1. Introduction
The World Bank considers ‘corruption a major challenge to its twin goals of ending extreme poverty by 2030 and boosting shared prosperity for the poorest 40 percent of people in developing countries’.Footnote 1 This characterization is consistent with the scholarly consensus that corruption is detrimental to economic growth (e.g. Bologna Pavlik, Reference Bologna Pavlik2018; Fisman and Svensson, Reference Fisman and Svensson2007; Mauro, Reference Mauro1995; Mo, Reference Mo2001; Pellegrini and Gerlagh, Reference Pellegrini and Gerlagh2004).Footnote 2 It would be encouraging if foreign aid policies helped to reduce corruption levels in developing countries. Alternatively, it would be troubling if those same policies promoted corruption.
There are plausible reasons to suspect a causal link between aid and recipients' corruption levels. Beginning in the 1990s, the development community emphasized channeling aid to countries that evidenced increased governance quality. More recently, there has also been an emphasis placed on ‘outcome-based conditionality’ whereby aid is disbursed when predetermined performance benchmarks for governance are met (World Bank Group, 2017: 266–277). This would be consistent with observed corruption levels causing aid allocations.
Conversely, aid might cause either decreases or increases in corruption. On the one hand, a government might wish to rein in corruption but is revenue-constrained from effectively doing so. Aid can be put toward rooting out corruption and/or providing government agents with higher pay to offset incentives toward corrupt behavior (Knack, Reference Knack2001; Van Rijckeghem and Weder, Reference Van Rijckeghem and Weder2001). On the other hand, aid can represent a flow of rents for government agents and special interests to compete for. This competition increases incentives toward corrupt behavior (Djankov et al., Reference Djankov, Montalvo and Reynal-Querol2008; Svensson, Reference Svensson2000).
When considering the relationships between aid and corruption, both the sign and direction of the effects are ambiguous. Evaluation of the relationships, then, becomes an empirical matter. Several studies have addressed it with mixed results. Both Svensson (Reference Svensson2000) and Alesina and Weder (Reference Alesina and Weder2002) fail to find evidence that less corrupt governments receive more aid.Footnote 3 Both studies report some suggestive evidence that aid might actually cause higher levels of corruption. Based on an instrumental variable (IV) identification strategy, Knack (Reference Knack2001) finds support for this suggestion. Alternatively, Tavares (Reference Tavares2003) employs a different IV strategy and reports that aid leads to lower corruption levels.Footnote 4 However, Coviello and Islam (Reference Coviello and Islam2006) find that either result disappears once country fixed effects are included in the estimations.Footnote 5
The existing empirical studies leave us with a murky picture. Simultaneity obviously looms large. Furthermore, linear regression models assume that the marginal effect of aid is constant or a continuous function of the aid level.Footnote 6 This may be inappropriate if, for example, there are economies of scale in a government's anti-corruption efforts; or if increases in aid must be large enough to trigger rent-seeking games that corrupt.
Related to the latter concern, existing studies of the aid–corruption nexus do not account for whether changes in aid are sustained. This is important in evaluating, specifically, a causal effect of aid on corruption. Recipient country aid flows are highly volatile through time. Numerous studies argue that this volatility decreases aid's effectiveness and has deleterious macroeconomic consequences for recipients (e.g. Arellano et al., Reference Arellano, Bulr, Lane and Lipschitz2009; Bulir and Hamann, Reference Bulir and Hamann2008; Celasun et al., Reference Celasun, Walliser, Tavares and Guiso2008; Hudson, Reference Hudson2015; Hudson and Mosely, Reference Hudson and Mosely2008a, Reference Hudson and Mosely2008b). An important contribution of our paper is that we consider three different types of aid ‘treatments’: (a) sustained increases in aid, (b) large increases, and (c) increases that are both large and sustained. (See section 3 for more details.)
