WORKING PAPER NUMBER 32
J
U L Y
2004
The Anarchy of Numbers:
Aid, Development,
and Cross-country Empirics
by David Roodman
Abstract
Contemporary econometric literature has generated a large number of stories of the relationship between how
much foreign aid a countries receives and how it grows. All the stories hinge on the statistical significance in
cross-country regressions of a quadratic term involving aid. Among the stories are that aid raises growth (on average) 1) in countries where economic policies are good; 2) in countries where policies are good and a civil war recently ended; 3) in all countries, but with diminishing returns; 4) in countries outside the tropics; 5) in countries
with difficult economic environments, characterized by declining or volatile terms of trade, natural disasters, or
low population; or 6) when aid increases in countries experiencing negative export price shocks. The diversity of
results prima facie suggests that many are fragile. Easterly et al. (2004) find the aid-policy story (Burnside and
Dollar, 2000) to be fragile in the face of an expansion of the data set in years and countries. The present study expands that analysis by applying more tests, and to more studies. Each test involves altering just one aspect of the
regressions. All 19 tests are derived from sources of variation that are minimally arbitrary. Twelve derive from
specification differences between studies, what Leamer (1983) calls “whimsy.” Three derive from doubts about
the appropriateness of the definition of one variable in one study. The remaining four derive from the passage of
time, which allows sample expansion. This design allows an examination of the role of “whimsy” in the results
that are tested while minimizing “whimsy” in the testing itself. Among the stories examined, the aid-policy link
proves weakest, while the aid-tropics link is most robust.
The Anarchy of Numbers:
Aid, Development, and Cross-country Empirics
David Roodman1
Center for Global Development
This draft: July 2004
Abstract: Contemporary econometric literature has generated a large number of stories of the relationship between how much foreign aid a countries receives and how it grows. All the stories hinge on the
statistical significance in cross-country regressions of a quadratic term involving aid. Among the stories
are that aid raises growth (on average) 1) in countries where economic policies are good; 2) in countries
where policies are good and a civil war recently ended; 3) in all countries, but with diminishing returns;
4) in countries outside the tropics; 5) in countries with difficult economic environments, characterized by
declining or volatile terms of trade, natural disasters, or low population; or 6) when aid increases in countries experiencing negative export price shocks. The diversity of results prima facie suggests that many
are fragile. Easterly et al. (2004) find the aid-policy story (Burnside and Dollar, 2000) to be fragile in the
face of an expansion of the data set in years and countries. The present study expands that analysis by
applying more tests, and to more studies. Each test involves altering just one aspect of the regressions. All
19 tests are derived from sources of variation that are minimally arbitrary. Twelve derive from specification differences between studies, what Leamer (1983) calls “whimsy.” Three derive from doubts about the
appropriateness of the definition of one variable in one study. The remaining four derive from the passage
of time, which allows sample expansion. This design allows an examination of the role of “whimsy” in
the results that are tested while minimizing “whimsy” in the testing itself. Among the stories examined,
the aid-policy link proves weakest, while the aid-tropics link is most robust.
1
The author thanks William Easterly and Michael Clemens for advice, Craig Burnside, Lisa
Chauvet, Jan Dehn, and Henrik Hansen for data and assistance, and Stephen Knack, Patrick Guillaumont, and participants in an August 2003 seminar at the Center for Global Development for
valuable comments. Responsibility for the final product rests with the author. All judgments, opinions, and errors are those of the authors alone and do not represent the views of the Center for
Global Development, its staff, or board of directors.
Introduction
In the early weeks of 1981 economist Edward Leamer gave a speech at the University of
Toronto, in which he bemoaned the state of econometrics. Econometrics sought the status of a
science, with regressions its analog for the reproducible experiments of chemistry or physics. Yet
an essential part of econometric “experiments” was too often arbitrary, opaque, and unrepeatable. Adapting the speech for the American Economic Review, he wrote:
The econometric art as it is practiced at the computer terminal involves fitting many, perhaps
thousands, of statistical models. One or several that the researcher finds pleasing are selected for
reporting purposes. This search for a model is often well intentioned, but there can be no doubt
that such a specification search invalidates the traditional theories of inference. The concepts of
unbiasedness, consistency, efficiency, maximum-likelihood estimation, in fact, all the concepts of
traditional theory, utterly lose their meaning by the time an applied researcher pulls from the
bramble of computer output the one thorn of a model he likes best, the one he chooses to portray
as a rose.
…
This is a sad and decidedly unscientific state of affairs we find ourselves in. Hardly anyone takes
data analyses seriously. Or perhaps more accurately, hardly anyone takes anyone else’s data
analyses seriously. Like elaborately plumed birds who have long since lost the ability to procreate
but not the desire, we preen and strut and display our t-values. (Leamer, 1983)
The way out of the quagmire, Leamer argued, was for econometricians to explore large regions
of “specification space,” systematically analyzing the relationship between assumptions and conclusions:
[A]n inference is not believable if it is fragile, if it can be reversed by minor changes in assumptions. As consumers of research, we correctly reserve judgment on an inference until it stands up
to a study of fragility, usually by other researchers advocating opposite opinions. It is, however,
much more efficient for individual researchers to perform their own sensitivity analyses, and we
ought to be demanding much more complete and more honest reporting of the fragility of claimed
inferences….The job of a researcher is then to report economically and informatively the mapping from assumptions into inferences. (Leamer, 1983)
One econometric debate that has worrying hallmarks of Leamer’s syndrome is that on the
1
effectiveness of foreign aid to developing countries. Since Griffin and Enos (1970), econometricians have parried over the question of how aid affects economic growth in recipient nations.
Prominent in the contemporary work, Burnside and Dollar (2000) concluded, “aid has a positive
effect on growth in a good policy environment,” presumably because good policies increase the
productivity of aid-financed investment. Their evidence: the statistical significance in crosscountry panel growth regressions of an interaction term of total aid received and an indicator of
the quality of recipient economic policies.
The work of Burnside and Dollar has brought corroborations (Collier and Dehn, 2001;
Collier and Hoeffler 2002; Collier and Dollar, 2002, 2004) and challenges. From the ongoing
debate have emerged several stories of the relationship between aid and growth, each of which
turns on a particular quadratic or cubic term involving aid. The stories are not incompatible, but
most papers support only one, a few two. Hansen and Tarp (2001) find that entering the square
of aid drives out the significance of Burnside and Dollar’s aid×policy, and makes the simple aid
term significant too: aid works on average, but with diminishing returns. Guillaumont and Chauvet (2001) also fail to find significance for aid×policy, and instead offer evidence that aid works
best in countries with difficult economic environments, characterized by volatile and declining
terms of trade, low population, and natural disasters, perhaps because aid finances institutions
that help cushion the shocks. In the same vein, Collier and Dehn (2001) find that increasing aid
to countries experiencing negative export price shocks raises growth. Meanwhile, Collier and
Hoeffler (2002) offer a triple-interaction term: aid works particularly well in countries that are
recovering from civil war and that have good policies. Last, Hansen and Tarp, along with Dalgaard, tell a new story: aid raises growth outside the tropics but not in them, low latitudes apparently being associated with some combination of inhospitable natural environments and poor
2
policies and institutions (Dalgaard et al., 2004).
These papers naturally differ not only in their conclusions and policy implications but
also their specifications. Within the group, there are two different choices of period length in the
panel data sets, three definitions of “policy,” three of aid, and four choices of control variable set.
Though probably none of the choices are truly made on a whim, these differences appear to be
examples of what Leamer called “whimsy.” From Leamer’s point of view, the studies taken together represent a small and unsystematic sampling of specification space. Without further
analysis, it is impossible to know whether the results reveal solid underlying regularities in the
data or are fragile artifacts of “whimsy.”
In this paper, I therefore examine the possibility of fragility in this literature systematically. Since by the laws of chance any regression can be broken with enough experimentation, it
is essential for credibility that the testing suite itself be un-whimsical. I derive my tests therefore
from three canonical sources of variation: the “whimsy” already present in the original specifications; doubts about the appropriateness of the definition of one variable, the Collier and Dehn
negative shock variable; and the passage of time, which allows expansion of data sets. Each test
ideally involves varying just one aspect of the regressions, although sometimes additional
changes are made so that the modified regressions pass specification tests. In all, I subject 8 regressions from 7 of the most prominent studies to this systematic test suite.
The rest of this paper runs as follows. Section I places the recent empirical work on aid in
historical context and reviews the approaches and conclusions of the studies that are tested for
robustness. Section II describes the testing regime. Section III reports results. Section IV concludes.
I. History
It can be said that foreign aid for poor countries was born on the steps of the U.S. Capitol just
3
after noon on January 20, 1949. At that moment, the re-elected President Harry Truman gave his
inaugural address, in which he enunciated a historically novel vision of the relationship between
the democratic west and what is now called the “developing world.” The poorer nations were no
longer just colonies or sources of raw materials for the West to exploit, but potential allies in the
Cold War, which must be won over to capitalism and democracy. By sharing its capital and technical know-how, the United States could make poor nations richer and expand the sphere of freedom.
As Truman spoke, American assistance for the rapid, aid-financed redevelopment of
Western Europe was already underway, and would soon succeed unambiguously. But the effectiveness of aid for development in poorer countries has for decades been a point of intense controversy. Bauer (1976), Hancock (1989), Easterly (2001), and Reusse (2002), among others, have
pointed out how foreign assistance has been undermined by geopolitics, pressures from domestic
commercial interests for contracts, arrogance and perverse incentives within aid-giving institutions, and the sheer difficulty of fostering development from the outside. Against these criticisms, defenders have pointed to successes such as the eradication of smallpox, the widespread
vaccination of children against other diseases, and support for family planning that helped slow
population growth.
The hope has often arisen that a turn to the numbers would shed light on the contentious
questions of whether and when aid works. Starting in 1970, cross-country empirics were brought
to bear to examine how aid affects macro variables such as investment, growth, and poverty. In
the view of Hansen and Tarp (2000), this literature has gone through three generations. The first
generation essentially spanned 1970–72, and mainly investigated the aid-savings link. Influenced
by the Harrod-Domar model, in which savings is the binding constraint on growth, aid-induced
4
saving was assumed to lead directly to investment, thence to growth via a fixed incremental capital-output ratio. Not considered were the realistic possibilities that some aid is consumed and that
some invested aid has low, zero, even negative returns. The second generation of studies, which
ran from the early 1970s to the early 1990s, avoided the simplistic assumptions about savings by
directly investigating the relationship between aid on the one hand and investment and growth on
the other.
Hansen and Tarp argue that the preponderance of the evidence from these first two generations says that 1) aid increases total savings but less than one-to-one, partly substituting,
partly complementing other sources of savings; and 2) that aid increases investment and growth.
They suggest that studies with more pessimistic results, such as Mosley et al. (1987), have
gained disproportionate attention despite being in the minority precisely because they are contrarian.
The third generation commenced with Boone (1994) and continues to this day. It has
brought several innovations. The data sets cover more countries and years. Reflecting the influence of the new growth theory, regressors are typically included to represent the economic and
institutional environment (sometimes together called the “policy environment”). It has become
the norm to address methodologically the potential endogeneity of aid and policy to growth, usually with two-stage least squares. And, finally, the aid-growth relationship is allowed to be nonlinear, through incorporation of such regressors as aid2 and aid×policy. (Hansen and Tarp, 2000)
The data sets are almost always panels. The studies I test for robustness all belong to the third
generation.
Burnside and Dollar disseminated their first results on aid effectiveness in 1997, as a
World Bank working paper that eventually appeared in the American Economic Review (2000).
5
They test whether an interaction term of aid and an index of recipient economic policies is significantly associated with growth. Their data set is a panel drawn from developing countries outside the former Eastern bloc, covering the six four-year periods in 1970–93. They incorporate
some controls found significant in the general growth literature, namely: initial income (log real
GDP/capita) to capture convergence; ethno-linguistic fractionalization (Easterly and Levine,
1997), assassinations/capita, and the product thereof; the Knack-Keefer (1995) institutional quality variable, called “ICRGE”; M2/GDP, l to indicate financial depth, lagged one period to avoid
endogeneity (King and Levine, 1993); dummies for sub-Saharan Africa and fast-growing East
Asia; and period dummies.
Burnside and Dollar use a measure of aid called Effective Development Assistance
(EDA), as computed by Chang et al. (1998). EDA differs in two major respects from the usual
net Overseas Development Assistance measure (net ODA) tabulated by the Paris-based Development Assistance Committee (DAC). First, EDA excludes technical assistance, on the grounds
that it funds not so much recipient governments as consultants. Second, it differs in its treatment
of loans. Net ODA counts disbursements of concessional (low-interest) loans only, but at full
face value.1 It nets out principal but not interest payments on old loans because it is built on a
capital flow concept. In contrast, EDA includes all disbursements of all development loans regardless of how concessional they are (for example, near-commercial rate loans by the World
Bank to middle-income countries such as Brazil), but counts only their grant element, that is,
their net present value. To express EDA as a share of recipient GDP, Burnside and Dollar convert it to constant 1985 dollars using the IMF’s world Export Unit Value Index, then divide into
real GDP from Penn World Tables 5.5 (Summers and Heston, 1991).
1
DAC considers a loan concessional if it has a grant element of at least 25 percent of the loan value, using a 10 percent discount rate.
6
To represent recipient economic policies with a single variable, Burnside and Dollar first
run a growth regression without aid terms, but with all controls and three indicators of economic
policy—log (1+inflation), budget balance/GDP, and the Sachs-Warner (1995) variable measuring openness to trade. The coefficients of all three policy variables differ from 0 at the 0.05 level
in this regression, so Burnside and Dollar form a linear combination of the three using the coefficients as weights. This is their policy index.2
When Burnside and Dollar run their base specification—containing the controls, the policy index, aid, and aid×policy—on their full data set, the term of central interest, aid×policy,
does not in fact enter significantly, whether in OLS or in 2SLS with aid and aid×policy instrumented. However, they find that it becomes significant after either of two possible changes. Five
outlier observations can be excluded (Burnside and Dollar’s preferred specification). Or a cubic
term can be added—aid2×policy, in which case both aid×policy and aid2×policy appear significant, the first with positive sign, the second negative. Burnside and Dollar famously conclude
that aid raises growth in a good policy environment, but with diminishing returns.
Burnside and Dollar’s work triggered responses in the literature, some critical, some supportive. Hansen and Tarp (2001) make one prominent attack. They modify the Burnside and Dollar 2SLS regressions in several ways, most importantly by adding an aid2 term. Aid×policy is not
significant in their results, but aid and aid2 are, the first positive and the second negative. The
implication is that aid is effective on average, but with diminishing returns—regardless of recipients’ policies as far as the evidence goes. Hansen and Tarp then criticize both the Burnside and
Dollar regressions and their own 2SLS regressions for failing to handle several econometric
problems. There may be unobserved country-level effects that correlate with both policies and
growth. Failing to purge or control for all such effects could give spurious explanatory power to
2
They also add a constant term to the index, but this has no effect on the regression results of interest here.
7
policies and aid×policy. Also, variables other than aid and its interaction terms, such as fiscal
balance, could be endogenous and ought to be instrumented. Thus they deploy the ArellanoBond GMM estimator. This estimator runs in first differences, which purges country effects, and
it allows the instrumentation of many variables, using their own lags. In switching to this “difference GMM” estimator, Hansen and Tarp also modify the regressor list. They drop fiscal balance
as a policy variable. And they add ∆aid and ∆(aid2). Hansen and Tarp’s key results on aid and
aid2 hold. And ∆aid and ∆(aid2) are significant too, again the first with positive sign and the second negative.
Guillaumont and Chauvet (2001) tell a third story of aid effectiveness. They hypothesize
that the economic vulnerability of a country influences aid effectiveness. They call economic
vulnerability the “environment,” not to be confused with Burnside and Dollar’s “policy environment.” In this story, aid flows stabilize countries that are particularly buffeted by terms of
trade difficulties, other sorts of external shocks, or natural disasters. In the spirit of Burnside and
Dollar, Guillaumont and Chauvet build an environment index out of four variables: volatility of
agricultural value added (to proxy for natural disasters), volatility of export earnings, long-term
terms of trade trend, and log of population (small countries being more vulnerable to external
forces). Their specification is unique in this literature in using 12-year periods, and in its set of
controls, which are partly inspired by Barro (1991) and Mankiw et al. (1992). They control for
population growth, mean years of secondary school education among adults, a Barro-Lee measures of political instability based on assassinations and revolutions, ethno-linguistic fractionalization, and lagged M2/GDP. In their OLS and 2SLS regressions, aid×environment appears with the
predicted negative sign, indicating that aid works better in countries with worse environments.
The term also drives out the significance of aid×policy.
8
Other papers have reached conclusions similar to those of Burnside and Dollar. Collier
and Dollar (2002) corroborate them with a quite different data set and specification. They use
OLS only. They include former Eastern bloc countries, the Bahamas, and Singapore. They use
net ODA rather than EDA. They study 1974–97 instead of 1970–93. They drop all Burnside and
Dollar controls except log initial GDP/capita, ICRGE, and period dummies. They add region
dummies.3 And they define policy as the overall score from the World Bank’s Country Policy
and Institutional Assessment (CPIA), which is a composite rating of countries on 20 aspects of
policies and institutions.4
In a paper that takes the Collier and Dollar core regression as its starting point, Collier
and Hoeffler (2002) analyze how aid effectiveness is influenced by whether a country has recently ended a civil war. Sticking to the four-year panel arrangement, they create three dummies
to indicate how recently civil war ended. The dummy for “peace-onset” is 1 in the period when a
country goes from civil war to peace. “Post-conflict 1” takes a value of 1 in the following period,
and “post-conflict 2” in the period after that—assuming civil war does not recur. In Collier and
Hoeffler’s preferred (OLS) specification, aid×policy×post-conflict 1 is significantly different
from 0: aid works particularly well in a good policy environment a few years after conflict has
ended.
