GNI	.025**	.096**	.027**	.101**	.024**	.090**
Neighbors’ Mil.Exp./GNI	(.008)	(.032)	(.008)	(.030)	(.008)	(.029)
US Defense Pact	.000	.003	−.010	−.040	−.004	−.016
US Defense Pact	(.045)	(.171)	(.034)	(.129)	(.036)	(.138)
GDP per capita	.005	.020	.007	.028	.013	.049
GDP per capita	(.028)	(.109)	(.028)	(.108)	(.028)	(.107)
Mil. Exp./GNI	−.262**	−2.80**	−.266**	−2.74**	−.266**	−2.75**
Mil. Exp./GNI	(.022)	(.328)	(.022)	(.320)	(.022)	(.314)
Observations	3154		3260		3382
F (p > F)	16.97 (.000)		16.46 (.000)		18.46 (.000)

Note: Dependent variable: ΔMilitary Expenditure/GNI_i,t. Robust clustered standard errors are in parentheses. LRM = long-run multipliers; UDS = Unified Democracy Score; GNI = gross national income; GDP = gross domestic product; Mil. Exp. = military expenditure.

p < .10, **p < .05.

According to our hypothesis, the aid variable should be positively signed, while the interaction term should be negatively signed. The aid LRMs are consistently positive and significant, indicating that ODA significantly increases military spending in the most autocratic countries. The interaction term LRMs are negative, as expected, but significant only in the UDS model. What ultimately matters, however, are the marginal effects of aid at different degrees of democracy (Brambor, Clark, and Golder 2006; Kam and Franzese 2007). These effects—specifically, conditional long-run multipliers—are presented in Figure 1.

Figure 1.

Conditional effects of development aid on military spending.

Figure 1 plots the aid LRMs, on the y axis, against the degree of democracy, on the x axis. The solid lines represent LRM point estimates, while the dashed lines depict 90 percent confidence intervals. Figures 1(a), 1(b), and 1(c) present results based on W, Polity, and UDS, respectively. All three measures yield similar results. When democracy equals zero, aid significantly increases military spending. Specifically, a 1 percent increase in aid/GNI increases military spending/GNI by 0.22, 0.20, and 0.31 percent, respectively, when W, Polity, and UDS equal zero. The effects of aid continue to be positive and significant until W exceeds .25 and Polity and UDS reach .5. Put differently, the significant positive effects pertain to 31, 55, and 44 percent of the sample for W, Polity, and UDS, respectively. Beyond these thresholds, the effects of aid become insignificant and approach zero in full democracies. The LRM results thus support our hypothesis: ODA increases military spending in autocracies but not in democracies.

We have thus far treated aid as exogenous. However, it could arguably be endogenous to military spending. For example, if donors engaged in “balancing” behavior, they might give more aid—even development aid, which they know to be fungible—to militarily weaker states. This would create a negative (or weaken a positive) relationship between aid and military spending. Conversely, if donors “bandwagoned” and used aid to strengthen the already strong, this would have the opposite effect. It seems doubtful that such dynamics can explain our conditional results, as this would require aid donors to balance among democracies but to bandwagon among autocracies, and we know of no reason why this would occur. Nonetheless, the possibility that aid could be endogenous requires us to address this concern.

To address this concern, we use two-stage least squares (2SLS) regression. For reasons discussed above, we treat four variables as endogenous: the first-differenced and lagged aid variables and their interactions with democracy. To perform 2SLS, we thus require at least four exogenous instruments that affect our dependent variable only through the endogenous variables. We would prefer to have even more exogenous instruments, as this permits the diagnostic tests discussed below. We obtain these instruments from two sources.