We attempt to address the above-mentioned concerns and sort out the aid–corruption nexus. We do so by following Hausmann et al. (Reference Hausmann, Pritchett and Rodrik2005) and Grier and Grier (Reference Grier and Grier2020) in employing matching methods. Matching methods are non-parametric and allow us to (1) define a treatment in terms of a specific type of change in aid flows or corruption, (2) identify countries that received a treatment, and (3) construct a plausible counterfactual for each treated country against which we can compare subsequent changes in corruption or aid. The counterfactuals are constructed based on a set of covariates that plausibly determine the probability of receiving the treatment and/or are otherwise correlated with the outcome. Importantly, then, the counterfactuals are countries that were similarly likely to have received the treatment but did not. This creates a set of quasi-experiments with which to assess the aid–corruption nexus.
Matching methods can help to mitigate some endogeneity concerns. Regarding simultaneity, we are able to define treatments in terms of either aid or corruption, and then construct relevant counterfactuals for each set of treatments. Therefore, the episodes used to identify an aid–growth effect are distinct from the episodes used to identify a corruption–aid effect. However, there remain concerns about relevant unobservables that are not taken into account during matching.Footnote 7 As such, we focus our analyses on post-treatment changes in aid or corruption. Similar to panel data models that include country fixed effects, focusing on changes in the outcome serves to difference-out time-invariant heterogeneity that may bias the results (An and Winship, Reference An and Winship2017; Grier and Grier, Reference Grier and Grier2020). However, unlike panel data models, matching does not rely on extrapolation to estimate a treatment effect.
We do not report compelling evidence of an effect of corruption on aid flows. Furthermore, any results that are suggestive tend to imply that corruption reforms lead countries to receive less aid. Alternatively, we generally find that, over a 10-year horizon, a sustained increase in aid leads to more corruption in a recipient country. Importantly, the extent to which an increase in aid is sustained seems to be important to this effect (whereas we generally do not report significant results for large changes in aid that are not sustained over time).
Although we focus on the aid–corruption nexus specifically, our paper fits into two broader literatures. First, there are a large number of studies that explore the relationship between foreign aid and institutional/governance quality generally. For example, Bräutigam and Knack (Reference Bräutigam and Knack2004), Rajan and Subramanian (Reference Rajan and Subramanian2007), and Busse and Gröning (Reference Busse and Gröning2009) report a negative relationship between aid and governance quality in recipient countries. Djankov et al. (Reference Djankov, Montalvo and Reynal-Querol2008) report that aid harms recipient political institutions and Kalyvitis and Vlachaki (Reference Kalyvitis and Vlachaki2012) find democratic reforms to be less likely where aid is being received. Alternatively, Knack (Reference Knack2004) fails to find a significant impact and Jones and Tarp (Reference Jones and Tarp2016) report a small positive effect on political institutions. Heckelman and Knack (Reference Heckelman and Knack2008) report that aid makes economic reforms less likely (although in a later paper – Heckelman and Knack (Reference Heckelman and Knack2009) – they report no significant effect of aid on economic institutions). Young and Sheehan (Reference Young and Sheehan2014) find that aid negatively affects both political and economic institutions.
Second, there are also several studies that explore the determinants of foreign aid. Several of these report that donors' strategic concerns are important. Alesina and Dollar (Reference Alesina and Dollar2000) report that income per capita and the size of an economy are positively linked to the size of its aid flows, but so are institutional/policy variables such as trade openness and democracy. Alternatively, Burnside and Dollar (Reference Burnside and Dollar2004) and Alesina and Weder (Reference Alesina and Weder2002) find no evidence that institutional/policy variables matter for aid flows. Particularly relevant to the current paper, Brück and Xu (Reference Brück and Xu2012) study sudden jumps in aid flows and report that they are predicted by regime changes and wars.
We proceed as follows. In section 2 we discuss the matching methods. The data are then discussed in section 3. Results of our analysis are reported in section 4. Section 5 concludes with a summarization of our findings and implications for future research.
2. Matching methods
We aim to identify effects running from aid to corruption and/or corruption to aid. Identification is challenging for at least three reasons. First, countries that receive aid are not randomly selected; and determinants of how much aid they receive may be correlated with corruption levels. Second, although a country's level of corruption may cause it to receive more or less aid, it is also plausible that the amount of aid it receives helps to determine its level of corruption. Third, there may be other unobservables that are correlated with both aid and corruption. Thus, there are concerns that estimates will contain biases associated with selection, simultaneity, and/or omitted variables.