Also corroborating Burnside and Dollar, Collier and Dehn (2001) hew more closely to
the Burnside and Dollar specification and data set, and tell a story that synthesizes elements from
Burnside and Dollar and Guillaumont and Chauvet. They find that adding variables incorporating information on export shocks renders Burnside and Dollar’s preferred specification—the one
3
The regions are Europe and Central Asia, Middle East and North Africa, Southern Asia, East Asia and Pacific,
Sub-Saharan Africa, and Latin America and the Caribbean, as defined by the World Bank.
4
Collier and Hoeffler (2002) make a small correction to the Collier and Dollar data set, excluding 5 observations
where a missing value had been treated as 0. I test the Collier and Hoeffler version of the Collier and Dollar regres-
9
with aid×policy but not aid2×policy—more robust to the inclusion of Burnside and Dollar’s five
outliers. First, they add two variables indicating the magnitude of any positive or negative commodity export price shocks. Aid×policy is then significant at 0.01 for a regression on the full
sample. The negative-shock variable is too, with the expected minus sign. Then Collier and Dehn
add four aid-shock interaction terms: lagged aid×positive shock, lagged aid×negative shock,
∆aid×positive shock, and ∆aid×negative shock. The first and last prove positive and significant
in OLS, and the last, ∆aid×negative shock proves particularly robust in their testing. But including the four raised the significance level of aid×policy to 0.08.5 Still, the study provides some
buttressing for Burnside and Dollar, and suggests that well-timed aid increases ameliorate negative export shocks. This matches the Guillaumont and Chauvet result in spirit. But where Guillaumont and Chauvet interact the amount of aid with the standard deviation of an index of export
volume and other variables, Collier and Dehn’s significant interaction term involves the change
in aid and the change in export prices.
Most recently in the peer-reviewed literature, Dalgaard et al. (2004) tell a novel aidgrowth story. They focus on the share of a country’s area that is in the tropics as a determinant of
both growth and the influence of aid on growth. This variable is indisputably free of the endogeneity worries that beset other variables advocated as determinants of aid effectiveness, such as
inflation and export volume volatility. It surfaces as a growth determinant in the work of Jeffrey
Sachs and others (Bloom and Sachs, 1998; Gallup and Sachs, 1999; Sachs, 2001, 2003). And the
causal links between tropical location and growth may include institutions and economic policies
(Acemoglu et al., 2001; Easterly and Levine, 2003). Dalgaard et al. thus see tropical area as an
sion.
5
I am able to reproduce exactly the results of the specification with the four interaction terms, in which aid×policy is
marginally significant. That is the one tested below. But I am not able to reproduce their results for the variant including only positive- and negative-shock terms. In my results, aid×policy has a t statistic of only 0.42. Yet the R2
10
exogenous “deep determinant” of growth. In OLS, 2SLS, Arellano-Bond “difference GMM,”
and Blundell-Bond “system GMM” regressions6, aid and aid×tropical area fraction are quite significant, the first with positive sign, the second with negative sign and similar magnitude. For
countries in the tropics, the derivative of growth with respect to aid (the sum of the coefficients
on aid and aid×tropical area fraction) is statistically indistinguishable from 0. Thus, on average,
aid seems to work outside the tropics but not in them. The authors report that their new interaction term drives out both aid×policy and aid2.
There are other third-generation studies. Hadjimichael et al. (1995), Durbarry et al.
(1998), and Lensink and White (2001), all find evidence for Hansen and Tarp’s story of aid effectiveness. Svensson (1999) finds a positive interaction between aid and recipients’ level of democracy. Chauvet and Guillaumont (2002) enrich their earlier analysis, in draft form. In a working paper, Burnside and Dollar (2004) defend their earlier analysis with a radically different
specification, a cross-section of countries rich and poor in the 1990s with minimal controls and a
different definition of policy.
In the present paper I focus on the studies already highlighted as being among the most
influential and, with two exceptions, having been published in the peer-reviewed literature. The
two exceptions are Collier and Dehn (2001) and Collier and Hoeffler (2002), which are pillars of
the peer-reviewed Collier and Dollar (2004). From 6 of these 7 studies, I test the single regression that appears to be the authors’ preferred one. From Hansen and Tarp (2001), I take two regressions. One, an Arellano-Bond GMM regression, seems to be their preferred regression. I in-
and sample size match theirs exactly.
6
Blundell-Bond “system GMM” augments Arellano-Bond “difference GMM” by creating a system of equations,
half in first differences, half in levels. In the difference equations, predetermined and endogenous variables are instrumented with lags of their own levels while in the levels equations they are instrumented with lags of their first
differences. See Blundell and Bond (1998).
11
clude one of their 2SLS regressions too because it is most akin to the core specification in an important new study by Clemens et al. (2004).
II. The Test Suite
A. The Tests
There is some robustness testing in the recent literature on aid-growth connections, albeit focusing almost exclusively on Burnside and Dollar (2000). Lu and Ram (2001) introduce fixed effects into the Burnside and Dollar regressions. Ram (2004) splits the aid variable into the components coming from bilateral and multilateral donors, and also tests alternative definitions of
policy. Dalgaard and Hansen (2001) modify the choice of excluded outliers. Easterly et al.
(2004) extend the data set to additional countries and an additional period, 1994–97. All these
tests eliminate the key Burnside and Dollar (2000) result.
The present study expands Easterly et al. work along two dimensions. It applies more
tests. And it tests more studies. Table 1 details the regressions chosen for testing from the publications highlighted above. The regressions vary in type of estimator, control set, countries sampled, length of periods within the panel, overall study timeframe, definitions of aid and policy,
and treatment of outliers. They do appear to contain “whimsy.”
12
Table 1. Regressions tested
Regression
Estima- Former East
tor
bloc?
Burnside &
Dollar
5/OLS
OLS
No
Collier &
Dehn 3.4
““
““
Collier &
Dollar 1.21
OLS
Yes
Collier &
Hoeffler
3.4
OLS
““
Hansen &
Tarp 1.2
2SLS
No
Hansen &
Tarp 3.2
Difference
GMM
““
Dalgaard, System
GMM
et al.
Yes
Definition of
Study Years/
Outliers Key significant
Aid
Policy
Controls
period period
out?
term(s)
LGDP, ETHNF,
ASSAS,
BB,
EDA/real
ETHNF×ASSAS, 1970– 4
Yes
INFL,
aid×policy
GDP
ICRGE, M2, SSA, 93
SACW
EASIA, period
dummies
aid×policy,
1974–
““
““
““
““
No
∆aid×negative
93
shock
LGDP, ICRGE,
1974–
ODA/real
aid×policy,
““
CPIA
““
policy, period and
97
GDP
aid2
region dummies
““
““
LGDP, ETHNF,
ASSAS,
ETHNF×ASSAS,
““
ICRGE, M2, SSA,
EASIA, period
dummies
LGDP, ASSAS,
ETHNF×ASSAS, 1978–
93
ICRGE, M2, period dummies
LGDP, policy, pe- 1970–
riod dummies
97
““
““
““
aid×policy×
post-conflict 1
ODA/
BB,
exchange INFL,
rate GDP SACW
““
aid, aid2
““
““
““
““
INFL,
SACW
““
aid, aid2, ∆aid,
∆aid2
““
EDA/real
GDP2
BB,
INFL,
SACW
““
aid,
aid×tropical
area fraction
GuillauLGDP, ENV, SYR,
aid,
ODA/
mont &
POPG, M2, PIN- 1970–
2SLS
No
12 exchange
““
““
aid
×
environChauvet
STAB, ETHNF,
93
rate GDP
ment
2.4
period dummy
1
As revised in Collier & Hoeffler 1.1. 2As extrapolated to 1970–74 and 1996–97 in Easterly et al. (2004).
Abbreviations: LGDP=log initial real GDP/capita; ETHNF=ethno-linguistic fractionalization, 1960; ASSAS=assassinations/capita; ICRGE=composite of International Country Risk Guide governance indicators; M2=M2/GDP, lagged; SSA=Sub-Saharan Africa dummy; EASIA=fast-growing East Asia dummy;
ENV=Guillaumont & Chauvet “environment” variable; SYR=mean years of secondary schooling among
adults; PINSTAB=average of ASSAS and revolutions/year; BB=budget balance/GDP;
INFL=log(1+inflation); SACW=Sachs-Warner openness; EDA=Effective Development Assistance;
ODA=Net Overseas Development Assistance.
The tests applied to these regressions constitute a systematic sampling of a larger region
of specification space than has hitherto been examined in the aid-growth literature. To limit
complexity and avoid whimsy, each test ideally involves changing just one aspect of the estima-
13
tions at a time. The tests are summarized in Table 2. The first four groups of tests, relating to the
controls, the definition of aid and policy, and period length, transfer one specification’s “whimsical” choices to the others. Next are the tests relating to the definition of export shock, which are
motivated not by differences among studies but concern about the appropriateness of the original
authors’ definition. Last are tests that modify the sample by dropping outliers (copying Burnside
and Dollar’s “whimsical” choice) and/or expanding to new countries and periods.
Following are more detailed descriptions of the tests:
1. Changing the control set. In his discourse on whimsy, the specification choice that Leamer
worries most about is the choice of regressors. The first set of tests is in this spirit. The studies examined use a variety of control sets, by which I mean regressors other than aid, the
variables it is interacted with, and the interaction terms themselves. Burnside and Dollar,
Collier and Dehn, and Hansen and Tarp control for initial log real GDP/capita; ethnolinguistic fractionalization, assassinations/capita, and the product thereof; the ICRGE governance variable; M2/GDP, lagged; being in sub-Saharan Africa or fast-growing East Asia;
and fixed period effects. Dalgaard et al. control for about half of those—log real GDP/capita,
ICRGE, and sub-Saharan Africa, East Asia, and period dummies.7 Guillaumont and Chauvet
control for a different but equally rich set of variables, namely initial log real GDP/capita,
mean years of secondary schooling, population growth, ethno-linguistic fractionalization, the
Barro-Lee political instability variable, and period effects. Collier and Dollar opt for a simpler set: initial log real GDP/capita, ICRGE, period effects, and—uniquely—region effects.
These four sets of choices give rise to four robustness tests. Each test substitutes a given
7
Dalgaard et al. actually use the listed control set for their OLS and 2SLS regressions. For their system GMM regression, they use only log real GDP/capita and period dummies. But the fuller set is more appropriate for testing the
regressions from other papers because all but one is OLS or 2SLS, and that one—the Hansen and Tarp GMM regression—is a pure first difference regression in which the additional controls all drop out because they are constant
14
control set for the original one and examines the effect on the significance of key terms.
One important comment is in order, which applies to other robustness tests as well. I always use all complete observations available for developing countries (including the countries of Eastern Europe). Because different variables are available for different subsets of
countries, changing the regressor set changes the regression sample. One could perform variants of the tests that are restricted to the intersections of the old and new samples in an attempt to distinguish the effects of changing sample and changing variables. But this would
add to the complexity, and the approach I take aims to answer the hypothetical, “What would
the results have been if the original authors had used alternative controls?” The authors almost certainly would have used all available observations.
over time. The slimmer control set causes widespread autocorrelation.
15
Table 2. Robustness Tests
Test
Changing aid definition
EDA/real GDP
ODA/real GDP
ODA/exchange rate GDP
Changing policy definition
INFL, BB, SACW
INFL, SACW
CPIA
Changing controls
BD controls
CD controls
GC controls
DHT controls
Changing period length
12-year
Description
Effective Development Assistance/real GDP, as in Burnside & Dollar,
Collier & Dehn, Dalgaard et al.
Net Overseas Development Assistance/real GDP, as in Collier & Dollar,
Collier & Hoeffler
Net Overseas Development Assistance/exchange rate GDP, as in
Hansen & Tarp, Guillaumont & Chauvet
Inflation, budget balance, and Sachs-Warner openness, as in Burnside &
Dollar, Collier & Dehn, Hansen & Tarp 2SLS
Inflation and Sachs-Warner, as in Hansen & Tarp GMM
Country Policy and Institutional Assessment, as in Collier & Dollar, Collier
& Hoeffler
Control for LGDP, ETHNF, ASSAS, ETHNF×ASSAS, ICRGE, M2, SSA,
EASIA, period effects, as in Burnside & Dollar, Collier & Dehn, Hansen
& Tarp
Control for LGDP, ICRGE, period and region effects, as in Collier &
Dollar, Collier & Hoeffler
Control for LGDP, ENV, SYR, POPG, M2, PINSTAB, ETHNF, period effects, as in Guillaumont & Chauvet
Control for LGDP, ICRGE, SSA, EASIA, period effects, as in Dalgaard et
al.
Aggregate over 12-year periods, as in Guillaumont & Chauvet
Changing shock definition
Pooled distribution
Use one threshold for all countries, rather than country-specific thresholds, that the unpredicted component of commodity export price index
change must exceed to be a shock
Shock/GDP
Express shock magnitude as share of GDP rather than price change
Shock/GDP, pooled distribu- Combine above two changes
tion
Changing sample and data set
No outliers
Remove Hadi outliers in the partial scatter of the dependent variable and
the independent variable of greatest interest
Expanded sample
New data set. Carried to 2001, except shocks data end in 1997 and Guillaumont & Chauvet environment variable not updated
Expanded sample, no outCombine above two changes
liers
Expanded sample, ARUse new data; use 5-year periods to eliminate higher-order autocorrelarobust
tion; instrument almost all variables with one-period lags; cluster
standard errors by country
Expanded sample, ARSame as previous but removing Hadi outliers
robust, no outliers
Abbreviations as in Table 1.
16
2. Redefining aid. All the studies take total aid received as a share of recipient GDP. But there
are differences in defining both the numerator and denominator of the ratio. Burnside and
Dollar, Collier and Dehn, and Dalgaard et al. use Effective Development Assistance in the
numerator while the rest use net ODA. On the choice of denominator, there is also a split.
Hansen and Tarp and Guillaumont and Chauvet use GDP converted to dollars using market
exchange rates. The others use real GDP from the Penn World Tables. A country’s relative
price level strongly correlates with income per head, with the poorest countries having a
price levels 20–25% that of the United States. Thus, using purchasing power parities instead
of exchange rates will cause the GDPs of the poorest countries to be measured as relatively
larger and aid to them as relatively smaller as a share of GDP. It is hard to know a priori what
effect this change could have on regression coefficients for aid and its interactions, but it
could be significant.
The use of exchange rates seems more appropriate. One way to see this is to ask what the
local-currency cost is to the recipient of not receiving a quantum of aid. If the aid would be
spent entirely on tradables, which cost about the same everywhere, then the cost to Sri Lanka
of not receiving $1 million in aid is the exchange-rate equivalent in rupees. The opposite extreme would occur if the aid would be spent on the representative consumption basket for the
country, including tradables and nontradables, with all goods and services purchased at donor-economy prices. In this case, the recipient government could purchase the same goods
and services for far less, so that the value of aid would be greatly inflated going by exchange
rates, and the PPP adjustment would be appropriate. This case, however, seems quite
unlikely. By definition, donors must purchase nontradables locally. They may pay abovemarket, but probably do not pay close to the donor-economy prices that can be 400% higher
17
or more.8 In fact, studies of the “tying” of aid—which is when donors require that it be spent
into the their own economy, on their own tractors or consultants—put the cost increase at
only 15–30%, not 400% or more (Jepma, 1991). This argues for exchange rates.
At any rate, with two options each for measuring aid and GDP, there are four possible
combinations for aid/GDP. The literature includes three of them (all but EDA/exchange rate
GDP), and these are the bases for three tests.9 In fact, EDA/real GDP and ODA/real GDP are
highly correlated (Dalgaard and Hansen, 2001), so switching from one to the other may not
stress results much. Switching between real and nominal GDP can be expected to impose a
more difficult test, because the correlations are lower. (See Table 3.)
Table 3. Simple correlations of aid measures, four-year periods, all available observations
EDA/real GDP
ODA/real GDP
ODA/exchange rate GDP
EDA/real GDP
1.00
0.97
0.78
ODA/real GDP
ODA/ exchange rate GDP
1.00
0.82
1.00
3. Redefining good policy. Three sets of “good policy” variables appear among the tested regressions: 1) Burnside and Dollar’s famous combination of budget balance, inflation, and
Sachs-Warner openness; 2) inflation and Sachs-Warner only (Hansen and Tarp GMM); and
3) CPIA alone (Collier and Dollar, Collier and Hoeffler). These generate three robustness
tests. Using Burnside and Dollar’s coefficients to form policy indexes (6.85 for budget balance, –1.40 for inflation, and 2.16 for Sachs-Warner), I find that the first two policy definitions are highly correlated, but the third varies more distinctly. (See Table 4.) Switching between the first two definitions is probably a mild test, but switching between them and CPIA
a more severe one. To apply the tests, in each case I rerun the Burnside-Dollar–style index8
If the overall price level in a donor country is five times that of the recipient, but the price level for tradeables is
about the same in both countries, then the ratio for nontradables must be well above five.