First, we employ measures of foreign policy similarity between the recipient countries, on the one hand, and the United States, Britain and France, on the other. We focus on these three countries because recipients aligned with these great powers tend to receive more aid (Alesina and Dollar 2000; Thacker 1999). These instruments should be exogenous because, theoretically, they should not affect recipient military spending directly. They may affect spending indirectly, if increased aid provides resources that can be spent on the military, but this indirect (via aid) channel is precisely what makes these variables good instruments. We obtain our measure of foreign policy similarity—Signorino and Ritter’s (1999) S—from EUGene (Bennett and Stam 2000). Second, to obtain additional instruments, we employ the Lewbel (1997) solution of including higher-order moments of each endogenous regressor. As Lewbel (1997) demonstrates, these higher-order moments are, by construction, correlated with the endogenous regressors but uncorrelated with the error term of the second-stage regression.²¹ We include one additional moment for each endogenous regressor, giving us a total of seven instruments.

To perform 2SLS, we first regress the four endogenous regressors against the seven exogenous instruments and all other independent variables. We then employ the first-stage results to generate predicted values of the endogenous regressors. Finally, we include these predicted values on the right-hand side of the second-stage regression, in which military spending is the dependent variable. Because the predicted values of the endogenous regressors should, by construction, be uncorrelated with the second-stage error term, the second-stage results should not be biased by endogeneity. Second-stage results are shown in Table 2.²²

Table 2.

Two-Stage Least Squares Regression Results.

	Democracy Measure
	W		Polity		UDS
Explanatory Variable	(1) Coefficient	(2) LRM	(3) Coefficient	(4) LRM	(5) Coefficient	(6) LRM
First differences
ΔAid/GNI	.278**		.111		.297
ΔAid/GNI	(.069)		(.085)		(.141)
ΔAid/GNI *Democracy	−.474**		−.167		−.592
ΔAid/GNI *Democracy	(.111)		(.123)		(.308)
ΔDemocracy	.893**		.212		.941
ΔDemocracy	(.230)		(.246)		(.589)
ΔDomestic Conflict	.039**		.038**		.038
ΔDomestic Conflict	(.014)		(.015)		(.014)
ΔInterstate Conflict	.034**		.021		.027
ΔInterstate Conflict	(.014)		(.014)		(.014)
ΔNeighbors’ Mil. Exp./GNI	.081**		.088**		.083
ΔNeighbors’ Mil. Exp./GNI	(.020)		(.019)		(.020)
Δ US Defense Pact	.003		.059		−.000
Δ US Defense Pact	(.036)		(.086)		(.083)
ΔGDP per capita	−.405**		−.433**		−.391
ΔGDP per capita	(.119)		(.114)		(.108)
One-year lags
Aid/GNI	.126**	.454**	.092**	.320**	.135**	.449**
Aid/GNI	(.037)	(.139)	(.035)	(.127)	(.059)	(.217)
Aid/GNI *Democracy	−.201**	−.744**	−.106**	−.379*	−.220*	−.717
Aid/GNI *Democracy	(.070)	(.273)	(.053)	(.212)	(.119)	(.453)
Democracy	.335**	1.20**	.126	.413	.288	.806
Democracy	(.155)	(.608)	(.116)	(.456)	(.253)	(.956)
Domestic Conflict	.034**	.136**	.034**	.129**	.031**	.122**
Domestic Conflict	(.009)	(.038)	(.011)	(.043)	(.010)	(.041)
Interstate Conflict	.025**	.112**	.014	.071	.021*	.099**
Interstate Conflict	(.012)	(.050)	(.011)	(.044)	(.013)	(.050)
Neighbors’ Mil. Exp./GNI	.022**	.080**	.027**	.096**	.022**	.081**
Neighbors’ Mil. Exp./GNI	(.008)	(.031)	(.007)	(.029)	(.007)	(.029)
US Defense Pact	.009	.098	−.019	−.004	−.009	.027
US Defense Pact	(.055)	(.210)	(.043)	(.156)	(.044)	(.162)
GDP per capita	.020	.065	.035	.115	.033	.116
GDP per capita	(.029)	(.114)	(.029)	(.112)	(.029)	(.113)
Mil. Exp./GNI	−.256**	−2.87**	−.264**	−2.78**	−.259**	−2.85**
Mil. Exp./GNI	(.021)	(.327)	(.021)	(.308)	(.021)	(.331)
Observations	2840		2939		3037
F (p > F)	14.33 (.000)		15.08 (.000)		13.35 (.000)
Underidentification Test (H₀: Instruments are uncorrelated with endogenous regressors)
χ² (p value)	16.98 (.000)		10.84 (.008)		21.68 (.000)
Overidentification Test (H₀: Instruments are uncorrelated with the error term)
χ² (p value)	4.28 (.232)		4.62 (.201)		4.04 (.256)
Exogeneity Test (H₀: Regressors are exogenous)
χ² (p value)	5.81 (.213)		3.06 (.546)		2.16 (.706)

p < .10, **p < .05.