Due to these concerns, standard regression analysis is unlikely to sort out the different causal effects at play. As an alternative, we employ matching methods. Take the case of a potential causal effect of aid on corruption. We identify episodes where countries experienced sustained and/or large increases in aid. Those episodes are the ‘treatments’. For each of those cases, we create a counterfactual based on a country or countries (‘matches’) that are as similar as possible to the treated country along a chosen set of characteristics. Those characteristics are chosen to be relevant to both the outcome of interest (corruption) and the likelihood of a country receiving the treatment.
Matching methods were developed to mitigate concerns for selection bias (Rosenbaum and Rubin, Reference Rosenbaum and Rubin1983). For each treated country, the matches are chosen such that the counterfactual was similarly likely to have received the treatment (but did not). The post-treatment effect is a treated country's subsequent change in corruption or aid relative to the counterfactual. Because we focus on post-treatment changes in corruption or aid, we are also differencing out time-invariant heterogeneity. Similar to the inclusion of country fixed effects in a panel regression, this differencing mitigates concerns about omitted variable bias.Footnote 8
We employ two different matching methods: propensity score matching (PSM) and Mahalanobis distance matching (MDM). For PSM, we begin with a logit model of the probability of treatment conditional on a set of covariates. Having estimated the model, each country is assigned a propensity score (i.e. the estimated probability of having received treatment). Each treated country is then matched to one or more non-treated countries with similar propensity scores. Here, we will refer to a treated country's ‘neighbors’ in terms of how close their propensity scores are. We report results for matching using the nearest neighbor criterion where k = 1, 2, 3, and 4. An alternative to using a logit model is to match based on the covariates directly. A concern with PSM is that although it matches appropriately on propensity scores, it may ignore variation in the covariates if this information is not contained in the propensity score (King and Nielson, Reference King and Nielsen2019). Matching based on covariates directly addresses this issue. We do this using the Mahalanobis distance metric. For two countries, this is essentially a scale-invariant and variance-adjusted Euclidean distance between their covariate vectors. Similar to PSM, we report Mahalanobis results using nearest neighbor criteria (k = 1, 2, 3, or 4).
For both PSM and Mahalanobis, we calculate and report the average treatment effect on the treated (ATET). This is the average difference in the change of our outcome variable for our treated countries relative to the countries' they matched with. To gage the statistical significance of this comparison, we use bootstrapping to compute standard errors for PSM and bias-corrected standard errors for Mahalanobis (Abadie and Imbens, Reference Abadie and Imbens2011).
3. Data
Our discussion of data will be organized into three categories: treatments, outcomes, and covariates. We consider both changes in aid flows and changes in corruption indices as treatments; then we relate them, respectively, to subsequent changes in corruption and aid, over both 5-year and 10-year horizons. Counterfactuals are created for each case of treatment by matching based on the covariates.
Treatments: corruption reforms and increases in aid
We are considering corruption and foreign aid data from 1996 through 2013. Our corruption measure is the Control of Corruption (COFC) indicator from the Worldwide Governance Indicators out of the World Bank (Kaufmann et al., Reference Kaufmann, Kraay and Mastruzzi2010). The COFC reflects the perception that public power is being used for rent-seeking. Countries receive values on a scale of −2.5 (indicating very little control over corruption) to 2.5 (indicating that corruption is well-controlled). Note that a higher value of this indicator implies less perceived corruption.Footnote 9
Data on foreign aid are drawn from the AidData database (v. 3.1 described in Tierney et al., Reference Tierney, Nielson, Hawkins, Roberts, Findley, Powers, Parks, Wilson and Hicks2011; http://aiddata.org). AidData takes an appropriately broad view of aid as all ‘development finance’, including loans and grants from governments and their official aid agencies; also inter-governmental organizations. This both expands and circumscribes conventional aid measures. In terms of expanding, AidData includes international loans made at benchmark market interest rates; furthermore, it includes aid from multilateral development banks (e.g. the World Bank) that have traditionally been excluded from official project databases. Alternatively, AidData excludes both bilateral and multilateral military assistance. Since developed and published, this database has become the basis for numerous studies.Footnote 10 AidData allows us to consider not only overall official development assistance (ODA; grants and concessional loans) but also ‘economic’ and ‘governance’ (as well as the residual ‘other’) aid separately. Economic aid is aimed at the production sectors of a recipient's economy. Alternatively, governance aid is aimed at strengthening the public sector and its plans/policies, developing civil society, and preventing conflict and human rights abuses. (See Jones and Tarp (Reference Jones and Tarp2016, Appendix C) for more details.) Both bilateral and multilateral aid flows are included in these measures. Aid flows are nominal and divided by a recipient's nominal GDP.