9
The published EDA data (Chang et al., 1998) cover only 1975–95. I extrapolate EDA to the rest of 1970–2001 via
18
forming regression, which includes all regressors except aid and its interaction terms, then
use the coefficients on the policy variables to make the index.10 I include all candidate policy
variables in the index regardless of their significance in this regression.
Table 4. Simple correlations of “good policy” measures
Inflation, budget balance, Sachs-Warner
Inflation, budget balance,
Sachs-Warner
Inflation, Sachs-Warner
CPIA
Inflation, Sachs-Warner
CPIA
1.00
0.52
1.00
1.00
0.98
0.53
4. Changing periodization. All but one of the studies use four-year periods, the exception being
Guillaumont and Chauvet’s, which uses 12 years. Since I lack higher-frequency observations
of the Guillaumont and Chauvet environment variable, I cannot test their regression on a 4year-period panel. But I test all the other regressions on 12-year panels. Notably, key studies
in the broader growth literature use periods of 10–25 years despite the small samples that result11 (Barro, 1991; Mankiw et al., 1992; Sachs and Warner, 1995).
a regression of EDA on net ODA, which is available for the whole period.
10
I compute the constant term in the policy index in the same manner as BD. It is the predicted growth rate in the
model when the policy variables and the period dummies are zero, and all other variables take their sample-average
values.
11
The question of whether the effects measured in four-year regressions are “short-term” is not straightforward to
answer. On the one hand, very little of the aid in a given P-year period is disbursed right at the start of the period
and very little of the growth record occurs right at the end. In other words, assuming that aid disbursements are
spread evenly over time within the period, the average positive lag between two point in time within the period—the
first when aid is disbursed the second when a quantum of growth experience occurs—works out to be:
PP
∫ ∫ (s − t )dsdt
0 t
P P
∫ ∫ dsdt
=
P
.
3
0 t
For P=4 years, this is 16 months. On the other hand, aid is significantly autocorrelated. I find that the three aid variables used in this literature have a serial correlation of 0.80–0.85 with 4-year periods. Thus, information about current-period aid flows conveys a good deal about previous-period aid. Among the tested regressions, only the Hansen
and Tarp GMM regression controls for previous-period aid, so the coefficients in all the other regressions actually
19
5. Changing the definition of shock. This test applies to the Collier and Dehn regression only.
Their positive and negative shock variables are built from a data set of commodity prices for
113 developing countries (Dehn, 2000). The definition has two parts: a rule for determining
whether a change in a country’s aggregate commodity export price index is large and unexpected enough to constitute a shock, and a formula for measuring the size of the shock. To
determine which price movements are shocks, Collier and Dehn examine the residuals from a
regression based on the following forecasting model:
∆yit = α 0 + α1t + β1∆yi ,t −1 + β 2 yi ,t −2 + ε it
where yit is the commodity export price index for country i in time t and εit is the forecasting
error. The regression is run separately for each country over 1957–97, and those forecasting
errors at least 1.96 standard deviations from the mean are considered shocks. The magnitude
of a shock is then the full price change ∆yit.
Two aspects of this definition deserve comment. First, the threshold that the unpredicted
component of a price movement must exceed to be a “shock” varies by country. This arguably makes sense in that an “unexpected” 20% price change might be routine in one country
and once-a-century in another. Countries that experience large price changes more frequently
may adapt to them, so that the effects on growth and poverty would be systematically different. On the other hand, this leads to the odd result that countries that are in fact more shockprone (in lay terms) do not necessarily experience more “shocks.” To take two extreme ex-
reflect effects of past aid too. One can estimate the true average aid-growth lag in these regressions as a weighted
average involving not just P/3 but terms such as P, 2P, 3P…, with weights ρ, ρ2, ρ3…, where ρ is the autocorrelation coefficient. It can be shown that the average lag is then:
P
+ Pρ + 2 Pρ 2 + 3Pρ 3 + ...
P 1+ ρ + ρ 2
3
.
=
3 1− ρ
1 + ρ + ρ 2 + ρ 3 + ...
For P=4 and ρ=0.81–0.85, this equals 17.3–22.9 years.
20
amples, in South Africa, where the standard deviation of the forecasting error was 4.8% during 1957–97, the 11.0% price index increase in 1988 (with a 13.2% forecasting error) is considered a positive shock. But in Laos, where the standard deviation of forecasting error was
24.9%, the 32.7% percent drop in 1987 (forecasting error of –48.1%) is not considered a
shock.
Second, the magnitude of the shocks as defined by Collier and Dehn does not take into
account the economic significance of commodities exports for a country. The growth impact
of a commodities price shock is probably related to both its magnitude and the share of commodity exports in GDP. But the Collier-Dehn definition is purely a measure of price change.
In contrast, Easterly and Rebello (1993), for example, gauge terms-of-trade shocks relative to
GDP.
I test the Collier and Dehn regressions with two changes that modify these aspects of the
shock definition—first separately, then together, for a total of three robustness checks. To
address the concern about the country dependence of shock definition, I pool the forecasting
errors for all 117 countries in the Dehn (2000) data set, and choose a single 1.96-standarderror shock threshold, which turns out to be a forecasting error of ±29.5%. To address the
concern about economic significance, I express the price changes as shares of GDP, using
1990 data on commodities exports, total exports, and total exports/GDP from Dehn (2000).12
6. Removing outliers. The Burnside and Dollar specification I test excludes five observations
that are a) outliers in aid×policy.and b) highly influential with respect to the coefficient on
that term. This raises a general question about the extent to which significant results in this
12
This implicitly assumes that the share of exports in GDP remained fixed at 1990 levels throughout the study period. This assumption is not completely realistic, but it allows use of Dehn’s data, with its broad coverage, and re-
21
literature are driven by outliers. To investigate the role of outliers, I rerun the reproductions
of the original regressions after excluding outliers. I do the same for the expanded-sample
versions of the regressions. (See below.) The process for picking outliers is different from
Burnside and Dollar’s, but less subjective. I apply the Hadi (1992) procedure for identifying
multiple outliers to the partial scatter of growth with a regressor of particular interest, such as
aid×policy, using 0.05 as the cut-off significance level.13 In instrumented regressions, I use
the variable of interest after projection onto the instruments.
I even run this test on the Burnside and Dollar 5/OLS regressions, from which one set of
outliers is already excluded. Fundamentally, regardless of the genesis of these regressions’
results, it is still interesting to determine whether they are driven by a few observations in the
remaining sample.
Outliers are not synonymous with influential observations. Why then focus on outliers?
For one, even outliers that do not have a high influence on coefficients of interest—what
standard tests for influence measure—can substantially affect the standard errors of the coefficients, which is at least as important for the present study. In addition, outliers are the observations most likely to signal measurement problems or structural breaks beyond which the
core model does not hold—both of which seem better reasons than high influence for exclusion. That said, outliers do not necessarily signal measurement problems or structural break.
This is especially possible when the variable of interest is highly non-normal, such as the
Collier and Dehn export price shock variable, which is usually 0 but occasionally takes large
values. In such cases, outliers may contain valuable information about the development process under rare combinations of circumstances. Still, on balance, regression results driven by a
duces any endogeneity of the modified shock variable to growth.
13
Applying the Hadi procedure directly to a full, many-dimensioned regression data set typically identified 20% or
22
few outliers need to be interpreted with care.
The method I use for identifying outliers does not extend straightforwardly to GMM because the two-dimensional partial scatterplot is a construct without a perfect analogue in the
GMM setting. Moreover, in system GMM, with parallel equations in levels and differences,
the notion of an observation itself becomes fuzzy. For these reasons, I do not attempt to identify and remove outliers from difference and system GMM regressions. Ideally, the combination of extensive instrumentation and GLS-style reweighting trims and deemphasizes outliers.
7. Expanding the sample. Easterly et al. (2004) develop a new dataset that extends that of Burnside and Dollar from 1970–93 to 1970–97 and adds six countries. For the present study, that
data set has been extended to 2001, pushed back to 1950, expanded to include variables in
other studies and the literature, and given better coverage of post-Communist Eastern
Europe. (See Appendix.) I use pre-1970 data only for lagged regressors and instruments, or
for computing first differences for 1970–73. This data set allows a net expansion in both
years and countries for all but Guillaumont and Chauvet regression, whose 12-year periods
and unusual environment variable make extension difficult. (See Table 5.) For example, in
the case of the Hansen and Tarp 2SLS regression, although 16 of the 231 observations complete in the original data set are incomplete in the new one, the new set has 194 novel observations, for a total of 409. More sample size information is in Table 14.
more of observations as outliers.
23
Table 5. Overview of differences in regression samples, original and expanded data sets
Regression
Burnside &
Dollar
Collier & Dehn
Collier & Dollar,
Collier &
Hoeffler
Hansen & Tarp
2SLS
Hansen & Tarp
GMM
Dalgaard et al.
Guillaumont &
Chauvet
Countries unique to the regression sample
Original set
Expanded set
Burkina Faso, Bulgaria, China, Cyprus,
Somalia,
Hungary, Iran, Jordan, Myanmar, Papua New
Tanzania
Guinea, Poland, Republic of Congo,
Romania, Singapore, South Africa, Uganda
““
““
Angola, Burkina Faso, Bulgaria, China, Cyprus,
Czech Republic, Guinea, Guinea-Bissau, Iran,
Jordan, Liberia, Mongolia, Mozambique,
None
Myanmar, Namibia, Oman, Papua New
Guinea, Poland, Republic of Congo,
Romania, Russia, Somalia, Suriname,
Uganda
Burkina Faso, Bulgaria, China, Côte d’Ivoire,
Guyana,
Cyprus, Hungary, Iran, Jordan, Mali,
Myanmar, Papua New Guinea, Poland,
Somalia,
Tanzania
Republic of Congo, Romania, Singapore,
South Africa, Uganda
Angola, Burundi, Benin, Burkina Faso,
Barbados, Bulgaria, Central African Republic,
Chad, China, Cyprus, Hungary, Iran, Jordan,
Somalia
Mauritania, Mauritius, Mozambique,
Myanmar, Nepal, Papua New Guinea,
Poland, Republic of Congo, Romania,
Rwanda, Singapore, South Africa, Uganda
Bangladesh, Czech Republic, Guinea-Bissau,
None
Russia, Singapore, South Africa
None
None
Study period
Original
Expanded
1970–93
1970–
2001
1974–93
1974–97
1974–97
1974–
2001
1974–93
1970–
2001
1978–93
““
1974–97
““
1970–93
1970–93
B. Testing the validity of the modified regressions
I apply up to three specification tests to the modified regressions. The first, which applies to all
the regressions, is for autocorrelation in the residuals. Autocorrelation can bias coefficients as
well as standard errors. In the OLS and 2SLS regressions I test, many of the regressors that are
treated as exogenous—inflation, governance quality, etc.—are potentially affected by past
growth (predetermined), which would render them endogenous in the presence of autocorrelation
and bias results. In the GMM regressions, few regressors are treated as exogenous; they are instrumented instead. But the instruments are lags of regressors in levels or first differences, which
can themselves be rendered invalid by autocorrelation of certain orders. To check for autocorrelation, I use the Arellano-Bond (1991) test for AR(), which is a flexible test designed for linear
24
GMM regression on panel data with arbitrary patterns of autocorrelation and heteroskedasticity.14 Since OLS and 2SLS with robust standard errors are special cases of linear GMM, the
Arellano-Bond test is appropriate for all the regressions I run. For the GMM regressions, I follow
the usual practice of applying the test to first difference residuals, which can detect autocorrelation in the error component that is purged of fixed country effects (Arellano and Bond, 1991). I
use a significance threshold of 0.05.
The second specification test, which applies to all the instrumented regressions, is the
Hansen J test of overidentifying restrictions—also using a significance level of 0.05. Failure on
this test indicates that an excluded instrument may in fact be a significant growth determinant
and that its exclusion may be causing omitted variable bias. Unlike the Sargan test of overidentifying restrictions, the Hansen test is consistent in the presence of heteroskedasticity and autocorrelation.
The third specification “test” is a check on whether the number of instruments in instrumented regressions is large. As the instruments become numerous relative to the sample size,
they can overfit the instrumented variables, biasing the results toward those of OLS (in the case
of 2SLS) or feasible GLS (in the case of GMM). In the extreme case, where instruments match
or outnumber observations, the results will match those of OLS or FGLS. However, the literature
provides little guidance on how many instruments is too many (Ruud, 2000 (p. 515)). Proliferation of collinear or nearly collinear instruments can also cause the two-step estimate of the covariance of the moments, which is the basis for the optimal twos-step GMM weighting matrix, to
be singular.15
14
I apply the test to OLS and 2SLS regressions using my “abar” module for Stata.
The two-step weighting matrix is (Z'HZ)-1, where Z is the instrument matrix and H is a robust proxy for covariance of the errors. Normally in Arellano-Bond/Blundell-Bond estimation rank(H)=N, the number of individuals in
the panel. This is because H is block diagonal, with one block for each individual. Each block is an outer product
15
25
Indeed, this appears to have happened in the original Dalgaard et al. regression, and this
“test” is only relevant for that regression. In Arellano-Bond and Blundell-Bond GMM regressions, one “GMM-style” instrument is generated for each instrument variable, time period, and
available lag (Holtz-Eakin et al., 1988; Arellano and Bond, 1991). Instruments can easily number in the hundreds. Where the Hansen and Tarp GMM specification covers 4 time periods and
uses at most 1 or 2 lags of 6 instrumenting variables, the newer Dalgaard et al. one covers 6 periods, imposes no lag limits, and uses 12 instrumenting variables, leading to 303 instruments for
371 observations in my reproduction.16
In performing the “test” of excessive instruments, the rule of thumb I use is that the number of instruments should not exceed the number of countries in the regression.17 Typically there
is an average of 6 observations per country in the variants of the Dalgaard et al. regression that I
run, so this rule is equivalent to requiring that the ratio of instruments to observations not exceed
about 0.17.
If a modified regression fails one of these specification tests, the question then is what to
do about it. One possible response to an invalid specification is to simply not report the results.
Another is to report the results but document that they come from an invalid specification. A
third is to make judicious additional changes to the failing specification so that it passes. I sometimes take the second approach, sometimes the third. On the one hand, searching for additional
modifications that can allow the specifications to pass tests can rapidly raise the complexity of
the testing and open the door to whimsy. On the other hand, minimal changes sometimes can
eiei', where ei is the column vector of one-step residuals for individual i. These blocks have rank 1. As the number of
columns in Z approaches rank(H), the risk of singularity of Z'HZ rises.
16
In their own paper, the authors note this problem. But they report that limiting the number of lags does not affect
their results significantly and prefer to report the results from the unlimited regression as simpler, apparently not
noticing the singular matrix problem.
17
I thank Henrik Hansen for this rule of thumb.
26
make invalid tests much more meaningful. For example, it useful and relatively un-whimsical to
limit the number of instruments in variants of the Dalgaard et al. regression. And autocorrelation
of various orders turns out to be endemic in the results from the sample-expansion test; some effort at overcoming it makes the results from this important test more useful.
To be precise, I make three additional changes in order to reduce the number of modified
regressions that fail specification tests. First, I add the log of initial population as regressor in all
robustness tests, except for the test that simply drops outliers from the original regression. All the
2SLS regressions I test use this variable as an instrument for aid because of the well-known bias
among donors toward small countries. But perhaps because of the economic performance of
China and India since the early 1990s the variable has picked up significance for growth too, especially under the sample-expansion test, which extends most of the regression samples to
2001.18 This change not only allows many of the modified 2SLS regressions to pass the Hansen J
test, it also eliminates some occurrences of AR(1).
Second, I perform a version of the sample-expansion test that incorporates several
changes to remove or accommodate autocorrelation. I call this the “AR-robust” sampleexpansion test. Autocorrelation of up to order 4 occurs in many of the expanded-sample regressions. For example, the Arellano-Bond test results for AR() of various orders in the Burnside and
Dollar regression on the enlarged sample are:
Order
z
p
1
2.64 0.008
2
1.65 0.098
3
–1.77 0.076
4
2.32 0.021
where z is the (normally distributed) test statistic and p is the corresponding two-tailed probabil-
18
Except that the data set is only extended to 1997 or the Colliar and Dehn regression, for lack of the shock variable
after 1997, and not extended at all for the Guillaumont and Chauvet regression, for lack of their environment variable after 1993.