Before discussing the regression results, we examine some tests of instrument validity. One criterion for instrument validity is relevance: the instruments must be correlated with the endogenous regressors. To verify this, we performed a test of underidentification in which the null hypothesis is that the instruments are uncorrelated with endogenous regressors. As shown at the bottom of Table 2, the χ² statistics associated with the underidentification test are highly significant. We thus reject the null hypothesis and conclude that our instruments are relevant. A second criterion for instrument validity is exogeneity: the instruments must not be correlated with the error term of the second-stage regression. To verify this, we performed a test of overidentifying restrictions in which the null hypothesis is that the instruments are uncorrelated with the error term. As shown at the bottom of Table 2, the null hypothesis cannot be rejected (p = .232, .201, and .256). Our instruments thus appear to be both relevant and exogenous.

Having established that our instruments are valid, we also investigate whether the potentially endogenous regressors are in fact endogenous. Specifically, we test the null hypothesis that the endogenous regressors are actually exogenous. As shown at the bottom of Table 2, the null hypothesis cannot be rejected (p = .213, .546, and .706). Aid and its interaction with democracy thus appear to be exogenous. Although this implies that our previous results are valid, we present the 2SLS results for robustness.

The 2SLS results are similar to our previous ones. Again, we focus on the LRMs. The aid/GNI LRMs remain significant and positive but are larger than before: now, a 1 percent increase in aid/GNI increases military spending/GNI by 0.45, 0.32, and 0.45 percent, respectively, when W, Polity, and UDS equal zero. The interaction term LRMs remain negative but are larger than before and are now significant in two models. As before, we calculate conditional aid LRMs and present them graphically in Figure 2. This figure tells much the same story as Figure 1: ODA significantly increases military spending in autocracies, but this effect becomes insignificant once each democracy measure reaches a threshold of about .5. The 2SLS regressions thus reinforce our main result.

Figure 2.

Two-stage least squares (2SLS) regression results.

For reasons discussed earlier, we have thus far assumed that autocrats always face revolutionary threats. We have consequently examined the effects of aid conditional on regime type, but we have not further conditioned these results on any measure of revolutionary threat. We now relax this assumption. Although we believe, as stated earlier, that revolutionary threat is often latent and thus hard to measure, it seems likely that Bueno de Mesquita and Smith’s (2009, 2010) measure captures differences in the degree of threat faced by rulers. This measure is based on the change in mass political movements—demonstrations, riots, strikes, and revolutions—over the previous three years. In brief, the authors standardize the four protest measures, take their average, and examine changes rather than levels to account for the fact that “normal” protest levels differ across countries.²³ Following Bueno de Mesquita and Smith (2010), we code country-years as “low-threat” if the threat measure is decreasing or stable (threat ≤ 0) and as “high-threat” if the threat measure is increasing (threat > 0). We then repeat our analysis on both low-threat and high-threat samples. If leaders in fact face stronger revolutionary threats in the high-threat than in the low-threat sample, then the effects of aid on military spending should be stronger in the former.²⁴ Results are shown in Table 3. The top half of the table presents results for the high-threat subsample (Revolutionary Threat > 0), while the bottom half presents results for the low-threat subsample (Revolutionary Threat ≤ 0). For ease of presentation, we present only the LRMs and their standard errors.

Table 3.

Effects of Aid in High- and Low-Threat Subsamples.