Using the COFC indicator, we define treatments in a similar fashion to Bologna Pavlik et al. (Reference Bologna Pavlik, Grier and Grier2020).Footnote 11 In particular, we identify large and sustained increases in the corruption index. (Since a higher value of the COFC indicator corresponds to less corruption, we henceforth refer to corruption reforms.) There are two parts to defining treatments as such. First, we consider a large corruption reform to be a ⩾0.20 (about one standard deviation) increase in the indicator value. Second, we consider the reform to be sustained if, 5 years later, the value has fallen by no more than 0.05 (one-quarter of the initial increase). Intuitively, the corruption reform is sustained if at least 75% of it (as measured by the indicator) remains 5 years later.Footnote 12
Defining treatments in terms of aid flows is a bit trickier. ODA series are highly volatile; in particular, we observe many large increases in aid followed in the next year by large drops. The tendency for aid flows to change dramatically from year to year makes determining what constitutes a meaningful treatment difficult. An important contribution of our paper – which is possible given matching methods – is to define three different sets of treatments.
First, we identify what (1) sustained increases in aid. These are increases that are followed by 5 successive years where aid remained higher than the level preceding the initial increase. (E.g. if the level of aid was 1 in 1979 and then increased to 2 in 1980, then we consider that increase a treatment if aid in 1981, 1982, 1983, 1984, and 1985 remained >1.) Second, we identify (2) large increases in aid. We take the distribution of aid flow changes (which are around a mean near zero) and use a standard deviation (about 6 for overall ODA) to define large.Footnote 13 Third, we identify (3) large sustained increases. These satisfy both of the previous two criteria. Given the volatility of aid series and the associated difficulty in determining which sort of an increase in foreign aid might matter for corruption, having these three different treatment sets – and being able to compare the post-treatment estimates across them – is an important contribution of this paper.
In Appendix Tables A1 and A2, we report the treatment (country, year, and size) for corruption reforms and the three different treatment sets for aid flows.Footnote 14
Outcomes: post-treatment changes in corruption or aid
For corruption reforms, we aim to determine whether these cause post-treatment increases or decreases in aid flows. Conversely, for aid treatments, we aim to determine whether they cause post-treatment changes in corruption levels.
For the corruption outcomes, we use the same COFC indicator. We estimate average treatment effects over the treated (ATETs) over both the 5-year and 10-year horizons. Considering a treatment occurring in year T, these are based simply on subsequent changes in the outcome variables from T to T + 5; and then T to T + 10. The only other important thing to reiterate is that higher values of the COFC indicator correspond to less corruption.
We also estimate ATETs over 5-year and 10-year horizons for aid in response to corruption reform treatments. However, the high volatility of the aid series again complicates things. When looking at a change over a particular time period (say, T to T + 5), the value can be radically different than changing the time period slightly (say, ending it in T + 4 or T + 6 instead). To mitigate this problem, we use 2-year moving averages in calculating the post-treatment changes in aid. (We also check on how critical this choice is by re-running some estimations based on 3-year moving averages instead.)
Summary statistics for aid flows (as GDP shares) and the COFC indicator are reported in Tables 1 and 2. In addition to statistics based on annual data, those based on the 5-year and 10-year changes are also reported.
Summary statistics for ODA variables
Summary statistics for corruption variables: 1996–2018
Covariates
When employing matching methods, the aim is to choose covariates that correlate with the outcome of interest and/or determine the likelihood of receiving the treatment. Taking into account variables that correlate with the outcome is standard to any empirical analysis. Accounting for determinants of treatment probability, however, is distinct and fundamental to matching methods. For any estimation, we want to match each treated country to a country (or countries) that were similarly likely to have received the treatment. This makes the matches effective counterfactuals against which to determine whether observed changes in the treated countries' outcomes are being caused by the treatments.