27
ity. The source of this autocorrelation is not obvious. It may be a statistical artifact. Indeed, the
first change I make to deal with autocorrelation in the sample-expansion test, switching from
four- to five-year periods, eliminates all the autocorrelation of concern, except for AR(1) in the
OLS and 2SLS regressions. Having restricted the problem to AR(1) in OLS and 2SLS, I then instrument almost all right-hand-side variables in these regressions with their one-period lags in
order to make the regressions consistent even if these variables are predetermined. I exempt only
the Collier and Dehn price shock variables, the Collier and Hoeffler post-conflict 1 variable, and
interaction terms involving them. The shock and post-conflict variables are quite stochastic and
hard to instrument, and at least the price shock variable should not have a large predetermined
component. Finally, I report standard errors that are “clustered” on the country identifier, making
them robust to autocorrelation.19
The third change I make to pass specification tests is to limit the number of instruments
in the Dalgaard et al. regression. In standard difference and system GMM, sets of “GMM-style”
instruments (Holtz-Eakin et al., 1988; Arellano and Bond, 1991) embody the expectations:
∑w
i ,t −l
∆eit = 0 for each t and l , L1 ≤ l ≤ L2
i
where w is an instrumenting variable, e, is the residual vector, i is the panel index, t the time index, and L1 and L2 define the range over which lags can be taken. (Typically L1=0 or 1.) Thus
there is one column in the instrument matrix for each w, t, and l. In testing the Dalgaard et al.
regression, I find that even setting L2=1 allows too many instruments. I therefore group together
columns of the instrument matrix that are for the same w and lag distance and combine them by
addition in order to generate a smaller set of moment conditions, which work out to imply the
expectations:
19
An alternative approach would be to increase the period length until all autocorrelation disappears—in practice
28
∑w
i ,t − l
∆eit = 0 for each l , L1 ≤ l ≤ L2 .
i ,t
I find that when instruments are combined in this way, L2 can take a value of up to 3 without violating the rule of thumb. So in all tests of the Dalgaard et al. regression, I “collapse” the instruments and set L2=3.20
C. Theoretical issues in interpreting the results
If Leamer’s (1983) extreme bounds analysis is applied to the results of this testing, then a coefficient will be deemed robustly different from 0 only if it is significantly different from 0 in every
test. However, as Sali-I-Martin (1997) argues, this definition of robustness may be too extreme.
For example, I could test the robustness of a regression by averaging together all observations for
each global region, generating a sample of some 6 observations. Presumably almost no regression would pass this test. One could argue that this test is “unfair,” which is to say, too demanding to generate meaningful results. But there is no bright line dividing fair tests from unfair ones.
Indeed, in this test suite, the 12-year-period test destroys every regression it can be applied to. It
is not obvious a priori whether this means the test is too strong or the regressions too weak. For
this reason, as Sali-I-Martin suggests, robustness should be thought of a continuous rather than
dichotomous concept. Results can be more or less robust.
Sala-I-Martin offers his own procedure for assessing robustness. In essence, he estimates
the cumulative distribution function for a coefficient of interest by running a large number of
variants of the regression it comes from. The robustness of a coefficient is then the fraction of
the cumulative distribution that is on one or the other side of zero. For example, a coefficient
would be robustly different from 0 at the conventional level of significance if 95% of its cdf is
above or below zero.
about eight years. But this would destroy more information than the approach I use.
29
The validity of this inference is based on the assumption, however informal, that the set
of regressions actually run is a representative sample of all possible variants of the original regression. For the collection of tests assembled here, that assumption does not seem valid. Consider the set of tests that involves varying how total aid receipts are measured. As described
above, two of the three aid definitions are highly correlated in practice. So regressions that originally used the third definition are subjected to two nearly identical aid-related tests. Sala-iMartin’s algorithm would treat these two tests as distinct, giving them nearly equal weight, rather
than as what is essentially an unrepresentative oversampling of one test. Similarly, one subset of
tests, those expanding the sample, cannot be applied to the Guillaumont and Chauvet regression.
It does not seem plausible that the test suite is representative both with and without this important subset of tests.
In sum, the sampling of specification space that is made here is minimally arbitrary, but
cannot be assumed to be representative of all possible tests. Thus while Leamer’s definition of
robustness may be to harsh for this context, Sali-I-Martin’s has its own limitations. This would
be true even if I performed every possible combination of tests in the suite rather than just one at
a time. In the end, it seems that human judgment applied to the full set of results must substitute
for mechanical definitions of robustness. This in turn argues for keeping the number of tests
small enough for the human mind to embrace.
III. Results
In the first step of the testing process, I use the authors’ data sets to reproduce their original re-
sults. (See Tables 6–10. The dependent variable in all the regressions is average annual real
GDP/capita growth.) All of the reproductions exhibit the same pattern of results as the original
20
I use the “collapse” sub-option of my xtabond2 module for Stata.
30
and all but one have the same sample size.21 The Burnside and Dollar, Collier and Dehn, and
Hansen and Tarp reproductions are perfect. Since the purpose of the paper is to test robustness,
the inexact matches are not a major problem. If the results from the tested regressions are robust,
they should withstand whatever minor changes in data or specification cause the discrepancies in
my reproductions.
I discovered two important specification issues in the original regressions. One was a
multicolinearity problem in the Collier and Hoeffler regression. In their preliminary regression
3.1 (not regression 3.4, which is reproduced here), they include the variables post-conflict 1,
post-conflict 1×policy, and post-conflict 1×aid2, along with post-conflict 1×aid ×policy. These
four terms involving post-conflict 1 all have absolute t statistics of 0.5 or less. Collier and Hoeffler then search for a specification iteratively, by dropping the least significant of these terms
one-by-one and rerunning the regression. But in my reproduction of 3.1, post-conflict
1×aid×policy has a partial correlation of 0.985 with post-conflict 1×aid, making the two statistically indistinguishable. Thus the Collier and Hoeffler results ought to be interpreted as pertaining
to either post-conflict 1×aid ×policy or post-conflict 1×aid. Occam’s razor argues for the latter.
The second has already been mentioned. In the Dalgaard et al. regression, the two-step
estimated covariance matrix of the moments turns out to be singular.22 I avoid this problem in
my reproduction by reducing the number of instruments exactly as described above. My reproduction has their key terms still quite significant, and with larger magnitudes than in the original.
21
The Dalgaard et al. regression was executed with the DPD for Ox package. It turns out that an undocumented
limitation in this software—incomplete observations that create gaps in the time series must always be included in
the data file rather than deleted—led to a slight mishandling of the data. I use my xtabond2 module for Stata, which
does not have this limitation. This explains the difference in samples.
22
The DPD for Ox package computes a generalized inverse in such cases.
31
Table 6. Reproduction of Burnside and Dollar, Collier and Dehn results
Regression
Log initial real GDP/capita
Ethno-linguistic fractionalization, 1960
Assassinations/capita
Ethno-linguistic fractionalization × Assassinations/capita
Sub-Saharan
Africa
Fast-growing East Asia
Institutional quality (ICRGE)
M2/GDP, lagged
Policy
Aid/GDP
Aid/GDP×policy
Positive shock
Burnside &
Dollar 5/OLS
–0.60
Collier &
Dehn 3.4
(OLS)
–0.77
(–1.02)
(–1.32)
–0.42
–0.35
(–0.57)
(–0.45)
–0.45
–0.37
(–1.68)
(–1.27)
0.79
0.63
(1.74)
(1.31)
–1.87
–2.08
(–2.41)
(–2.83)
1.31
1.21
(2.19)
(1.90)
0.69
0.67
(3.90)
(3.57)
0.01
0.02
(0.84)
(1.12)
0.71
0.86
(3.63)
(4.23)
–0.02
–0.16
(–0.13)
(–1.23)
0.19
0.10
(2.61)
(1.70)
0.00
(0.18)
Negative shock
–0.03
(–2.38)
∆Aid/GDP ×negative shock
0.04
∆Aid/GDP ×positive shock
0.00
(3.17)
(–0.01)
Aid/GDP, lagged×negative shock
0.01
Aid/GDP, lagged×positive shock
0.02
(1.23)
(2.40)
270
234
Observations
0.39
0.46
R2
0.54
0.88
Arellano-Bond AR(1) test (p value)
Period dummies and constant term not reported. Heteroskedasticity-robust t statistics in parenthesis. Entries significant at 0.05 in bold.
32
Table 7. Reproduction of Collier and Dollar, Collier and Hoeffler results
Log initial real GDP/capita
Collier &
Collier &
1
Dollar 1.2 Hoeffler 3.4
0.70
0.69
1.13
1.11
Institutional quality (ICRGE)
0.12
0.14
0.73
0.93
CPIA
1.16
1.15
2.89
2.88
0.14
0.12
2.15
1.88
–0.03
–0.03
2.20
2.20
Aid/GDP×policy
(Aid/GDP)
2
0.18
Aid×policy×post-conflict 1
3.92
Observations
R2
344
0.37
0.63
344
0.38
0.61
Arellano-Bond AR(1) test (p value)
Period and region dummies and constant term not reported. Heteroskedasticity-robust t statistics in parenthesis. Entries significant at 0.05 in bold. Reproduction is not exact, but exhibits the same pattern and
matches in sample size.
1
As revised in Collier and Hoeffler (2002), regression 1.1, where five erroneous observations were deleted.
33
Table 8. Reproduction of Hansen and Tarp results
Regression
Average annual GDP/capita growth, lagged
1.2 (2SLS) 3.2 (GMM)
–0.37
(–7.09)
Log initial real GDP/capita
Ethno-linguistic fractionalization, 1960
0.09
–3.56
(0.14)
(–1.05)
0.11
(0.12)
Assassinations/capita
Ethno-linguistic fractionalization × Assassinations/capita
Sub-Saharan Africa
–0.46
–0.53
(–2.02)
(–2.31)
0.92
1.00
(2.17)
(2.75)
–2.25
(–2.98)
Fast-growing E. Asia
1.52
(2.42)
Institutional quality (ICRGE)
0.81
(4.57)
M2/GDP, lagged
0.01
Budget surplus/GDP
9.12
(0.55)
(2.49)
Log (1 + inflation)
Sachs-Warner
Aid/GDP
(Aid/GDP)
2
∆(Aid/GDP)
–1.13
–0.19
(–2.30)
(–0.30)
1.70
2.83
(3.36)
(4.37)
0.24
0.90
(2.34)
(4.22)
–0.01
–0.02
(–2.38)
(–3.83)
–0.70
(–4.91)
∆(Aid/GDP)
2
0.01
(3.64)
231
213
Observations
2
0.38
R
0.76
0.12
Arellano-Bond test for AR(1) (p value)
0.81
0.39
Hansen J (p value)
Period dummies and constant term not reported. Robust t statistics in parenthesis. For GMM, t statistics
are autocorrelation-robust too, and Arellano-Bond test is for AR(2) in first differences. Some coefficients
differ from original by a factor of 100 because of scaling changes. Entries significant at 0.05 in bold.
34
Table 9. Reproduction of Dalgaard et al. results
Log initial real GDP/capita
2.03
Budget surplus/GDP
0.09
(1.67)
(0.55)
Log (1 + inflation)
–2.98
(–2.88)
Sachs-Warner
1.57
(1.80)
Aid/GDP
1.47
(4.02)
Aid/GDP × tropical area fraction
–1.33
(–2.62)
371
Observations
0.37
Arellano-Bond test for AR(2) in first differences (p value)
0.21
Hansen J (p value)
Period dummy and constant term not reported. Unlike in original, to limit the number of instruments, at
most 3 lags of instrumenting variables are used, and sets of instruments are combined by addition, as
described in text. t statistics (in parentheses) are heteroskedasticity- and autocorrelation-robust and include the Windmeijer (2000) finite-sample correction. Entries significant at 0.05 in bold.
Table 10. Reproduction of Guillaumont and Chauvet 2SLS results
Log initial real GDP/capita
–2.51
(–3.11)
Mean years secondary schooling among those over 25
0.93
(1.16)
Population growth
–0.83
(–2.64)
M2/GDP, lagged
0.07
(2.64)
Barro-Lee political instability, lagged
–2.03
Ethno-linguistic fractionalization, 1960
–2.13
(–1.08)
(–2.04)
Environment/low vulnerability
0.53
Aid/GDP
0.78
(1.91)
(1.47)
Aid/GDP×environment
–0.15
(–1.68)
68
Observations
0.63
R2
0.08
Arellano-Bond test for AR(1) (p value)
0.98
Hansen J (p value)
Period dummy and constant term not reported. Heteroskedasticity-robust t statistics in parenthesis. Entries significant at 0.05 in bold.
35
I run 86 robustness checks in all. Full results are at <www.cgdev.org>. Here, I report full
details only for the Burnside and Dollar regressions, as an illustration, and results on key coefficients for the rest.
Table 11 shows the full Burnside and Dollar test results. Note first that the testing is not
nihilistic: some regressors survive all or most of the tests. Dummies for Sub-Saharan Africa and
fast-growing East Asia, the governance and policy indexes, and the newly added population
variable are usually significant at or near the 0.05 level, frequently enough that these do appear
to be true regularities in the data. But aid×policy, the essential term for Burnside and Dollar, is
more fragile. Switching to the stripped-down control set of Collier and Dollar raises the significance level of aid×policy above 0.05. Adopting the Guillaumont and Chauvet controls depresses
it further, albeit with AR(1). Only the Dalgaard et al. control set, not so different from Burnside
and Dollar’s original, leaves the key term significant. Changing the definition of aid does reduce
the coefficient and, though not dramatically, its significance. Switching to the Collier and Dollar
definition of policy as CPIA completely eliminates the result. 23 Going to 12-year periods also
erodes the t statistic.
In a counterpoint to the focus of Leamer (1983), Levine and Renelt (1992), and Sali-IMartin (1997) on the choice of regressors as a source of fragility, it appears that modifying the
sample affects results much more than modifying the regressor set. Strikingly, removing seven
additional outliers (Botswana 1978–81, 1982–85, and 1986–89, Gabon 1974–77, Mali 1986–89,
and Zambia 1986–89 and 1990–93) completely eliminates the result, sending the coefficient on
aid×policy slightly negative. Expanding the dataset to 2001 and to new countries also gives
aid×policy a negative but insignificant coefficient. (Easterly et al. (2004) get the same result
when extending to 1997.) Excluding outliers from the expanded-sample regression actually
36
strengthens this contrary result, so that result is not itself driven by a few outliers. Unfortunately,
the expanded-sample regressions exhibit autocorrelation of order up to 4. So the final two columns show the results after switching to five-year periods to expunge the higher-order autocorrelation, and after instrumenting all variables with their lags and clustering the standard errors by
country to make the results robust to autocorrelation. Aid×policy remains insignificant.
The results from the original regression and the “AR-robust,” expanded sample regression are illustrated in Figure 1, with and without the outliers picked by the Hadi procedure. Each
graph in the figure shows the partial scatter plot of GDP/capita growth versus aid×policy in the
5/OLS regression. The two digits in the data point labels indicate the first year of the period for
each observation. Outliers are marked separately, and two partial regression lines are shown, one
for the full sample, one for the sample excluding outliers. Note that the second line is not the best
fit to the non-outlier data points as plotted. Deleting observations causes the estimated coefficients to shift and all remaining data points in the partial scatter to move. The second line therefore is the best fit to the data points in their post-exclusion positions, which are not shown.
Figure 1 shows that in Burnside and Dollar’s original regression, Botswana had very high
aid×policy and fairly high growth throughout the 1980s, controlling for the other regressors,
while Zambia was opposite on both counts in the late 1980s and early 1990s. Their experiences
seem to drive the original 5/OLS result on aid×policy. Moreover it seems quite possible that the
Botswana observations are a case where reverse causality plays a role, with high growth (and
perhaps good policies) attracting more aid. When aid and aid×policy are instrumented they cease
to be outliers. (Results not shown.)
Table 12, Table 13, and Table 14 report results on key terms in all the tested regressions.
Because not all tests were applicable to all regressions, some cells are blank. The test involving
23
Ram (2003) performs a similar test.
37
the definition of aid as EDA/real GDP, for example, is not applicable to regressions that originally use it. Using 12-year periods does not work for the Collier and Hoeffler regression, because
the definition of their post-conflict 1 variable assumes 4-year periods. Some regressions do not
have a policy variable and so were exempt from policy-related tests.24 Lack of higher-frequency
data for Guillaumont and Chauvet’s environment variable prevents short-period tests.
Table 12 has results for most of the tests inspired by “whimsical” differences among the
original regressions. It turns out that the first test, switching to the Burnside and Dollar control
set, generally reinforces regressions that did not use it in the first place. The Dalgaard et al. subset of the Burnside and Dollar controls has a similar effect, except that it undermines Collier and
Dehn. The slim Collier and Dollar control set is more destructive, leaving only the Hansen and
Tarp 2SLS and Dalgaard et al. results significant at 0.05. These, along with Collier and Hoeffler
and Hansen and Tarp GMM pass the Guillaumont and Chauvet control test. Overall, the Collier
and Dehn results are most fragile to control changes.
Altering the definitions of aid proves to be a mild test. As expected, in the first four tested
regressions, which use real GDP in the denominator of aid, switching between ODA and EDA in
the aid/GDP numerator has little effect. Changing the denominator turns out not to be a much
harder test. But changing the definition of policy proves tougher. The Collier and Dehn, Collier
and Dollar, and Hansen and Tarp regressions are all vulnerable to it to various degrees. Aggregating variables over 12 years is uniformly destructive. The drastic reductions in sample size
may be the reason, and may make this test “unfair”; on the other hand, several regressors not involving aid pass this test easily in the Burnside and Dollar test results in Table 11.
Overall, the Collier and Hoeffler result on post-conflict 1×aid×policy (or the collinear
post-conflict 1×aid), the Hansen and Tarp 2SLS coefficients on aid and aid2, and the Dalgaard et
24
However, I do take license to stretch their definition of post-conflict 1 to 5-year periods in the “AR-robust” tests.