	Democracy Measure
Explanatory Variable	W	Polity	UDS
High-Threat (Revolutionary Threat > 0)
Aid/GNI	.980 (.381)**	1.31 (.349)**	1.46 (.524)**
Aid/GNI *Democracy	−.436 (.693)	−1.11 (.621)*	−1.78 (1.03)*
Democracy	.164 (1.39)	1.64 (1.15)	2.25 (1.97)
Domestic Conflict	.089 (.042)**	.096 (.054)*	.093 (.050)*
Interstate Conflict	.206 (.088)**	.106 (.086)	.080 (.087)
Neighbors’ Mil. Exp./GNI	.039 (.069)	−.006 (.088)	−.020 (.077)
GDP per capita	.289 (.175)*	.086 (.189)	.128 (.188)
Mil. Exp./GNI	−3.13 (.640)**	−3.48 (.603)**	−3.69 (.675)**
Observations	666	715	728
Low-Threat (Revolutionary Threat ≤ 0)
Aid/GNI	.530 (.135)**	.246 (.175)	.395 (.300)
Aid/GNI *Democracy	−.960 (.235)**	−.377 (.252)	−.721 (.565)
Democracy	1.77 (.520)**	.431 (.538)	.892 (1.17)
Domestic Conflict	.146 (.046)**	.131 (.056)**	.118 (.054)**
Interstate Conflict	.064 (.056)	.023 (.049)	.077 (.059)
Neighbors’ Mil. Exp./GNI	.122 (.035)**	.133 (.033)**	.127 (.033)**
GDP per capita	.052 (.125)	.117 (.129)	.122 (.131)
Mil. Exp./GNI	−2.69 (.359)**	−2.62 (.349)**	−2.72 (.363)**
Observations	1933	1977	2034

Note: Dependent variable: ΔMilitary Expenditure/GNI_i,t. Robust clustered standard errors are in parentheses. UDS = Unified Democracy Score; GNI = gross national income; Mil. Exp. = military expenditure.

p < .10, **p < .05.

Note first that the results are qualitatively similar in both subsamples: the aid/GNI coefficients are consistently positive, while the interaction terms are consistently negative. Moreover, these relationships are significant even in the low-threat subsample, albeit only for the model that uses W. Given this, we cannot reject the possibility that leaders face revolutionary threats in both subsamples. That said, the results are clearly stronger in the high-threat subsample. The aid/GNI coefficients are much larger and significant in all three models, implying that autocratic leaders are more likely to divert ODA to military spending. An analysis of marginal effects reinforces this conclusion, as shown in Figure 3.

Figure 3.

Effects of aid in high-threat and low-threat subsamples.

The top half of Figure 3 (a, b, and c) shows results for the high-threat subsample, while the bottom half (d, e, and f) shows results for the low-threat subsample. The high-threat results are very similar to previous ones—aid significantly increases military spending in autocracies but not in democracies—but the aid coefficients are larger, consistent with the idea that leaders in this subsample face greater revolutionary threats. The low-threat results are qualitatively similar, but the aid coefficients are smaller and significant only in the W analysis. This is consistent with the idea that leaders in this subsample face weaker revolutionary threats. Although the significant results in the low-threat subsample suggest that revolutionary threat is measured with some error—or, alternatively, that such threats are indeed ubiquitous—the split-sample results nonetheless tend to strengthen our theoretical argument. They are stronger in the high-threat subsample—where, theoretically, they should be—suggesting that autocratic leaders in fact spend ODA on the military in an effort to counter revolutionary threats.

Conclusion

A growing body of research shows that development aid has failed to promote development, at least under autocratic regimes. Although explanations for this failure vary, a common theme is that recipients have not used aid for its intended purpose. We provide concrete evidence of such misuse, showing that autocratic recipients have systematically diverted development aid toward military spending. This is undesirable on both economic and political grounds. Military spending does not promote economic development (Dunne and Uye 2009); hence aid diverted to the military is, from a developmental standpoint, wasted. Moreover, in many autocratic countries, the military is used to repress domestic dissent. Such repression is undesirable in its own right and may also have economic feedback effects: as Isham, Kaufmann, and Pritchett (1997) demonstrate, aid-funded projects perform better when civil liberties are strong. Our results thus shed light on why development aid does not promote development in autocracies.