Since we are estimating, separately, both the effects of corruption on aid and the effects of aid on corruption, we need separate covariate sets for (1) matching countries treated with corruption reforms and (2) matching countries treated with aid increases. In both cases, it is important to note that we are matching on pre-treatment levels of our outcome. In addition to looking at changes as our outcome of interest, effectively differencing out time invariant unobservables, matching on pre-treatment levels allows us to focus on countries with the same initial value.
We first take the case of (1): matching countries treated with corruption reforms. For covariates, we first draw on Alesina and Dollar (Reference Alesina and Dollar2000) and Alesina and Weder (Reference Alesina and Weder2002). We include GDP per capita (logged; real, PPP-adjusted 2011 dollars) and GDP per capita squared; population (logged) and population squared; the trade share of GDP, the polity2 index of autocracy-democracy, and years that a country spent as a colony. GDP, population, and trade data are from the World Bank's World Development Indicators (WDI). The polity2 index is from the Polity5 project out of the Center for Systemic Peace (Marshall and Gurr, Reference Marshall and Gurr2020). The years-as-a-colony variable is taken from Alesina and Dollar's (Reference Alesina and Dollar2000) data. All of these variables are lagged 5 years (relative to the treatment date). Additionally, we include lagged corruption and lagged aid (levels) as covariates. (Including levels of treatment and outcome variables as covariates is standard.)
For the case of (2) – matching countries treated with aid increases – the set of covariates again contains log real GDP per capita and the trade share of GDP. Additional covariates are the urban population share, life expectancy, and oil rents as a percent of GDP. All of these variables are again from the World Bank's WDI. Levels of both corruption and aid are also included as covariates. Again, due to the volatility of aid, instead of lagged values from a single year, all of these covariates are included as 5-year averages, where the last year included is the year prior to treatment. Predicting jumps in aid is difficult. It is unclear when or how the events occurring in any given year after subsequent aid shares. Using averaged covariates has the additional benefit of incorporating the observations that may have a single year of data missing.
Appendix Tables A3 and A4 report summary statistics for all of the covariates described above.Footnote 15 In Appendix C, we report evidence of covariate balance for all treatment definitions, for the PSM and Mahalanobis k = 4 specifications for both 5- and 10-year horizons.Footnote 16 In Appendix Figures C1 through C8, we also report the pre-post matching histograms of propensity scores for our treated and control groups showing the significant overlap after matching. For both PSM and Mahalanobis, we report the difference in means between (1) the treated countries and their potential matches for the entire sample (raw data) and (2) the analogous difference after matching. The difference in means falls substantially following both PSM and Mahalanobis matching. Furthermore, we are able to calculate and report Chi-squared tests for the PSM estimations. The null hypothesis of this test is that the covariates are balanced on average between the treated countries and their matches. With p-values near 1.0, we fail to reject the null, giving us confidence in our estimates.
4. Results
This section reports our estimates of corruption reform treatments on aid flows; conversely, it also reports our estimates of aid treatments on (the control of) corruption. In both cases, estimates are reported over both 5-year and 10-year post-treatment horizons.
Before reporting those estimates, we examine simple difference-in-means and ordinary-least squares (OLS) panel regression results to suggest the importance of a plausible identification strategy.Footnote 17 To conserve space, these are reported in Appendix B. Table B1 reports differences in the means between corruption reform-treated countries and their matches for both 5-year and 10-year changes in aid. Table B2 reports the same for aid-treated countries, with a separate panel for each of the three treatment definitions. Corruption reform-treated countries tend to have, on average, lower aid 5-years out but higher aid 10-years out. However, the differences in means are not statistically significant. Turning attention to the aid-treated countries, all of the mean differences are negative, implying that more aid leads to more corruption. However, they are only statistically significant for sustained – including large and sustained – aid increases and for the 5-year horizon. (The 10-year differences in means are never significant.)
Next, the OLS panel regressions are reported in Appendix Tables B3 and B4. The regressions include the variables described in the ‘Covariates’ section above along with country and year fixed effects. Across all of the regressions, the point estimates are negative. Corruption reforms are associated with less aid; increases in aid are associated with more corruption. However, the corruption treatments never enter significantly and sustained aid treatments only enter significantly for 10-year corruption changes while large and sustained aid treatments only do so for 5-year changes. (Large aid treatments never enter significantly.)