38
al. results for aid and aid×tropical area fraction persist most under tests inspired by “whimsy” in
the literature. They are the most whimsy-robust, one could say. Interestingly, except for the Hansen and Tarp 2SLS coefficients, all of these relatively strong results center on highly non-normal
variables. The Collier and Hoeffler post-conflict 1 dummy is 1 for only 13 of the 344 observations in their original sample. Only 38 of the 234 Collier and Dehn observations have negative
shocks. In the Dalgaard et al. sample, 233 of the 371 observations have tropical area fraction=1
and 68 have it 0, leaving 70 in between. Evidently regularities involving such variables are more
resilient to specification changes.
The Guillaumont and Chauvet result on aid×environment is also persistent, but is frequently marred by autocorrelation in the tests. (Indeed, the p value for the Arellano-Bond test for
AR(1) in my reproduction of the original regression is 0.08, as shown in Table 10.)
Only Collier and Dehn’s regression included export shocks per se, so only it was subjected to the sensitivity tests relating to that variable. (See Table 13.) The result on
∆aid×negative shock is robust to the two modifications of the shock definition whether applied
separately or together.
Results from sample-modifying tests appear in Table 14. The first two results columns
are based on regressions on the original authors’ datasets—first for their full sample, second for
the sample excluding outliers picked by the Hadi algorithm on partial scatterplots. The next pair
of columns are analogous, but for the expanded data set. Autocorrelation is prevalent in the expanded-sample results. So the final pair of columns shows the results from making expandedsample regressions “AR-robust.”
Except for the Guillaumont and Chauvet result, all the original OLS and 2SLS results depend on outliers for some or all of their significance. The dependence is particularly heavy for
39
the regressions involving aid×policy. On the other hand, the lack of significance of most of the
coefficients under the sample-expansion test is not driven by new, wayward outliers. Excluding
them does not restore significance. (See Figures 1–8.)
The weakest results again are those on aid×policy, from Burnside and Dollar, Collier and
Dollar, and Collier and Dehn. The Collier and Dehn coefficient on ∆aid×negative shock is
stronger—arguably stronger than a glance at the table suggests. The coefficient is dramatically
reversed by the exclusion of outliers from the original sample. So it would seem that, leaving
aside extreme observations, increasing aid to countries undergoing such shocks slows growth.
However, shocks are by definition outlier events. The 10 outliers identified in the Collier and
Dehn original-sample regression include 8 of the 38 negative shock episodes in the sample. It
may be inconsistent therefore to draw conclusions about the role of shocks in growth having excluded many of the most dramatic examples. On the other hand, 30 shock episodes remain even
after excluding outliers.
Two regressions without such stochastic terms go relatively unscathed in the first four
columns of Table 14. The Guillaumont and Chauvet result goes relatively unscathed but also
relatively untested because I am not able to expand its sample. I do nearly double the sample of
the Hansen and Tarp 2SLS regression, and it does comparatively well in the first four columns.
The coefficients on aid and aid2 achieve similar values and t statistics in the expanded sample as
in the original, and the significance is not dependent on outliers.
However, all these expanded-sample results are in some doubt because all fail autocorrelation tests at 0.05 or 0.06. In the face of specification problems that can bias results, one can err
on the side of inclusion—taking the regressions as they are, caveat emptor—or exclusion—
purging the data of biasing information, but along with it, probably, information that is both rel-
40
vant and non-biasing. Table 14 does both. Specifically, its final pair of columns shows the results
of making the sample-expansion regressions “AR-robust”—using 5-year periods and autocorrelation-robust standard errors, and instrumenting most variables with their lags. All the OSL and
2SLS results that can be put to this test fail it. But again, though tough, the test is not inherently
nihilistic. In the Burnside and Dollar regression, both the Sub-Saharan Africa dummy and the
institutional quality index survived this test.
Meanwhile, the two GMM regressions are, if anything, revivified by the AR-robust sample-expansion test. Of course for these regressions, which already instrument most right-handside variables and have autocorrelation-robust standard errors, the AR-robust test consists only in
switching from 4- to 5-year periods in order to expunge higher-order autocorrelation that can
render instruments invalid. So the test for these regressions is arguably less severe. Nevertheless,
the overall pattern is striking. The most methodologically conservative regressions tested produce coefficients in the expanded sample that, though smaller, are significant at or near 0.05 and
consistent with the authors’ original results. Of these, the Dalgaard et al. results also pass almost
all the “whimsy”-inspired tests (Table 12), the only exception being the 12-year test.
41
Table 11. Robustness tests of Burnside and Dollar regression
Changing controls
Log initial real
GDP/capita
Ethno-linguistic fractionalization
Assassinations/
capita
Ethnic × Assas.
Original
CD GC DHT
–0.60 –0.37 –0.05 –0.43
(–1.02)
(–0.65) (–0.11) (–0.78)
(–0.52)
(–0.57)
(–0.69)
(–0.90)
–0.42
–1.10
–0.86
–0.93
–0.93
–0.83
(–0.57)
(–1.62)
Fast–growing E. Asia
(–1.90)
(–1.14)
(–1.39)
(–1.90)
(–1.75)
–0.36 –0.54
(–1.06)
–0.80
–0.72
–0.51
–0.41
(–1.12)
(–1.18)
(–1.21)
(–1.15)
–0.45
–0.50
–0.47
–0.47
–0.36
(–1.68)
(–1.88)
(–1.74)
(–1.74)
(–1.22)
(–0.99)
0.79
0.87
0.82
0.77
0.51
(1.74)
Sub–Saharan Africa
Changing aid
Changing sample
Changing
Changing policy
periods OrigiODA/
ODA/
New data
New data, AR-robust
nal, no Full No out- Full samPPP
XR
INFL,
GDP
GDP
SACW
CPIA
12-year outliers sample1 liers1
ple1 No outliers
–0.30 –0.32
–0.39
–0.50
–0.61 –1.01
–0.39 –0.49
–1.16
–0.90
(–0.73)
(–1.19)
(–1.09)
(–0.47)
(–0.39)
–0.30 –0.40
(–0.34)
–0.39
–0.39
0.19
0.05
(–1.41)
(–1.65)
(–1.62)
(0.44)
(0.14)
0.49
0.69
0.26
0.24
–0.84
–0.44
(0.68)
(1.50)
(0.41)
(0.38)
(–0.77)
(–0.51)
–1.71 –2.28
–1.20
–1.37
–1.83
–1.77
(1.98)
(1.85)
(1.68)
(0.98)
–1.87
–2.28
–1.68
–1.48
–1.80
–1.81
(–2.41)
(–3.58)
(–2.38)
(–2.06)
(–2.55)
(–2.76)
(–2.00)
(–3.26)
(–2.20)
(–2.56)
(–2.74)
(–2.73)
1.31
0.89
0.78
0.82
0.84
1.55
1.09
1.04
0.74
0.65
1.64
1.37
(2.19)
(1.53)
(1.31)
(1.36)
(1.37)
(2.51)
(1.48)
(1.81)
(1.45)
(1.27)
(1.69)
(1.56)
0.43
Institutional quality
(ICRGE)
M2/GDP, lagged
0.69 0.67
0.71
0.63
0.63
0.15
0.64
0.67
0.38
0.36
0.44
(3.90)
(0.71)
(3.48)
(3.41)
(0.74)
(3.30)
(3.74)
(3.56)
(3.38)
(3.02)
(3.21)
0.01
0.01
0.01
0.01
0.04
0.01
0.01
0.01
0.02
0.01
(1.01)
(1.01)
(0.75)
(0.69)
(1.84)
(0.62)
(0.54)
(0.86)
(1.03)
(0.99)
Policy
0.71 0.91 0.92 0.80
0.81
0.80
0.79
0.78
0.89
1.34
1.40
0.45
0.77
(3.63)
(3.93)
(4.16)
(3.84)
(4.31)
(3.07)
(4.53)
(5.65)
(5.92)
(0.74)
(1.56)
–0.02 0.17 0.01 0.16
0.14
(3.71)
0.01
0.04
(0.84)
(2.68)
(4.66)
(7.57)
Mean years secondary schooling
Population growth
–0.01
Political instability,
lagged
Aid
–0.61
(–0.04)
–0.01
(–0.06)
(–0.94)
0.16
0.04
–0.24
0.07
–0.12
0.06
0.31
0.41
–0.89
(0.73)
(0.80)
(0.72)
(–0.73)
(0.46)
(–0.52)
(0.26)
(1.15)
(1.40)
(–0.98)
(0.18)
0.19 0.13 0.06 0.19
0.14
0.05
0.15
0.00
0.12 –0.05
–0.15
–0.28
0.39
–0.19
(–0.13)
Aid × policy
(2.61)
Log population
(0.88)
(1.73)
(0.07)
(2.27)
(1.95)
(1.63)
(2.32)
(0.01)
(1.31)
(–1.04)
(–1.54)
(0.97)
(–0.45)
0.18 0.49 0.35
(1.06)
0.39
0.36
0.40
0.27
0.17
0.40
0.40
0.10
0.22
(1.18)
(2.50)
(2.44)
(2.52)
(1.67)
(0.85)
(3.19)
(3.25)
(0.41)
(1.06)
(3.73)
(2.28)
(–0.45)
Observations
270 278 262 278
275
272
268
264
97
263
430
420
287
276
2
R
0.39 0.43 0.41 0.42
0.46
0.46
0.43
0.38
0.61 0.41
0.37
0.38
0.39
0.40
0.34
0.32
0.36
0.92
0.31 0.19
0.08
0.13
AR(1) (p value)
0.54 0.48 0.05 0.24
0.01
0.04
1
Regression fails Arellano-Bond test for AR(1) at 0.05 for either the full regression sample or that excluding residual–lagged residual outliers.
Period dummies and constant term not reported. All t statistics are heteroskedasticity-robust; those in last two columns also robust to arbitrary patterns of autocorrelation. Entries significant at 0.05 in bold.
42
Table 12. Coefficients on key terms under specification-modifying tests (original data set)
Changing controls
Specification
Key
term
Aid ×
Burnside
policy
& Dollar
Aid ×
policy
Collier & ∆Aid ×
Dehn
negative
shock
Aid ×
Collier & policy
Dollar
Original BD
0.19
(1.73)
(1.06)
(2.27)
(1.95)
(1.63)
(3.02)
(0.01)
(1.31)
278 262
0.03 0.02
278
0.04
275 272
0.06 0.02
296
0.09
264
0.15
97
–0.02
(1.76)
(0.46)
(0.51)
(0.61)
(1.02)
(1.33)
(1.65)
(1.07)
(–0.16)
0.04
0.02 0.02
0.02
0.03 0.01
0.03
0.02
0.01
(3.17)
(1.11)
(1.21)
(0.93)
(2.83)
(4.41)
(1.93)
(0.83)
(1.03)
234
242
227
242
281
281
256
268
51
–0.01
0.20
0.17
0.04
0.07
0.06
0.19
(–0.24)
(2.71)
(1.72)
(1.65)
(1.44)
(1.19)
(1.64)
374
349
349
347
351
388
119
0.111 0.161
0.30
0.04
0.15
0.181
0.14 0.21
(2.15)
(2.87)
344
337
Hansen & Aid
Tarp
2SLS
Aid2
(3.92)
(3.54)
(2.70)
(3.46)
(3.64)
(3.93)
(3.03)
(4.13)
344
337
374
349
349
347
351
388
0.24
0.32 0.38 0.391
0.74
1.00
0.24
0.113
(2.34)
(2.75)
(1.85)
(2.99)
(2.61)
(1.45)
(1.13)
–0.01 –0.01 –0.011 –0.08 –0.09
–0.01
0.003
–0.01
–0.01
(3.27)
(–2.60) (–2.94)
(–1.16)
(–2.33)
(–2.51)
(–1.31)
(–1.14)
232 206
1.04 1.12
232 231
1.04 –0.05
231
2.20
264
50
0.91
216
1.01
(4.22)
(1.64)
(1.64)
(1.59)
(2.01)
(1.46)
0.06 –0.13
∆Aid
–0.70
(3.04)
(–3.07)
0.20
231
0.90
–0.02
Aid
(3.81)
(–2.38)
Aid2
∆(Aid2)
EDA/ ODA/ ODA/ INFL,
real real XR BB,
INFL,
DHT GDP GDP GDP SACW SACW CPIA 12-year
0.14 0.05
0.00
0.12
0.19
0.26
270
0.10
0.18 0.16
Hansen
& Tarp
GMM
Changing
periods
Changing policy
(2.61)
PostCollier & conflict
Hoeffler 1 × aid
× policy
Aid
CD GC
0.13 0.061
Changing aid
–0.02 –0.02 –0.02
(–3.83)
(–0.03)
–0.02
–0.02
(–1.04)
(–1.45)
(–0.49)
–0.52 –0.71 –0.52 –0.83 –1.79
(–1.07) (–2.41)
(–1.07)
(0.16)
–0.80
–0.86
(–4.91)
(–1.50) (–1.93)
(–1.50)
(–0.96)
(–1.92)
(–2.51)
(–1.88)
0.01
0.01 0.02
0.01
0.03
0.11
0.01
0.01
(3.64)
(0.97)
(1.62)
(0.97)
(0.10)
(1.15)
(1.87)
(1.00)
213
213 181
1.47 1.37 1.47 1.34
213
214
214
0.76 0.29
213
215
(4.02)
(3.50)
(2.99)
(2.69)
(4.20)
(3.32)
0.15
(0.02)
Dalgaard
Aid ×
–2.30
-1.33 –1.73 –1.70 –1.55
–0.87 –0.23
et al.
(-2.62) (–4.10) (–2.80) (–3.15)
(–4.27) (–2.37)
(–0.14)
tropical
GMM
area
371 354 371 315
371 365
116
fraction
Guillau- Aid ×
–0.15 –0.16 –0.15
–0.12 –0.491 –0.351
–0.161
–0.151 –0.14
(–1.79) (–2.01) (–1.88)
(–1.82) (–2.03) (–1.96)
(–1.91)
(–2.30)
(–2.38)
mont & enviChauvet ronment
71
73
73
66
66
66
68
69
68
1
Regression fails Arellano-Bond test for AR(1) at 0.05 significance level for either the full regression sample or that excluding residual–lagged residual outliers. 2Regression fails Arellano-Bond test for AR(2) at in
first differences at 0.05. 3Regression fails Hansen J test of overidentifying restrictions at 0.05.
All t statistics are heteroskedasticity-robust; those for GMM regressions also autocorrelation-robust. Except for original Hansen and Tarp regression, all GMM standard errors include the Windmeijer (2000) finite-sample correction. Entries significant at 0.05 in bold.
43
Table 13. Coefficients on key terms in Collier and Dehn regression under tests of shock
definition
Distribution of forecasting errors used Country- Countryfor shock definition: specific specific
Shock measure- Price
ment: change
Aid × policy
∆Aid × negative
shock
0.10
Share of
GDP
0.07
Pooled
Pooled
Price
change
Share of
GDP
0.06
0.04
(1.76)
(1.06)
(1.00)
(0.91)
0.04
0.18
0.03
0.50
(3.17)
(1.96)
(2.35)
(4.25)
Observations
234
234
234
234
Heteroskedasticity-robust t statistics in parenthesis. Those significant at 0.05 in bold. First results column
is for original specification.
44
Table 14. Coefficients on key terms under data set–modifying tests
Specification
B&D 5/OLS
key term
Aid × policy
Observations
Aid × policy
Collier & Dehn
Collier & Dollar
Collier & Hoeffler
∆Aid × negative shock
Observations
Aid × policy
Observations
Post-conflict 1
× aid × policy
Observations
Aid
Hansen & Tarp 2SLS
Aid
2
Observations
Aid
0.19
–0.05 –0.151 –0.281
0.391
(2.61)
(–0.45)
(–1.04)
–0.19
(–1.54)
(0.97)
(–0.45)
270
0.10
263
0.11
430
0.031
420
0.011
287
0.16
276
0.35
(0.58)
(0.05)
(1.39)
(1.81)
0.031 –0.161
0.01
0.03
(–1.75)
(0.64)
(0.32)
388
364
0.001 –0.022
297
–0.03
279
–0.03
(–0.30)
(–0.43)
(–0.58)
521
506
1
0.08 –0.102
296
0.09
291
0.22
(1.70)
(1.11)
0.04
–0.06
(3.17)
(–1.33)
234
0.14
224
0.07
(2.15)
(1.06)
344
0.18
341
1.18
(3.92)
(2.12)
(2.12)
(–0.29)
(0.96)
(0.43)
344
0.24
333
0.15
521
0.181
495
0.181
296
–0.01
287
–0.02
(2.34)
(1.82)
(2.35)
(2.54)
(0.06)
(2.13)
(–0.07)
(–0.20)
–0.01 –0.005 –0.011 –0.011
0.00
0.00
(–2.38)
(–1.90)
(–2.28)
(–1.43)
(0.27)
(0.38)
231
0.90
229
409
0.163
406
294
0.29
293
(4.22)
(0.81)
(1.86)
–0.02
–0.0023
–0.01
(–3.83)
(–1.01)
(–1.95)
–0.70
3
–0.30
(–4.91)
(–1.12)
(–2.43)
0.01
3
0.01
(3.64)
(1.08)
(2.19)
Observations
213
Aid
1.47
516
0.194
381
0.41
(4.02)
(2.60)
(4.39)
Aid
Hansen & Tarp GMM
Expanded sam- Expanded sample,
Original
ple
AR-robust
Full
No outFull No out- Full sam- No outsample
liers
sample liers
ple
liers
2
∆Aid
∆(Aid2)
–0.18
0.002
Aid × tropical
–0.104
–0.39
-1.33
(-2.62)
(–1.30)
(–3.73)
area fraction
371
Observations
450
343
Aid × environ–0.15 –0.11
(–1.79)
(–1.96)
Guillaumont & Chauvet ment
Observations
68
67
1
Regression fails Arellano-Bond test for AR(1) at 0.05 for either the full regression sample or that excluding residual–lagged residual outliers. 2Fails same test at 0.06. 3Regression fails test for AR(3) in firstdifferences at 0.002, rendering several instruments invalid. 4Regression fails test for AR(3) and AR(4) in
first-differences at 0.05, rendering several instruments invalid.