Our results say less about what is going on in democracies. Bueno de Mesquita and Smith (2009) and Smith (2008) predict that democracies will spend aid on public goods. If so, this could explain why aid seems to promote development in democratic recipients (Dollar and Burnside 2004; Dollar and Levin 2005; Isham, Kaufmann, and Pritchett 1997; Kosack 2003; Svensson 1999). It would be useful, in future research, to investigate this hypothesis further. However, this could be difficult for at least two reasons.

One problem is assessing which categories of spending are public and which are private. Although the distinction is sometimes clear-cut—for example, industry subsidies are typically private goods—many goods that appear to be public could actually be private, in the sense that they are both excludable and rival in consumption. For example, we typically think of education spending as public, but in many developing countries it is skewed toward tertiary education and a privileged upper class. Similarly, while roads and bridges are classic public goods, the associated construction contracts are all-too-typical examples of pork-barrel spending. As a consequence, it is difficult to say exactly where—that is, in what spending categories—we should find evidence that democracies spend foreign aid on public goods.

A second problem is that, even in the context of the selectorate model, democracies might not spend aid on public goods at all. Although Bueno de Mesquita and Smith (2009) and Smith (2008) treat the tax rate as exogenous, Bueno de Mesquita et al. (2003) endogenize the tax rate and find that large-W systems have lower taxes than small-W systems. This implies that democratic leaders might use foreign aid, not to increase any kind of spending, but to reduce the tax burden. Indeed, Cashel-Cordo and Craig (1990) point to such tax reductions as yet another type of aid fungibility. In sum, democracies could spend development aid in a variety of ways that are difficult to specify empirically, or they might not spend the money at all. For these reasons, we focus on repressive spending, for which the model’s implications are clear.

Despite these caveats, our results do tell us something important about democratic as well as autocratic recipients: the former do not divert ODA to military spending. We can thus rule out this important type of aid misuse. Along with the evidence that ODA promotes growth in democracies, our results strengthen the claim that democracies put ODA to better use. For donors concerned with development, this has obvious policy implications.

Footnotes

Acknowledgements

We thank Bruce Bueno de Mesquita and three anonymous Political Research Quarterly reviewers for helpful comments on earlier drafts. All errors are, of course, our own.

Declaration of Conflicting Interests

The author(s) declared no potential conflicts of interest with respect to the research, authorship, and/or publication of this article.

Funding

The author(s) received no financial support for the research, authorship, and/or publication of this article.

Notes

References

Alesina

Alberto

Dollar

David

. 2000. “Who Gives Foreign Aid to Whom and Why?” Journal of Economic Growth 5 (1): 33–63.

Anderson

T. W.

Hsiao

Cheng

. 1982. “Formulation and Estimation of Dynamic Models Using Panel Data.” Journal of Econometrics 18 (1): 47–82.

Arellano

Manuel

Bond

Stephen

. 1991. “Some Tests of Specification for Panel Data: Monte Carlo Evidence and an Application to Employment Equations.” Review of Economic Studies 58 (2): 277–97.

Bearce

David H.

Tirone

Daniel C.

2010. “Foreign Aid Effectiveness and the Strategic Goals of Donor Governments.” Journal of Politics 72 (3): 837–51.

Beck

Nathaniel

Katz

Jonathan N.

2004. “Time-Series—Cross-Section Issues: Dynamics.” Working Paper. The Society for Political Methodology. Washington University in St. Louis, St.Louis, MO.

Bennett

D. Scott

Stam

Allan

. 2000. “EUGene: A Conceptual Manual.” International Interactions 26 (2):179–204.

Bewley

Ronald A.

1979. “The Direct Estimation of the Equilibrium Response in a Linear Dynamic Model.” Economics Letters 3 (4): 357–61.

Bond

Stephen R.

“Linear Panel Data Models.” Lecture Notes, Royal Economic Society Easter School in Econometrics on Dynamic Panel Data (Manuel Arellano and Steve Bond), 20–24 March 2006, Nuffield College, University of Oxford.

Brambor

Thomas

Clark

William Roberts

Golder

Matt

. 2006. “Understanding Interaction Models: Improving Empirical Analyses.” Political Analysis 14 (1): 63–82.