The difference-in-means and panel regression results reported above illustrate how important a compelling identification strategy is to sorting out the aid–corruption nexus. The point estimates are generally consistent with ‘bad’ linkages between the two variables. The estimates are often imprecise and determining which direction(s) they run is unclear. Rather than (as in the case of the panel regressions) rely generally on the variation in treated versus untreated countries, with matching methods we are able to construct plausible counterfactuals for each treated country. By emphasizing only countries that are similar to a treated unit in terms of their covariates, we ultimately discount other countries in the sample that are poor comparisons and likely to confound inference. Matching methods also have the advantage of estimating the simple average treatment effect, as opposed to a weighted average resulting from a panel regression that can include negative weights resulting in a bias.
Effects of corruption reforms on aid
Our prior is that, all else equal, when a country experiences a corruption reform (i.e. in this context, a large, sustained increase in its COFC indicator value) this will cause it to receive increased aid flows (or, at worst, there will be no effect). The results reported here are not generally supportive of that prior. The estimated ATETs over the 5-year horizon are reported in Table 3 and those over the 10-year horizon are reported in Table 4. The estimated effects are on post-treatment changes in ODA (or a component of it) as a share of GDP.
Effect of sustained corruption reforms on 5-year changes in ODA shares
Notes: *, **, and *** indicate statistical significance at the 10, 5, and 1% levels, respectively. P-values given in brackets. Baseline covariates include lagged corruption levels, ODA shares, (log) GDP per-capita and its square, (log) population and its square, trade GDP share, polity score, (log plus 1) number of years as a colony after 1900. Each specification has 39 treatments and 747 potential control (untreated) country/year observations.
Effect of sustained corruption reforms on 10-year changes in ODA shares
Notes: *, **, and *** indicate statistical significance at the 10, 5, and 1% levels, respectively. P-values given in brackets. Baseline covariates include lagged corruption levels, ODA shares, (log) GDP per-capita and its square, (log) population and its square, trade GDP share, polity score, (log plus 1) number of years as a colony after 1900. Each specification has 18 treatments and 267 potential control (untreated) country/year observations.
Considering the 5-year horizon, there are statistically significant effects based on Mahalanobis matching, and they are all negative. In particular, they are uniformly negative and significant for overall ODA and for the ‘other’ (i.e. neither government- nor economic-specific) component. Considering the 10-year horizon, all of the statistically significant effects for overall ODA disappear. The only statistically significant estimates are for the government- and economic-specific aid shares and both are positive. Those estimates are again based on Mahalanobis matching; but they are, in each case, only significant for a single specification of neighbors (the former is only significant for k = 2; the latter only for k = 1).
To summarize the results for corruption reform on aid flows, there is some evidence of an effect over the 5-year horizon when using Mahalanobis-based matching. However, whenever the results are statistically significant for overall ODA, the point estimates are negative. A negative corruption reform–aid effect is troubling. It implies that when a country experiences a sustained corruption reform, this causes donors to provide it with less aid. If the identification strategy is valid, negative estimates cannot be accounted for by poor countries receiving more aid; nor by aid creating rent-seeking opportunities that lead to more corruption. Income levels and corruption levels are both covariates in the analysis. Rather, negative estimates suggest that donors are more likely to give aid to countries for being more corrupt per se.
The above being said, we reemphasize that the corruption reform–aid results are not particularly robust. For overall aid, there are no statistically significant estimates when considering the 10-year horizon. Furthermore, the two cases where significant results are reported for specific aid components – which are for the 10-year horizon – indicate a positive effect of corruption reform on aid. The empirical picture remains murky. There is no compelling evidence to suggest that countries undertaking meaningful and sustained corruption reforms are rewarded with more aid. However, although the 5-year results are based on 39 treatments the 10-year results are based on only 18. As such, the ‘murkiness’ regarding the longer horizon may possibly be due to the limited number of treatments available.
Effects of aid on corruption
When considering aid flows as the causal factor, we are considering three different treatment sets: (1) sustained increases, (2) large increases, and (3) large sustained increases. We report results based on (1), (2), and (3) in that order. All statistically significant results that follow have negative signs. The COFC indicator takes higher values for less corruption, so negative effects imply aid causing greater levels of corruption.