All t statistics are heteroskedasticity-robust; those in last two columns or in GMM regressions also autocorrelation-robust. Except for original Hansen and Tarp regression, all GMM standard errors include the
Windmeijer (2000) finite-sample correction. Entries significant at 0.05 in bold.
Dalgaard et al. GMM
45
Figure 1. B&D regression 5/OLS: Partial scatter of GDP/capita growth versus aid×policy
Original data
GAB74
GDP/capita Growth
-5
0
5
10
CMR78
ZMB86
ZMB90
SYR74
DOM70
EGY82
NGA70
PRY78
EGY74
GAB70
ECU70 SYR78
MEX78
SYR90
BRA70
LKA82
NGA90
PAK82
ARG90
MLI86
KEN70
EGY78
KOR86TTO78
BOL82
PAK78
URY86
BRA86
IDN90
SEN82
URY78
KOR82
CMR82
SLV90
THA86
NGA74
DOM86
NGA86
PAK86
LKA90
ARG74
TUR90
IND86
KEN86
ETH86
MAR82
SOM74
MAR74
NIC74
TUN82
CMR74
CHL90
GAB82
THA90
IDN78
SLE78
IND82
ZWE82
GUY74
PAK90
PRY74
PER78
HTI78
NER78
KOR90
NGA82
BRA82
ZAR82
GMB74
GTM70
COL78
IDN86
TZA82
ZWE86
GTM74
GAB90
IDN82
KEN78
CHL86
TGO78
SLV82
MWI82
CRI70
ZAR70
PHL78
CHL78
LKA78
ARG82
GMB82
MYS90
URY74
KOR74
BRA74
ARG86
COL70
LKA86
MEX70
COL82
TTO74
SLV74
GHA78
COL90
GHA70
VEN90
TZA86
ARG70
PHL86
BOL90
COL86
GHA86
SLE86
PHL74
KOR70
PER90
DOM78
GHA90
URY90
LKA74
MAR78
TUN90
THA82
SEN74
HND78
HND86
PRY70
SLE90
EGY86
SLE70
KEN82
BOL74
SYR70
IND90
DOM74
PER70
DZA74
GUY78
MYS78
PHL70
GTM78
HND70
ZAR86
PER74
TGO74
HND74
IDN74
MEX82
ZMB70
HND90
DZA70
ARG78
HND82
BRA78
PER86 BRA90
SLV70
PRY86
MDG86
TGO86
HTI74
PAK70
GHA82
GUY70
NIC82
CRI90
DOM82
MAR86
CRI74
MEX74
GTM86
ZWE90
SLE82
ECU82
GTM90
KOR78
SLV86
DOM90
IDN70
COL74
MWI78
MYS82
ZMB78
IND78
PAK74
GAB86
HTI82
ECU90
TTO70
HTI70
TGO82
JAM82
THA78
PER82
ECU78
IND74
LKA70
MWI90
EGY90
MAR70
ECU74
ECU86
MYS70
KEN74
VEN74
MEX90
GMB78
ZMB82
BOL78
GUY86
NIC70
CRI86
MYS86
KEN90
MWI86
CRI82
BOL70
TUN86
BOL86
SEN70
SLE74
CRI78
VEN70
SOM78
URY70
ZAR78
GUY82
ZMB74
VEN86
HTI86
PRY82
MYS74
GTM82
THA70
CHL70
PRY90
GMB70
MDG90
JAM78
CIV78
MDG70
NER74
THA74
NGA78
MEX86VEN82
PHL90
TTO82
MAR90
SYR86
SEN78
IND70
CHL82
MDG74
CMR86
CHL74
PHL82
GHA74
ZAR74
URY82
SLV78
VEN78
TTO86
JAM74
BWA78
BWA82
BWA86
-10
CMR90
GAB78
NIC78
ETH82
-10
-5
Non-outliers
Outliers
0
Aid*Policy
5
10
Fit to all data, coef = 0.19, t = 2.61, N = 270
Fit excl. outliers, coef = -0.05, t = -0.45, N = 263
10
Expanded sample, AR-robust
NGA70
BWA80
JOR75
BWA85
GDP/capita Growth
-5
0
5
CMR80
ARG90
DOM70
UGA95 ECU70
PAK80
GAB80
PRY75
BRA70
CYP85
SYR90
CHN90
UGA90
PNG90
NGA85
SYR75
IRN90 MMR95
KOR85
LKA90
MLI95
CHL90
DOM95
IDN90
LKA80
SLV90
TTO95
URY85
GMB80
TTO80
THA90
THA85
CHL85
GHA85
POL95
URY75
MMR80
URY90
SLE80
IDN80
PAK85
KEN85
LKA95
IND95
MAR75
HND75
BOL90
BWA95
ETH95
KOR90
CMR95
MYS90
MAR85
CHL95
BFA95
CIV95
CHN95
PER95
GMB75
GTM75
IND80
GTM70
SGP70
ZAR80
ZWE85
UGA85
PER90
CYP90
GHA70
SYR80 JAM85GAB75
IND85
PRY70
KOR75
TGO95
MMR90
MAR80
NGA90
GHA95
TUN95
GAB90
BFA85
TUN90
TUN80
LKA75
GHA90
ZWE95
CYP95
KOR80
SGP80
PRY80
MEX75
MEX90
TUR85
GTM95
SGP90
IDN85
TUR95
IDN75
HUN95
GTM90
KEN75
TGO85
HTI75
COL85
TUR80
URY95
IND90
SLE70
TGO80
EGY85
CRI95
MEX80
COL90
LKA85
IRN80
SEN80
TUR90
TUN75
SLV95
BOL95
COL70
DOM85
ZAR70
MMR75
KEN80
EGY95
PHL75
MYS80
JAM90
BFA80
BOL85
ECU75
BOL75
ZMB80
ZWE90
NGA95
COG95
DZA95
CRI90
IRN95
GTM85
PRY85
KOR70
PAK90
HND85
SEN75
THA80
SLV85
ARG95
BFA90
ZAF95
NIC80
PER70
VEN90
ARG80
BOL70
KEN95
PAK75
THA75
ECU90
DOM80
BFA75
HTI70
CRI75
COL75
BRA75
MAR70
PRY90
MEX95KOR95
HTI95
PAK95
SLV70
ARG75
COL80
CHL75
MDG95
TUR75
SGP85
HTI80
SLE75
DOM75
CRI85
ZAR85
JAM80
MLI90
NGA75
SLV75
MWI90
CIV85
MAR90
GAB85
SGP75
ETH90
MYS70
EGY90
MYS75
SYR95
PAK70
VEN75
GHA80
PHL70
HND95
PER80
HND70
MWI85
HND90
DOM90
MYS95
URY70
GTM80
PHL85
ECU80
CHL80
ZAR95
VEN70
TUN85
SGP95
COL95
SYR85
MEX85
IND75
KEN90
LKA70
JOR90
ECU85
VEN85
SLE85
MAR95
CMR85
HND80
PHL80
PER75
BRA80
PHL95
THA70
PER85
PNG85
HTI85
PRY95
MYS85
GHA75
URY80
VEN95
MMR70
PHL90
BOL80
CRI80
JOR95
JAM95
TGO90
ZMB75
MDG70
ECU95
CIV90
PNG80
IDN95
PNG95
MDG90
VEN80
CHL70
THA95
SLE90
NGA80
IND70
IRN85
CIV80
SLV80
ZAR75
HUN90MMR85
JOR85
CMR90
SLE95
NER80 HTI90
EGY80
BRA95
BWA90
-10
NIC75
ZAR90
-2
-1
Non-outliers
Outliers
0
Aid*Policy
1
2
Fit to all data, coef = 0.39, t = 0.97, N = 287
Fit excl. outliers, coef = -0.19, t = -0.45, N = 276
46
Figure 2. Collier and Dehn regression: Partial scatter of GDP/capita growth vs.
∆aid×negative shock
GDP/capita Growth
5
0
-5
10
Original data
CMR78
SYR86
GMB90
GAB74
EGY82
PRY78
BWA78
SYR74
EGY74
MEX78
SYR90
NGA86
BWA82
NGA90
ARG90
PAK82
TTO78
SEN82
SLV90BOL82
SLE78
LKA82
PAK78
CMR82
KOR86
URY78
KOR82
ARG74
PAK86
GAB82
BWA86
IDN90
BRA86
GMB82
URY86
LKA90
NIC74
GUY74
KEN86
IDN86
ETH86
NGA74
TUR90
TZA82
ZWE82
TGO78
MAR82
TUN82
CHL90
PRY74
KEN78
GAB90
CMR74
IND82
THA86
GHA78
MWI82
HTI78
IND86
GTM74
BRA74
PER78
BRA82
ZAR82
THA90
BOL74
PER74
KOR90
CHL78
NGA82
KOR74
URY74
GMB74
COL78
PAK90
LKA78
DOM86
ZWE86
IDN78
NER78
SLV82
SYR78
GUY90
TTO74
MAR74
IDN82
ARG86
GAB86
CHL86
ARG82
EGY78
EGY86
PHL78
TZA86
MYS90
COL82
LKA74
COL86
SLV74
HND86
ZMB74
GHA90
VEN90
DOM74
BOL90
GTM78
DOM78
PHL74
LKA86
GHA86
ZMB86
COL90
SLE90
MAR78
GUY78
HND78
URY90
HND90
CRI90
TUN90
PER90
ZMB90
GTM90
THA82
PHL86
MWI78
HND82
HND74
GMB78
TGO86
BRA78
MEX74
ZMB78
MYS78
NIC82
CRI74
MEX82
ARG78
GTM86
SLE82
IND90
GHA82
ZWE90
TGO82
MDG86
MWI90
PRY86
ZAR86
DOM82
COL74
HTI74
PAK74
ECU82
KOR78
VEN86
ECU86
KEN82
MYS86
TUN86
SLE86
MYS82
IND74
DOM90
VEN74
ZMB82
CRI86
IDN74
PER86
HTI82
SOM78
IND78
ECU90
BRA90
MAR86
ECU74
SLE74
THA78
ECU78
KEN90
PER82
EGY90
CIV78
MEX90
BOL78
CRI82
CHL74
SEN74
CRI78
JAM82
NIC86MEX86
DZA74
MDG90
MYS74
ZAR74
KEN74
PRY82
JAM78
GTM82
THA74
MWI86
PRY90
HTI86
GUY82
SEN78
ZAR78
NGA78
TTO82
CMR86
VEN82
GHA74
CHL82
GUY86
MAR90
TTO86
TGO74
PHL90
NER74
GMB86
MDG74
PHL82
URY82
SLV78
VEN78
JAM74
MLI86
SOM74
NIC90
SLV86
BOL86
CMR90
-10
NIC78
GAB78
ETH82
-50
0
50
Change in Aid*Negative Shock
Non-outliers
Outliers
100
Fit to all data, coef = 0.04, t = 3.17, N = 234
Fit excl. outliers, coef = -0.06, t = -1.33, N = 224
GDP/capita Growth
-5
0
5
10
Expanded sample, AR-robust
JOR75
BWA80
NGA70
BWA85
DOM70
NGA85
ARG90
CMR80
UGA95
EGY80
PAK80
ECU70
PRY75
BRA70
GAB80
SYR90
CHN90
PNG90
MMR95
CYP85
IRN90
LKA90
SLE80
MMR80
DOM95
CHL90
IDN90
KOR85
TTO95
GMB80
PAK85
URY75
THA90
TTO80
POL95
URY90
URY85
MLI95
JOR80
BOL90
CHL85
GHA85
MAR75
IDN80
LKA95
ETH95
KOR90
GMB75
THA85
IND95
LKA80
IDN85
KEN85
GTM70
NIC95 SLV90
HND75
SYR75
MYS90
CMR95
CHL95
BWA95
GHA70
PER95
BFA95
CHN95
CIV95
MAR85
ZAR80
CYP90
PER90
BFA85 BOL85
UGA90
MMR90
SGP70
GTM75
EGY85
SYR80
IND80
UGA85
ZWE85
BOL75
PRY70
LKA75
GAB90
NGA90
TUN90
MAR80
TUN95
KOR75
TGO95
ZWE95
COL85
TUN80
PRY80
IND85
BFA90
ZMB95 CHL75
SLE70
MEX90
CYP95
KOR80
GHA90
HUN95
TGO80
SGP90
GAB75
SLV85
GTM90
HND85
GTM95
ZAR70
SGP80
MMR75
TUR90
URY95
GHA95
PRY85
KOR70
COL90
TUR85
JAM90
CRI90
IND90
TUR95
BRA85
GTM85
PHL75
TUR80
MEX80
BRA95
SEN80
GAB85
ZWE90
TGO85
BOL95
HTI70
IRN80
CRI95
IDN75
LKA85
SLV95
SEN75
COG95
MEX75
ZMB80
COL70
JAM85
BFA80
NGA95
ARG95
MYS80
VEN90
THA75
EGY95
IRN95
ZMB85
PAK75
ECU90
NIC80
ECU75
KEN75
SLV70
BRA75
KEN95
DOM80
THA80
DZA95
SGP75
CRI85 NIC90
PRY90
HTI75
ZAF95
BOL70
MLI90
SGP85
PER70
CRI75
HTI95
DOM75
DOM85
PAK90
MEX95
MDG95
SLE75
KEN80
COL75
MEX85
VEN85
GHA80
TUN85
HTI80
ARG80
PAK95
TUN75
MWI90
COL80
TUR75
ARG75
HND90
PER75
BRA90
KOR95
BWA90
ETH90
HND70
MAR90
ZAR95
EGY90
ZAR85
SLV75
ECU85
SYR95
MAR70
DOM90
CIV85
BFA75
PHL70
PER80
MYS75
PAK70
MYS70
LKA70
URY70
JAM80
CMR85
ECU80
NGA75
MYS95
CHL80
GTM80
VEN75
MYS85
KEN90
SGP95
HND80
IND75
PHL85
COL95
MAR95
ZMB90
THA70
PHL95
BRA80
JOR90
PHL80
PRY95
HND95
MWI85
ARG85
HTI85
PNG85
MMR70
PER85
GHA75
VEN70
URY80
VEN95
IRN85
SLE85
MDG70
PHL90
BOL80
CRI80
JAM95
ECU95
TGO90
CIV90
MDG90
PNG95
IDN95
JOR95
PNG80
SLE90
CIV80
VEN80
CHL70
IND70
THA95
NGA80
ZAR75
HUN90
SLV80
MMR85
CMR90
NIC85
SLE95
HTI90
JOR85
NER80
SYR85
ZMB75
-10
NIC75
ZAR90
-100
-50
Non-outliers
Outliers
0
50
Change in Aid*Negative Shock
100
Fit to all data, coef = 0.01, t = 0.64, N = 297
Fit excl. outliers, coef = 0.03, t = 0.32, N = 279
47
Figure 3. Collier & Dollar regression: Partial scatter of GDP/capita growth vs. aid×policy
20
Original data
GDP/capita Growth
10
0
GAB74
SDN94
SDN74TGO94
BWA78
BWA82
PAN90
PRY78 CMR78
NIC94
SYR90
BHS82
BWA86
SYR74
CMR82 ARG90
EGY82
BHS78
ETH86
SDN90
EGY74
TTO78
GUY94
MEX78
GUY90
MLI74
CHL78
SLV90
THA86
DOM86
JAM86
ZWE78
HTI78
BWA74
MLI86
IDN78
KOR82
KOR86
THA90
PER94
IDN90
CHL90
PAN78
SEN82
SYR78
NGA90 CHL86
ETH94
DOM94
DOM74
NIC74
DOM78
ECU74
KEN86
DOM82
VEN90
LKA82
PAK78
SLE78
SLE86
ECU78
PAK82
MAR82
PRY86
GTM90
CRI90
HND86
BGD78
TGO78
DZA82
GMB82
NGA86
EGY78
HTI74
PRY74
MWI90
LKA90
ZAR82
COL90
SLV82
URY78
ETH90
IND94
SDN86
CMR74
URY86
IDN94
URY90
HUN86
HUN82
MWI82
ECU90
IDN74
GAB94
BOL74
COL86
MWI94
NER78
GTM74
BOL90
BGD82
BRA86
MLI82
IDN82
CHL94
CIV94
JAM90
MYS90
SLV86
BRA94
ZWE94
CIV74
GTM78
BGD90
HND90
IND82
GMB74
BWA90
TZA90
KOR90
NGA74
THA94
EGY86
ZMB86
CRI86
THA82
GHA90
DOM90
HUN94
PER78
SEN94
IDN86
TTO82
TZA86
NER86
TUN90
IND86
SLV94
MEX90
NGA94
GAB90
ZWE82
ZWE86
BRA82
COL78
KOR94
MAR94
BOL86
PHL86
MLI94
GAB82
SLV74
MAR74
BRA74
MYS94
GUY74
HTI82
ECU82
KEN78
NIC82
MAR86
PRY90
GHA86
COL94
GTM86
PER90
SEN86
GTM94
ZAR86
PAK86
SDN82
PAK90
EGY90
URY94
GUY86
HND74
MWI74
BWA94
TUR94
URY74
KEN94
SGP78
PAN82
EGY94
ECU94
GHA94
ZAR78
KEN82
COL82
HND78
LKA78
MDG82
KOR74
NER94
SLE82
MYS78
SLE74
BGD74
HND82BOL94
PER86
THA78
MYS86
SEN74
IND90
DZA74
BRA78
GHA78
GMB86
TZA94
LKA74
BGD94
LKA94
TUN78
SEN90
ARG74
GMB78
GMB90
MDG86
NGA82
ZAF94
MLI90
TTO94
PRY94
THA74
CHL82
ARG82
TGO86
MYS82
TGO74
TUN82
SGP82
ARG86
BRA90
LKA86
BOL82
HTI86
GHA82
KEN90
TGO82
CMR94
ARG94
DZA78
BOL78
TUN74
BGD86
ZMB90
NER74
ETH82
PHL94
CRI82
ZWE90
BHS86
TTO90
GUY78
MAR78
PHL78
MEX82
PAN94
JAM82
ZMB78
GTM82
TUN94
ARG78
ECU86
CRI94
MEX74
SYR82
MLI78
IND74
IND78
NER90
PER74
MDG94
PAK74
ZMB82
ZAR94
CIV86
JAM94
PAK94
CRI74
MDG90
PHL74
GAB86
CIV90
MWI86
HTI94
MWI78
VEN86
NIC90
SYR86
MDG78
MAR90
COL74ZAR74
DZA94
PER82
MYS74
MDG74
MEX94
PRY82
JAM78
MEX86
KOR78
HND94
HTI90
KEN74
ZMB74
VEN94
PHL90
CRI78
PAN74
HUN90
SDN78
GUY82 GMB94
BHS90
CHL74
CIV78
SGP74
TUN86
SEN78
CMR86
PAN86
DZA90
DZA86
CIV82
NIC86 SLE94
NGA78
GHA74 SLE90
NER82
TTO86
CMR90
PHL82
URY82
GAB78
JAM74
SLV78
TGO90
NIC78
ZAR90
-10
ZMB94
-15
-10
-5
Non-outliers
Outliers
Aid*Policy
0
5
10
Fit to all data, coef = 0.14, t = 2.15, N = 344
Fit excl. outliers, coef = 0.07, t = 1.06, N = 341
Expanded sample, AR-robust
10
COG80
-30
GDP/capita Growth
-20
-10
0
LBR95
BWA85
GUY90
BWA80
SYR90
PAN90
AGO95
SDN95
CMR80
SLV90
UGA90
ARG90
MOZ95
CHN90
EGY80
UGA95
CYP80
DOM95
CYP85
NGA85
GAB80
CHL90
THA90
CHL85
SDN85
PNG90
ROM80
SOM85
CHN85
IDN90
MWI95
KOR85
MMR95
PAK80
GHA85
THA85
GIN85
SLE80
MYS90
MLI95
IDN80
SDN90
POL95
URY90
TTO95
CYP90
TTO80
GMB80
KEN85
ETH95
LKA90
BWA95
URY85
BFA85
ZAR80
SUR90
CMR95
BOL90
KOR90
SEN95
DOM85
GIN90
UGA85
MMR90
JAM85
ZWE85
GTM90
CRI90
CIV95
MAR85
GAB90
JAM90
PER90 GUY95
BHS80
GHA90
CHN95
MMR80
BFA90
BFA95
NGA90
TGO85
MOZ90
TUN90
BWA90
GIN95
SDN80
LKA80
GHA95
BGD80
TUN95
CRI95
PRY90
IDN85
TGO95
TZA85
PAN95
ZWE90
ETH90
EGY85
SLV95
CHL95
PAN80
NER85
BGD90
SEN85
SUR85
GTM95
COL90
GAB95
EGY90
PAK85
DOM80
EGY95
HND85
SLV85
SYR80
OMN85
HUN95
MEX90
PRY80
BHS85
ZWE95
HTI80
HTI95
HND90
GUY85
BFA80
PER95
ZMB85
BOL95
OMN90
TUN80
DOM90
MAR80
VEN90
ETH80
PRY85
NIC80
SEN80
SGP80
GTM85
MLI85
LKA95
TUR85
MAR90