10.

Bueno de Mesquita

Bruce

Smith

Alastair

. 2009. “Political Survival and Endogenous Institutional Change.” Comparative Political Studies 42 (2): 167–97.

11.

Bueno de Mesquita

Bruce

Smith

Alastair

. 2010. “Leader Survival, Revolutions and the Nature of Government Finance.” American Journal of Political Science 54 (4): 936–50.

12.

Bueno de Mesquita

Bruce

Smith

Alastair

Siverson

Randolph M.

Morrow

James D.

2003. The Logic of Political Survival. Cambridge, MA: MIT Press.

13.

Burnside

Craig

Dollar

David

. 2000. “Aid, Policies, and Growth.” American Economic Review 90 (4): 847–68.

14.

Cashel-Cordo

Peter

Craig

Steven G.

1990. “The Public Sector Impact of International Resource Transfers.” Journal of Development Economics 32 (1): 17–42.

15.

Chen

Shaohua

Ravallion

Martin

. 2004. “How Have the World’s Poorest Fared since the Early 1980s?” World Bank Research Observer 19 (2): 141–69.

16.

Collier

Paul

Hoeffler

Anke

. 2007. “Unintended Consequences: Does Aid Promote Arms Races?” Oxford Bulletin of Economics and Statistics 69 (1): 1–27.

17.

De Boef

Suzanna

Keele

Luke

. 2008. “Taking Time Seriously: Dynamic Regression Models.” American Journal of Political Science 52 (1): 184–200.

18.

Djankov

Simeon

Montalvo

Jose G.

Reynal-Querol

Marta

. 2008. “The Curse of Aid.” Journal of Economic Growth 13 (3): 169–94.

19.

Dollar

David

Burnside

Craig

. 2004. “Aid, Policies, and Growth: Revisiting the Evidence.” World Bank Policy Research Working Paper 3251.

20.

Dollar

David

Levin

Victoria

. 2005. “Sowing and Reaping: Institutional Quality and Project Outcomes in Developing Countries.” World Bank Policy Research Working Paper 3524.

21.

Doucouliagos

Hristos

Paldam

Martin

. 2009. “The Aid Effectiveness Literature: The Sad Results of 40 Years of Research.” Journal of Economic Surveys 23 (3): 433–61.

22.

Dugger

Celia W.

2011. “Maternal Deaths Focus Harsh Light on Uganda.” The New York Times, July 29.

23.

Dunne

J. Paul

Uye

Mehmet

. 2009. “Military Spending and Development.” In The Global Arms Trade: A Handbook, edited by Tan

Andrew T. H.

London: Routledge.

24.

Easterly

William

. 2001. “The Lost Decades: Developing Countries’ Stagnation in Spite of Policy Reform, 1980-1998.” Journal of Economic Growth 6 (2): 135–57.

25.

Easterly

William

. 2008. “Can the West Save Africa?” NBER Working Paper No. 14363.

26.

Feyzioglu

Tarhan

Swaroop

Vinaya

Zhu

Min

. 1998. “A Panel Data Analysis of the Fungibility of Foreign Aid.” World Bank Economic Review 12 (1): 29–58.

27.

Finkel

Steven E.

Pérez-Liñán

Anibal S.

Seligson

Mitchell A.

2007. “The Effects of U.S. Foreign Assistance on Democracy Building, 1990–2003.” World Politics 59 (3): 404–39.

28.

Fordham

Benjamin O.

Walker

Thomas

. 2005. “Kantian Liberalism, Regime Type, and Military Resource Allocation: Do Democracies Spend Less?” International Studies Quarterly 49 (1): 141–57.

29.

Gleditsch

Nils Petter

Wallensteen

Peter

Eriksson

Mikael

Sollenberg

Margareta

Strand

Havard

. 2002. “Armed Conflict 1946-2001: A New Dataset.” Journal of Peace Research 39 (5): 615–37.

30.

Hodler

Roland

. 2007. “Rent Seeking and Aid Effectiveness.” International Tax and Public Finance 14 (5): 525–41.