Estimated ATETs for (1) sustained increases in ODA are reported in Table 5 (5-year horizon) and Table 6 (10-year horizon). There is only one statistically significant 5-year estimate (for the ‘other’ component; Mahalanobis, k = 1). Alternatively, most of the 10-year estimates for overall ODA are statistically significant and negative. In particular, three out of four PSM estimates are statistically significant, as are three out of four Mahalanobis estimates. Furthermore, for the two estimates that are not statistically significant (PSM, k = 4; Mahalanobis, k = 3), the p-values are very close to the 10% cutoff (0.120 and 0.105, respectively).Footnote 18 There is compelling evidence that sustained increases in aid cause increased corruption in recipient countries.
Effect of sustained increases in ODA on 5-year changes in corruption
Notes: *, **, and *** indicate statistical significance at the 10, 5, and 1% levels, respectively. P-values given in brackets. Baseline covariates include lagged ODA shares, corrupt levels, GDP per-capita, trade GDP share, urban population share, life expectancy, and oil GDP share. The number of treatments for total aid, government aid, economic aid, and other aid correspond to 210, 244, 191, and 199 treatments, respectively. Each specification has 2,239 potential observations.
Effect of sustained increase in ODA on 10-year changes in corruption
Notes: *, **, and *** indicate statistical significance at the 10, 5, and 1% levels, respectively. P-values given in brackets. Baseline covariates include lagged ODA shares, corrupt levels, GDP per-capita, trade GDP share, urban population share, life expectancy, and oil GDP share. The number of treatments for total aid, government aid, economic aid, and other aid correspond to 210, 244, 191, and 199 treatments, respectively. Each specification has 1,620 potential observations.
Referring to Table 6 again, although overall ODA increases are associated with increased corruption, there is no evidence that either the government-specific or economic-specific component of aid is driving the result. Indeed, although the estimated effects for the ‘other’ (residual) aid component are not statistically significant, the p-value for each of those estimates is considerably lower than those for the corresponding government- and economic-specific estimates. The average ‘Other Aid Share’ of GDP in our sample is about 3.9% versus only 0.7 and 1.3%, respectively, for the government- and economic-specific shares. Per the classification of Jones and Tarp (Reference Jones and Tarp2016), most of ODA is neither government- nor economic-specific. As such, the absence of significant effects associated with those specific components is not particularly surprising.
Turning to treatments of (2) large increases in ODA, we note that we have to rely on a considerably smaller number of treatments with (between 42 and 117 rather than between 189 and 244 with set (1)). Notwithstanding, considering the 5-year horizon (Table 7) three of the four Mahalanobis-based estimates for overall ODA are statistically significant and negative. None of the PSM-based estimates for overall ODA are significant, although they are all negative. However, all the PSM-based estimates for government-specific aid are positive and significant. Together these would be consistent with increases in overall aid leading to higher corruption, but aid targeted toward building state capacity and strengthening civil society tend to mitigate it. Note that government-specific aid, again per the Jones and Tarp (Reference Jones and Tarp2016) classification, is a very small part of total aid (less than 12%; see Table 1).
Effect of large increases in ODA on 5-year changes in corruption
Notes: *, **, and *** indicate statistical significance at the 10, 5, and 1% levels, respectively. P-values given in brackets. Baseline covariates include lagged ODA shares, corrupt levels, GDP per-capita, trade GDP share, urban population share, life expectancy, and oil GDP share. Each treatment represents a large (approximately equal to a mean change plus 1 standard deviation) jump in ODA shares. This corresponds to a jump of 6, 1, 3, and 4 for total aid, government aid, economic aid, and other aid corresponding to 90, 81, 67, and 117 treatments, respectively. Each specification has 2,239 potential observations.
Alternatively, none of the 10-year estimated effects are statistically significant (Table 8). The point estimates for overall ODA effects are all negative, but their p-values are generally large. At least over the longer-run horizon, the evidence for aid treatments defined by the large size of the increase is not compelling. Taken with the results reported in Table 6, this seems to suggest that the sustained nature of an aid increase is more important than its size in regard to an effect on corruption.