DZA80
KOR80
ZAR85
TUR90
BRA85
ECU90
COL85
TTO90
TZA90
TZA95
GNB80
COG95
TGO80
T
UR95
MDG85
THA80
MWI90
DZA95
MDG95
BGD95
BOL85
TUR80
POL90
KEN95
CRI85
ZMB80
IND80
URY95
IND85
KEN80
NGA95
IND95
SEN90
MYS80
MNG95
GAB85
HTI85
COG90
NER95
MLI90
JOR90
MEX80
GMB95
SGP85
PAK90
LKA85
IRN95
KEN90
JAM80
ECU80
GMB85
GNB85
HND95
ECU85
SOM80
ARG95
MEX95
NIC95
MWI85
BGD85
NIC90
MWI80
IND90
BRA95
ETH85
CZE95
JOR95
MLI80
CIV85
HUN85
SLE85
SYR85
COL80
GHA80
HND80
COG85
GNB90
BHS90
ROM95
ARG80
BRA90
PRY95
KOR95
CHL80
PHL95
PER80
MAR95
PHL90
TUN85
MDG90
GTM80
JAM95
PHL85
CMR85
ZMB90
MYS95
COL95
MEX85
TGO90
CIV90
PAK95
BGR95
ROM85
SLE90
BOL80
GMB90
GUY80
PER85
MDG80
DZA85
MYS85
PNG85
BRA80
LBR80
PHL80
VEN95
ECU95
PAN85
ROM90
NER90
ARG85
ZMB95
ZAR95
DZA90
URY80
CRI80
IDN95
THA95
TTO85
HTI90
HUN90
PNG95
NGA80
CMR90
SLV80
PNG80
NIC85
CIV80
MMR85
SLE95
LBR85
AGO90
NER80
GNB95
SOM90
ZAR90
JOR80
JOR85
LBR90
-10
Non-outliers
Outliers
0
10
Aid*Policy
20
30
Fit to all data, coef = -0.03, t = -0.43, N = 296
Fit excl. outliers, coef = -0.03, t = -0.58, N = 291
48
Figure 4. Collier & Hoeffler regression: Partial scatter of GDP/capita growth vs. Postconflict 1×aid ×policy
-10
0
GDP/capita Growth
10
20
30
40
Original data
GAB74
SDN94
SDN74
TGO94
PRY78
PAN90
BWA78
CMR78
BWA82
SYR90
CMR82
BHS82
EGY82
ETH86
SDN90
ARG90
BHS78
SYR74
MEX78
BWA86
TTO78
CHL78
MLI74
ZWE78
EGY74
GUY90
THA86
MLI86
NGA90
SLV90
GUY94
DOM86
KOR82
HTI78
KOR86
CHL86
PER94
IDN78
CHL90
THA90
IDN90
PAN78
JAM86
NGA86
DOM94
ETH94
VEN90
SLE78
SLE86
SEN82
NIC74
DOM74
DOM78
ZAR82
ECU74
KEN86
DZA82
PAK82
MAR82
BWA74
GTM90
PRY86
ECU78
PAK78
SYR78
URY78
URY86
DOM82
SDN86
TGO78
ETH90
PRY74
URY90
COL90
LKA82
CRI90
HTI74
HND86
IND94
COL86
HUN82
MWI90
BGD78
NGA74
IDN94
GMB82
EGY78
ECU90
HUN86
SLV82
CHL94
CMR74
IDN82
GTM74
MWI82
LKA90
ZMB86
BOL74
IDN74
IND82
MYS90
BRA86
CIV74
NER78
NGA94
MLI82
ZWE94
KOR90
MWI94
BGD82
BRA94
GTM78
PER78
GAB94
THA82
TUN90
IND86
IDN86
BGD90
COL78
DOM90
SLV86
THA94
TZA90
MEX90
JAM90
BRA74
EGY86
BRA82
ZWE86
MAR94
SLV74
HUN94
TTO82
ZAR86
ZWE82
NER86
MAR86
ZAR78
BOL90
TZA86
GHA90
GMB74
MAR74
CIV94
HND90
COL94
KOR94
MYS94
PRY90
COL82
SLV94
SEN94
CRI86
PHL86
PER90
URY74
GTM94
GUY74
SDN82
BWA90
KEN78
ECU82
GTM86
URY94
PAN82
PAK86
HTI82
TUR94
KEN94
PAK90
GAB90
SGP78
NIC82
GAB82
NGA82
SLE82
HND74
KOR74
KEN82
MDG82
MLI94
MWI74
SLE74
GHA94
EGY94
GUY86
ZAF94
GMB86
BWA94
THA78
MYS78
IND90
BOL86
GHA86
NER94
SEN86
ECU94
HND78
DZA74
GHA78
BRA78
ZMB90
EGY90
TZA94
LKA78
PER86
MYS86
TUN78
TUN82
CHL82
TTO94
SEN74
GHA82
BGD94
PRY94
THA74
DZA78
BGD74
SEN90
MDG86
GMB90
ARG74
HND82
SGP82
MLI90
LKA94
ARG82
LKA74
HTI94
TGO74
ETH82
MYS82
BRA90
ARG94
ARG86
TUN94
KEN90
HTI86
PHL78
ZAR94
NER90
BOL94
PHL94
BOL82
CMR94
TTO90
PAN94
BOL78
MEX82
TGO82
BGD86
ZWE90
MAR78
MEX74
TUN74
PER74
LKA86
ECU86
GTM82
BHS86
TGO86
GMB78
IND78
NER74
CRI94
ZMB78
ARG78
IND74
ZMB94
MLI78
MDG94
CRI74
GUY78
PHL74
COL74
SYR82
PAK94
CRI82
VEN86
CIV86 MAR90
MDG78
ZAR74
ZMB82
JAM94
MDG90
JAM82
DZA94
PAK74
PER82
MDG74
PRY82
MYS74
CIV90
KOR78
MEX86
SYR86
MEX94
GAB86
NIC90
MWI78
KEN74
ZMB74
MWI86
HTI90
VEN94
CRI78
PAN74
JAM78
PHL90
SDN78
HND94
HUN90
GUY82
CIV78
TUN86
CHL74
BHS90
SGP74
GMB94
DZA86
CMR86
CIV82
DZA90
PAN86
NGA78
SLE90
SEN78
SLE94
NIC86
GHA74
URY82
TTO86
NER82
PHL82
CMR90
GAB78
JAM74
SLV78
TGO90
ZAR90
NIC78
0
10
NIC94
20
Post-conflict*Aid*Policy
Non-outliers
Outliers
30
40
Fit to all data, coef = 0.18, t = 3.92, N = 344
Fit excl. outliers, coef = 1.18, t = 2.12, N = 333
20
Expanded sample, AR-robust
GDP/capita Growth
-10
0
10
COG80
MOZ95 UGA90
NIC95
-30
-20
BWA85
GUY90
BWA80
SYR90
PAN90
SDN95
SLV90
AGO95
CMR80
ARG90
EGY80
CHN90
UGA95
CYP80
DOM95
GAB80
NGA85
PNG90
SOM85
SDN85
CYP85
CHL85
THA90
CHL90
MWI95
ROM80
CHN85
MMR95
PAK80
IDN90
LBR95
KOR85
THA85
GHA85
MLI95
MYS90
POL95
SDN90
IDN80
GIN85
SLE80
TTO80
TTO95
KEN85
ZAR80
CYP90
LKA90
GMB80
URY90
SUR90
SEN95
BOL90
BFA85
CMR95
BWA95
DOM85
URY85
ETH95
PER90
CIV95
GIN90
JAM85
MMR90
KOR90
CRI90
GTM90
JAM90
ZWE85
GAB90
MAR85
UGA85
BFA95
CHN95
BFA90
GHA90
MOZ90
MMR80
NGA90
BHS80
GUY95
GIN95
TGO85
BWA90
BGD80
SDN80
TZA85
LKA80
TUN90
TGO95
PRY90
GHA95
SUR85
EGY85
IDN85
CRI95
ETH90
GTM95
PAN95
SEN85
BGD90
ZWE90
EGY95
NER85
DOM80
TUN95
EGY90
PAK85
PAN80
GAB95
HND85
COL90
SYR80
CHL95
MEX90
SLV85
SLV95
HUN95
OMN85
HND90
ZWE95
HTI95
HTI80
PRY80
BOL95
BFA80
GUY85
BHS85
PER95
DOM90
ZMB85
VEN90
SEN80
NIC80
OMN90
MLI85
TUN80
MAR80
TZA95
GNB80
BRA85
LKA95
ETH80
TUR85
GTM85
JOR80
PRY85
ZAR85
TZA90
TUR90
TTO90
TUR95
ECU90
COL85
COG95
KOR80
DZA80
SGP80
TGO80
MWI90
BGD95
BOL85
POL90
TUR80
MDG85
MAR90
MDG95
DZA95
THA80
IND80
KEN95
SEN90
CRI85
ZMB80
IND95
IND85
NGA95
URY95
GMB95
MLI90
KEN80
GAB85
NER95
HTI85
MNG95
MEX80
COG90
GNB85
JOR90
MYS80
GMB85
ECU80
PAK90
JAM80
LKA85
HND95
ARG95
MEX95
KEN90
ECU85
IRN95
SOM80
BGD85
SGP85
NIC90
MWI85
BRA95
MWI80
GNB90
JOR95
IND90
MLI80
CZE95
SYR85
ETH85
ARG80
HUN85
SLE85
ROM95
CIV85
GHA80
COG85
BRA90
HND80
COL80
PER80
BHS90
PHL95
CHL80
KOR95
PHL90
PRY95
MAR95
GTM80
PHL85
JAM95
MDG90
ZMB90
MEX85
TUN85
TGO90
COL95
CMR85
BGR95
PAK95
MYS95
GMB90
BOL80
CIV90
ROM85
PER85
SLE90
PNG85
GUY80
MDG80
BRA80
MYS85
DZA85
VEN95
LBR80
ZMB95
ECU95
PHL80
ARG85
NER90
PAN85
ROM90
ZAR95
DZA90
URY80
IDN95
CRI80
TTO85
THA95
HTI90
HUN90
PNG95
NGA80
PNG80
NIC85
CMR90
SLV80
JOR85
CIV80
MMR85
SLE95
GNB95
LBR85
NER80
AGO90
SOM90
ZAR90
LBR90
-10
0
Non-outliers
Outliers
10
Post-conflict*Aid*Policy
20
30
Fit to all data, coef = 0.09, t = 0.96, N = 296
Fit excl. outliers, coef = 0.22, t = 0.43, N = 287
49
Figure 5. Hansen & Tarp 2SLS regression: Partial scatter of GDP/capita growth vs. aid
15
Original data
GAB74
GDP/capita Growth
0
5
10
CMR78
SYR74
PRY78
EGY82
BWA78
ARG90
SYR78
MEX78
SYR90
LKA82
SOM74
BWA82
KOR86PAK82
EGY78 SEN82
TTO78
TZA86
TUR82
KOR82
PAK78
BWA86
ETH86
BRA86
URY86
THA86
DOM86
CMR82
URY78
TUR90
BOL82
MWI82
IND86
PAK86
NIC74
KEN86
SLV82
GUY90
SLV90 LKA90 NER78
NGA74
MAR82
CHL90
MAR74
GMB82
ARG74
GAB82
IDN90
TZA90
THA90
IND82
TUR74
PRY74
HTI78
ZAR82
TUR86
TGO78
PAK90
KOR90
GAB90
GUY74
GMB74BOL90
ZWE82
SLV74
BRA82
CHL86
ZWE86
GTM74
MWI90
PER78
IDN78
COL78
SLE78
CHL78
LKA78
KOR74
IDN86
PHL78
KEN78
ARG86
ARG82
IDN82
GHA86
COL90
BRA74
NIC90
GHA90
LKA86
MYS90
URY74
PHL86
HND86
COL82
HND90
VEN90
COL86
TTO74
TUN90
HND78
GHA78
PHL74
SEN74
HND82
ZAR86
URY90
ZMB86
TGO86
BOL74
DOM78
TZA82
SLV86
HND74
MAR78
IND90
PER90
THA82
PER86
SLE90
ETH90
ZMB90
NIC82
GUY78
SLE86
CRI90
KEN82
HTI74
ZWE90
GTM90
GTM78
DZA74
PRY86
DOM74
MYS78
GAB86
PER74
IDN74
LKA74
TGO82
GTM86
PER82
MAR86
GHA82
BRA78
DOM82
ARG78
MEX82
EGY86
DOM90
BRA90
KOR78
ECU82
ECU90
CRI74
HTI82
GMB78
MEX74
IND78
JAM82 KEN90
BOL78 CRI86
ZMB78
COL74
MYS82
BOL86
SLE82
IND74
BWA90
ECU86
THA78
TUR78
ECU74
PAK74
MEX90ECU78
ZMB82 MDG90
SOM78
HTI86
EGY90
MYS86
NIC86
CRI82
GUY82
KEN74
VEN74
TUN86
PRY90
GUY86
ZAR78
PRY82
GTM82
CRI78
ZMB74
VEN86
MYS74 GMB86
JAM78
SLE74
PHL90
THA74
SLV78
MAR90
GMB90
MWI86 SEN78
MEX86
TTO82
CHL82
NGA78
VEN82
CMR86
PHL82
CHL74
MDG74
ZAR74 GHA74
URY82
VEN78TTO86
HTI90
NGA90
-10
-5
NGA86
NGA82
ETH82
-10
-5
Non-outliers
Outliers
CMR90 NIC78
GAB78
0
Aid, instrumented values
5
Fit to all data, coef = 0.24, t = 2.34, N = 231
Fit excl. outliers, coef = 0.15, t = 1.82, N = 229
10
Expanded sample, AR-robust
GDP/capita Growth
-5
0
5
NGA70
-10
NIC95
JOR75
ARG90
DOM70 PNG90
CHN90
BWA80
CMR80
URY85
NGA85
SLE80PRY75
BRA70
IRN90
SYR90
EGY80 UGA95
PER90
UGA90
PAK80
BWA85
ECU70
URY75
GMB80
NIC80
GAB80
URY90
LKA90
MAR75
GMB75
BFA95
UGA85
TGO95
IND95
CHN95
IDN90
TTO95
LKA80
KEN85
MLI95
HND75
KOR85
THA85
TTO80
ZWE95
THA90
POL95
DOM95
PAK85
CHL85
SYR75
ZMB85
CYP85
LKA95
SLV90
MMR80
MYS90
JAM85
BRA85
GTM70
GTM75
ZAR80
PRY70
NGA90
IND80
CHL90
KOR90
IRN80
ZWE85
BWA95
NIC90
IDN80
CMR95
ETH95
DOM85
GAB75
TUN80
HTI95
TUR95
GHA95
BOL85
LKA75
CIV95
CHL95
TUR85
HUN95
IND85
ZWE90
ZMB80
GAB90
TUR80
BOL80
BFA85
PHL75
SGP70
DZA95
GHA85
IRN95
SYR80
GHA70
PRY85
KOR75
SEN80
JOR80
TGO85
HTI75
SLE75
MAR80
TUN95
SGP90
ZMB95
CYP95
JAM80
SGP80
COL70
TUN75
MEX75
GTM85
BFA90
LKA85
SLV85
MYS80
BOL95
CRI95
HND85
PER85
SLE70
CRI75
PAK90
BFA80
MAR85
CYP90
IND90
PRY80
PAK75
IDN75
GTM95
PAK95
ARG80
MEX80
NGA95
KOR80
PER95
BFA75
KEN75
ECU90
ARG95
SEN75
BTUR90
RA95
ARG75
MMR75
KEN80
TUN90
IDN85
HTI70
BRA90
ZAR95
NIC85
CHL75
EGY95
VEN90
KOR95
DOM80
URY95
SLE85
PER70
COG95
COL85
EGY85
ZAR70
MEX95
PHL70
THA75
GTM90
PER80
SGP95
MDG95
THA80
SLV95
CRI90
GHA90
BWA90
SLV70
MAR70
COL75
MEX90
ZMB90
PHL85
COL80
COL90
KOR70BOL90
ZAF95
SGP85
BRA75
MYS70
URY70
MWI90
SYR95
DOM75
ZAR85
GAB85
CRI85
TUR75
BOL75
MWI85
MYS95
HTI80
SLV75
JAM90
MYS75
HND70
ETH90
VEN75 KEN95
PAK70
TGO80
ECU85
HND90
PNG85
GHA75
LKA70
HND80
PHL95
EGY90
CIV85
PHL80
ARG85
GHA80
BOL70
HND95
KEN90
VEN85
ECU75
GTM80
CHL70
PER75
TUN85
DOM90
VEN70
SGP75
MMR70
PRY90
MEX85
COL95
IND75
MAR95
BRA80
HTI85
MAR90
MLI90
PNG80
NGA75
CRI80
SYR85
THA70
CIV90
ECU80
URY80
PNG95
ZMB75
JOR95
JAM95
VEN95
CMR85
MYS85
MDG90
JOR90
IDN95
TGO90
PRY95
THA95
PHL90
MDG70
ECU95
CHL80
SLE90
IND70
VEN80
CIV80
SLV80
ZAR75
IRN85 ZAR90
MMR85
NGA80
HTI90
CMR90
SLE95
NER80
JOR85
NIC75
-10
-5
0
Aid, instrumented values
Non-outliers
Outliers
5
Fit to all data, coef = -0.01, t = -0.07, N = 294
Fit excl. outliers, coef = -0.02, t = -0.20, N = 293
50
Figure 6. Guillaumont and Chauvet Regression 1.2: Partial Scatter of GDP/Capita Growth
versus Aid×Environment
4
Original data
GDP/capita Growth
-2
0
2
GMB82
GMB70
IND82
THA82
TTO70
DOM70
KOR82
PRY70
PAK82
ECU70
GTM82
GHA82
IDN70
MWI82
BOL82
SLV82
SYR82
EGY82
MYS82
DOM82 IDN82
HND82KOR70COG82
BRA70RWA70
KEN82
VEN82
COL82 JAM82
PAK70
PRY82 CYP82
HND70
URY82
MYS70
CRI82
MUS70
SLE70
CHL82
GUY82
MUS82
SLE82
MEX82
ARG82
PHL82
GUY70
PHL70
TGO82
VEN70 RWA82
BRA82
URY70
COL70BOL70
ECU82 TTO82
THA70
CHL70 LKA82
MMR82SLV70
GHA70
NIC82
-4
SEN82
CMR82
JOR82
ZAR82
-15
-10
Non-outliers
Outliers
-5
0
5
Aid*Environment, instrumented values
10
Fit to all data, coef = -0.15, t = -1.79, N = 68
Fit excl. outliers, coef = -0.11, t = -1.96, N = 67
IV. Conclusion
Each of the papers examined here embodies a set of choices about model specification and data.
Aid is measured a certain way. A certain epoch is studied. Periods have a certain length. And so
on. Some of these choices imply certain assumptions about the world, such as, say, that aid is not
endogenous to growth. All limit the scope of a strict interpretation of the results.
To wit, the Burnside and Dollar results can be stated more precisely as follows:
Aid was associated with higher GDP growth in a good policy environment during 1970–93, on
average, in countries and periods where the necessary data was collected, except for outliers
(unless aid2×policy is included to allow for diminishing returns to aid), when aid is defined as
“Effective Development Assistance” as a share of real GDP and polices are defined by inflation,
budget deficit, and the complex Sachs-Warner “openness” variable, controlling for log of initial
real GDP/capita, assassinations per capita, ethno-linguistic fractionalization, the product of
those two, money supply/GDP, and period effects, assuming that no unobserved country-specific
effects simultaneously and substantially influence aid, policies, and growth, and no variables
other than aid aid×policy are endogenous to growth.
51