31.

IHME (Institute for Health Metrics and Evaluation). 2010. Financing Global Health 2010: Development Assistance and Country Spending in Economic Uncertainty. Seattle, WA: IHME.

32.

Isham

Jonathan

Kaufmann

Daniel

Pritchett

Lant H.

1997. “Civil Liberties, Democracy, and the Performance of Government Projects.” World Bank Economic Review 11 (2): 219–42.

33.

Iversen

Torben

Cusack

Thomas R.

2000. “The Causes of Welfare State Expansion: Deindustrialization or Globalization?” World Politics 52 (3): 313–49.

34.

Kam

Cindy D.

Franzese

Robert J.

2007. Modeling and Interpreting Interactive Hypotheses in Regression Analysis: A Brief Refresher and Some Practical Advice. Ann Arbor, MI: University of Michigan Press.

35.

Khilji

Nasir M.

Zampelli

Ernest M.

1994. “The Fungibility of U.S. Military and Nonmilitary Assistance and the Impacts on Expenditures of Major Aid Recipients.” Journal of Development Economics 43 (3): 345–62.

36.

Kosack

Stephen

. 2003. “Effective Aid: How Democracy Allows Development Aid to Improve the Quality of Life.” World Development 31 (1): 1–22.

37.

Leeds

Brett Ashley

Ritter

Jeffrey M.

Mitchell

Sara McLaughlin

Long

Andrew G.

2002. Alliance Treaty Obligations and Provisions, 1815-1944. International Interactions 28 (2): 237–60.

38.

Lewbel

Arthur

. 1997. “Constructing Instruments for Regressions with Measurement Error When No Additional Data Are Available, with an Application to Patents and R&D.” Econometrica 65 (5): 1201–13.

39.

Morrison

Kevin M.

2009. “Oil, Non-Tax Revenue, and the Redistributional Foundations of Regime Stability.” International Organization 63 (1): 107–38.

40.

Moyo

Dambisa

. 2009. Dead Aid: Why Aid Is Not Working and How There Is Another Way for Africa. New York: Farrar, Straus and Giroux.

41.

Nickell

Stephen

. 1981. “Biases in Dynamic Models with Fixed Effects.” Econometrica 49 (6): 1417–26.

42.

Pemstein

Daniel

Meserve

Stephen A.

Melton

James

. 2010. “Democratic Compromise: A Latent Variable Analysis of Ten Measures of Regime Type.” Political Analysis 18 (4): 426–49.

43.

Rajan

Raghuram G.

Subramanian

Arvind

. 2008. “Aid and Growth: What Does the Cross-Country Evidence Really Show?” Review of Economics and Statistics 90 (4): 643–65.

44.

Rudra

Nita

. 2005. “Globalization and the Strengthening of Democracy in the Developing World.” American Journal of Political Science 49 (4): 704–30.

45.

Sandler

Todd

Hartley

Keith

. 1995. The Economics of Defense. New York: Cambridge University Press.

46.

Signorino

Curtis S.

Ritter

Jeffrey M.

1999. “Tau-b or Not Tau-b: Measuring the Similarity of Foreign Policy Positions.” International Studies Quarterly 43 (1): 115–44.

47.

Smith

Alastair

. 2008. “The Perils of Unearned Income.” Journal of Politics 70 (3): 780–93.

48.

Sullivan

Patricia L.

Tessman

Brock F.

Xiaojun

. 2011. “US Military Aid and Recipient State Cooperation.” Foreign Policy Analysis 7 (3): 275–94.

49.

Svensson

Jakob

. 1999. “Aid, Growth, and Democracy.” Economics and Politics 11 (3): 275–97.

50.

Svensson

Jakob

. 2000. “Foreign Aid and Rent-Seeking.” Journal of International Economics 51 (2): 437–61.

51.

Thacker

Strom C.

1999. “The High Politics of IMF Lending.” World Politics 52 (1): 38–75.

52.

Wright

Joseph

Winters

Matthew

. 2010. “The Politics of Effective Foreign Aid.” Annual Review of Political Science 13:61–80.