Effect of large increases in ODA on 10-year changes in corruption
Notes: *, **, and *** indicate statistical significance at the 10, 5, and 1% levels, respectively. P-values given in brackets. Baseline covariates include lagged ODA shares, corrupt levels, GDP per-capita, trade GDP share, urban population share, life expectancy, and oil GDP share. Each treatment represents a large (approximately equal to a mean change plus 1 standard deviation) jump in ODA shares. This corresponds to a jump of 6, 1, 3, and 4% for total aid, government aid, economic aid, and other aid corresponding to 69, 54, 42, and 95 treatments, respectively. Each specification has 1,620 potential observations.
This brings us to our third set of treatments: (3) large sustained increases in ODA. Unsurprisingly, this set – combining both the sustained and large characteristics of (1) and (2) – is quite limited and all estimations are based on only between 19 and 34 treatments. To again conserve on space, the results are reported in Appendix Tables H1 (5-year) and H2 (10-year). Similar to the 5-year results based on (2), the Mahalanobis-based estimates for overall ODA are all statistically significant and negative. The same is true of three out of four Mahalanobis-based estimates for the 10-year horizon. (There is a single 10-year PSM-based estimate for government-specific aid (k = 1) that is positive and significant.)
To summarize, aid is a very volatile series, so considering ‘sustained’ versus ‘large’ dimensions when defining treatments is important. Although sustained increases in ODA appear to cause increases in corruption, large increases, per se, do not. When we look at sustained and large increases, we are very limited in terms of treatments but the Mahalanobis-based estimates still strongly support a positive ODA-to-corruption link. Our results suggest that sustained increases in aid appear to have a corrupting effect on their recipients.
5. Conclusions
Foreign aid is perceived by many policymakers and scholars as a crucial tool for alleviating poverty in the developing world. However, for others aid is viewed as ineffective or, worse, deleterious to recipient institutions (e.g. Easterly, Reference Easterly2007; Williamson, Reference Williamson2010). Nobel Laureate Angus Deaton (Reference Deaton2013), based on a broad overview of extant research, concludes that aid is ineffective for promoting development, and particularly so in countries with weak institutions. Understanding the relationships between aid, institutional quality, and development outcomes is of clear importance.
Of course, the aid–corruption nexus is an important part of the story. The extant literature is mixed. Some studies find that corruption influences aid allocations; others find that aid flows affect recipient corruption. In terms of the latter, the effect of aid on corruption might be either negative or positive. Given that theory can cut either way, we are left with an empirical question.
We have attempted to sort out the aid–corruption nexus by employing matching methods. These allow us to identify meaningful changes in a country's corruption level or aid flows and then construct a compelling counterfactual against which to compare subsequent changes in the other variable. We have provided estimates of the effect of corruption reforms on subsequent changes in aid flows; also of aid increases on subsequent changes in corruption.
Regarding the latter, we have explored three different definitions of aid treatments. In itself, this is an important contribution. Country-level aid flows are volatile. Determining what would be a ‘meaningful’ change in aid – that can be related to subsequent changes in corruption – is not trivial. We have defined aid ‘treatments’ in terms of whether an increase in aid is (1) sustained, (2) large, or (3) both sustained and large.
We have reported no compelling evidence that a recipient's corruption reforms cause it to receive more aid. Alternatively, sustained increases in aid appear linked to changes in corruption. Unfortunately, the evidence suggests that increases in aid cause more corruption. The aid–corruption nexus appears to be an unfortunate one.
Our study is not the final word on this matter. Given that the literature has lagged behind the ‘credibility revolution’ in empirical research (Angrist and Pischke, Reference Angirst and Pischke2010), we hope that our study points the way forward to refinements and related avenues for research. Future research may build directly on our application of matching methods; alternatively, it might employ compelling new approaches to identification via IVs (e.g. Dreher and Langlotz, Reference Dreher and Langlotz2020); and there are undoubtedly other approaches to be considered.
Acknowledgements
We thank the seminar participants at the TTU Free Market Institute's Research Workshop for helpful comments and suggestions. We are especially thankful to Kevin Grier for valuable feedback. The comments of two anonymous referees are also greatly appreciated.