This is not quite “aid has a positive effect on growth in a good policy environment.”
In fairness, such qualifiers could be tacked on to the conclusion of any study in the crosscountry literature on aid and development, or in econometrics more generally (though perhaps
not always quite so many). Moreover, Burnside and Dollar did test some of their assumptions,
such as the exogeneity of the policy variables. Nevertheless, a question of great scientific and
practical importance remains, and it is how many of such implied qualifiers in studies of aid and
growth can be dropped without harming the conclusions. This study attempts to contribute to answering that question.
The test results reported here suggest that the fragility found in Easterly et al. (2004) for
the case of Burnside and Dollar is common in the cross-country aid effectiveness literature.
In surveying the results, it is tempting to ask which results are robust and which are not.
But the test data are best seen in shades of grey. The results tested here break roughly into five
groups, ranging from weakest to strongest. The weakest group consists of the results on
aid×policy in the Burnside and Dollar, Collier and Dollar, and Collier and Dehn regressions,
which lose significance at 0.05 in all but the weakest tests. In the second division I put the Collier and Dehn result on ∆aid×negative shock, which passes more tests but is quite sensitive to
changes in the control set, as well as to removal of a minority of the negative shocks in the sample. The Collier and Hoeffler result on post-conflict 1×aid×policy (or the collinear postconflict 1×aid), the Hansen and Tarp results on aid and aid2, and Guillaumont and Chauvet result
on aid×environment seem stronger. They generally pass the “whimsy”-based tests at or near
0.05. Most survive the sample-expansion test, but with autocorrelation—and then fail the ARrobust test meant to address this problem. The Guillaumont and Chauvet result could not be put
52
to the sample-expansion tests, so the degree of its robustness is less certain and I add it to this
middle category.
In the fourth and fifth categories are the GMM results of Hansen and Tarp and Dalgaard
et al., respectively. Both fare well under the sample expansion. The Hansen and Tarp GMM results, especially those on aid and lagged aid, generally persist through the test suite, though not
always significantly at 0.05. The only test that completely eliminates the Hansen and Tarp GMM
results is that of defining aid as EDA/real GDP, but this is a misleading measure of aid. As for
the Dalgaard et al. results, they come through powerfully in all the tests but the 12-year aggregation that reduces the sample size to 116.
Does this mean that the statistically weaker stories of aid effectiveness should be dismissed? Are recipient policies, exogenous economic factors, and post-conflict status irrelevant to
aid effectiveness? No. There can be no doubt that aid sometimes finances investment (Hansen
and Tarp, 2001), and that domestic policies, governance, external conditions, and historical circumstances influence the productivity of investment. Why then do such stories of aid effectiveness not shine more clearly through the numbers? The reasons are several. Aid is probably not a
fundamentally decisive factor for development, not as important as, say, domestic savings, inequality, and governance. Moreover, foreign assistance is not homogenous. It consists of everything from in-kind food aid to famine-struck countries and technical advice on building judiciaries to loans for paving roads. And some aid is poorly used. Thus the statistical noise nearly
drowns out the signal.
If there is one strong conclusion from this literature it is that on average aid works well
outside the tropics but not in them. But just as it would be a mistake to conclude that the other
stories of aid effectiveness contain no truth, it would also be mistaken to conclude that this result
53
is the wholly, simply true. Indeed, the Dalgaard et al. result is more of a question than an answer.
Presumably distance from the poles is not a direct determinant of aid effectiveness. Rather, the
causal pathways are complex, and so it cannot be assumed that no kind of aid will work well in
the tropics. Much the same can be said about the more optimistic, but somewhat less robust,
Hansen and Tarp result on the overall positive effect of aid on growth. Even accepting it as true,
it gives little guidance about where aid ought to be sent, and in what forms.
Perhaps further econometric work will disaggregate aid by types of program and recipient
and unearth more robust answers to the fundamental questions of aid policy. Or perhaps researchers have hit the limits of what cross-country empirics can reveal about aid. The search for
truth may need to rely more on the particularistic case study approach. Van de Walle and Johnston (1996), for example, synthesize conclusions from case studies on the use and effects of aid in
seven African countries, each jointly conducted by researchers from donor and recipient countries. Of course, the lessons that emerge from case studies are particular to the country studied.
But they can be generalized. Killick (1998) provides an excellent example by conducting a systematic survey of case studies that feeds into a trenchant analysis of the effects of IMF conditionality. Nevertheless, robust generalizations will not come easily.
54
Appendix. Data set construction
The new data set used in this study is based heavily on that for Easterly et al. (2004). Some variables in that set have been slightly revised. Others have been added to match the data sets of the
tested regressions. The period of coverage has been pushed back to 1958 and extended forward
to 2001 for most variables. All data were collected from standard cross-country sources, expect
for countries’ export price indexes, which were provided by Jan Dehn (see Dehn (2000)). (See
Table A–1.)
Following are notes on the data set construction:
(a)
•
•
•
•
•
(b)
•
•
•
•
Revisions since Easterly et al. (2004)
Some observations for inflation were completed by using wholesale inflation where consumer price inflation was unavailable.
The update of the Sachs-Warner variable was slightly revised under the influence of the
independent update by Wacziarg and Welch (2002). The full update will be described and
published separately.
Some missing values for Effective Development Assistance during 1975–95, the period
of the EDA data set, were filled in in the same manner as missing values outside this period already were, via a regression of EDA on net ODA.
ICRGE now varies over time, rather than taking 1982 values throughout. Observations
before 1982 were assigned 1982 values. In addition, the variable was revised in order to
extend it beyond 1997. In 1998, the PRS Group stopped reporting two of ICRGE’s original components, Expropriation Risk and Repudiation of Government Contracts. So these
were dropped entirely from ICRGE, leaving Corruption, Bureaucratic Quality, and Rule
of Law. On annual data, the revised ICRGE has a 0.97 correlation with the original.
Missing values for ethnolinguistic fractionalization were filled in from Roeder (2001).
Expansion of period
Data was collected for all available years in 1958–2001.
However, the Collier and Dehn shocks variables were only updated to 1997 because the
underlying data on export prices from Dehn (2000) cease in 1997.
The Guillaumont and Chauvet environment variable was not updated at all, for lack of
underlying data on its four components.
The 1998–2001 values for the updated Sachs-Warner variable are based on 1998 data
only. Currency Data International, the long-time source of black market premium data,
which is one component of Sachs-Warner, shut down in 1999.
Table A–1. Construction of data set
Variable
Per-capita GDP
growth
Initial GDP per
capita
Code
GDPG
Data source
World Bank, 2003
Notes1
LGDP
Summers and Heston,
1991, updated using
GDPG
Natural logarithm of
GDP/capita for first year of
period; constant 1985 dol-
55
Ethno-linguistic
fractionalization,
1960
Assassinations/
capita
Political instability, lagged
Institutional quality
ETHNF
Roeder, 2001
ASSAS
Banks, 2002
PINSTAB–1
Banks, 2002
ICRGE
PRS Group’s IRIS III
data set (see Knack
and Keefer, 1995)
M2/GDP, lagged
one period
Sub-Saharan Africa
East Asia
M2–1
World Bank, 2003
SSA
World Bank, 2003
Budget surplus
BB
World Bank, 2003;
IMF, 2003
Inflation
INFL
World Bank, 2003;
IMF, 2003
Sachs-Warner,
updated
SACW
Positive (and
negative) shock
POSSHOCK
NEGSHOCK
Sachs and Warner,
1995; Easterly et al.,
2004; Wacziarg and
Welch, 2002
Dehn, 2000
Positive (and
negative)
shock/GDP
POSSHOCKGDP
NEGSHOCKGDP
EASIA
lars
Probability that two individuals will belong to different ethnic groups
Assassinations/capita
Simple average of ASSAS
and revolutions/year
Revised version of variable. Computed as the average of the three components still reported after
1997.
Codes nations in the southern Sahara as sub-Saharan
Dummy for China, Indonesia, South Korea, Malaysia,
Philippines, and Thailand,
following Burnside and
Dollar
World Bank primary data
source. Additional values
extrapolated from IMF,
using series 80 and 99b
(local-currency budget surplus and GDP)
Natural logarithm of 1 +
inflation rate. World Bank
primary data source.
Wholesale price inflation
from IMF used where consumer price data unavailable
Extended to 1998. Slightly
revised pre-1993. Full description will be published
separately
Shocks are % price index
changes. “Shock” threshold
country-specific. Reconstructed based on underlying index data for 1957–97
Shocks are shares of GDP,
computed using 1990 data
on commodity share of exports and exports share of
56
Positive (and
negative) shock,
pooled basis
Positive (and
negative)
shock/GDP,
pooled basis
Effective Development Assistance/ real GDP
GDP from Dehn 2000.
“Shock” threshold countryspecific
Shocks are % price
changes. “Shock” threshold
universal
Shocks are shares of GDP.
“Shock” threshold universal
POSSHOCKPOOLED
NEGSHOCKPOOLED
POSSHOCKGDPPOOLED
NEGSHOCKGDPPOOLED
AID
Chang et al., 1998;
DAC, 2002; IMF,
2003; World Bank,
2003; Summer and
Heston, 1991
Net Overseas Development Assistance/real GDP
ODAPPPGDP
Net Overseas Development Assistance/nominal
GDP
Dummy for end
of civil conflict in
previous period
ODAXRGDP
DAC, 2002; IMF,
2003; World Bank,
2003; Summer and
Heston, 1991
DAC, 2002; World
Bank, 2003
POSTCONFLICT1
Available values for 1975–
95 from Chang et al. Missing values extrapolated
based on regression of
EDA on Net ODA. Converted to 1985 dollars with
World Import Unit Value
index from IMF, series 75.
GDP computed like LGDP
above
Like AID exception using
ODA from DAC
.
Collier and Hoeffler,
2002
Tropical area
TROPICAR
Gallup and Sachs,
fraction
1999
Population
LPOP
World Bank, 2003
Population
POPG
World Bank, 2003
growth
Mean years of
SYR
Barro and Lee, 2000
secondary schooling among those
over 25
Arms imARMS-1
U.S. Department of
ports/total imState, various years
ports lagged
1
All variables aggregated over time using arithmetic averages.
Natural logarithm
57
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