CIAO DATE: 04/01

Reevaluating the "Catalytic" Effect of IMF Programs

Martin S. Edwards

2000

Center for Global Security and Democracy
Rutgers University

 

Abstract

While it is generally thought that Fund programs serve as a 'good housekeeping seal of approval' the empirical evidence suggests that Fund programs do not attract added inflows of so-called 'catalytic' finance. The existing work on this subject, however, suffers from two important limitations. These works assume that all programs are successfully completed, and they fail to address the effects of self-selection into IMF programs. Given these shortcomings, it is not surprising that the findings on catalytic finance have heretofore been unimpressive.

This paper addresses both problems. I find, using a sample of IMF agreements signed by 106 states between 1979 and 1995, that selection bias is not a threat to inference. Failure to control for the degree of program compliance, however, is a major problem. Using multiplicative specifications, I find that states are not rewarded for good past performance under their Fund programs. Flows of FDI and loans decrease substantially when a state is under a Fund program and experienced a compliance problem leading to the suspension of the agreement. Thus, after addressing the inferential problems of previous studies, we find no evidence that the Fund serves as a 'seal of approval' to foreign investors and lenders.

 

"Apart from its financial value, this accord is a passport allowing Romania to return to the international markets."

-Romanian Prime Minister Radu Vasile, August 9, 1999

 

The International Financial Institutions (IFIs) have been at the center of public debate in recent years. In the policy community, concern for the effects of International Monetary Fund (hereafter IMF) policies on developing countries has always been an area of interest, regardless of political persuasion. On the right, the concern has been with the unintended consequences of Fund programs—basically the existence of moral hazard (Calomiris and Meltzer 1999; International Financial Institutions Advisory Commission 2000). On the left, the debate over the Fund turns on the distributional consequences of Fund programs, namely, who bears the burden of adjustment, as well as the moral standing of conditional aid (Danaher 1994; Myers 1987). The debate over what role the IFIs should play has become a political football between the President and Congress, as well as a campaign issue.

One justification that the IMF employs is that its programs serve as a signal of borrower credibility (Dhonte 1997). By signing a letter of intent and agreeing to implement it, the borrowing state sends a message to the outside world that it is about to adopt responsible economic policies. This claim has been perennially espoused as a rationale for conditionality and for making commitments more generally (Maxfield 1997). Unfortunately, evidence in support of this 'catalytic' effect has been scant.

The claim that Fund programs catalyze international finance is an important one for several reasons. First, this justification helps to further our understanding of how and why states delegate to international institutions: not only do they help to signal credibility, but they also provide resources to help resolve pressing domestic problems. Evaluating the extent to which Fund programs produce these catalytic flows thus tells us a great deal about the influence that international institutions have over markets; in other words, whether their endorsement is seen as credible.

Second, the success or failure of Fund programs to generate catalytic effects has been alleged to be a source of noncompliance. Fund programs break down frequently because a state fails to keep its promises in the letter of intent. ₁ If we accept that signing a Fund agreement produces costs as well as benefits, and everything we know about reform supports this claim, then it could well be that politicians breach Fund commitments because the reforms promise results (in the form of foreign investment, aid, and additional private loans) that never materialize.

As Schadler (1996) notes, securing external financing to support the adjustment program is part of the Fund's strategy for addressing macroeconomic imbalances. ₂ Fund programs are designed with specific assumptions about how economic variables will behave months in advance. If an adjustment program operates with the assumption that additional external loans or foreign investment will come in as a result of the program, and these fail to materialize, then it makes meeting the other benchmarks of the program more difficult. As a recent review of Fund conditionality noted, in a number of countries, external flows failed to materialize as projected (Schadler 1996:15). A failure to secure additional external financing (above pre-program levels) can pose problems if the current account deficit is not reduced to a sustainable level, thus necessitating further adjustment.

Existing studies of the catalytic effect find little evidence in support of it. Previous studies on this question (Killick 1995; Conway 1994; Hajivassiliou 1991; Bird and Rowlands 1997, 1999; Rodrik 1995; Adji et al 1997) find no evidence to suggest that signing a Fund program affects aid, investment, and flows of new loans. The existence of weak findings for the catalytic effect

serves to add to the chorus of criticisms of Fund programs (Killick 1995; Bird 1995; Edwards 1989) and strengthen the claims of those who charge that the Fund is ineffective.

Unfortunately, two problems of inference and research design call these findings into question. First, program involvement—the decision to sign a Fund letter of intent—is undertaken for very specific reasons. Existing studies of the conditions under which Fund agreements are chosen suggest that an array of economic variables account for the decision to enter into a Fund supported reform program. Because states seek Fund assistance only under certain conditions, this has important consequences for the study of catalytic finance. It suggests that the economic crisis that precedes the decision to obtain assistance from the Fund may have independent effects on whether investors and lenders choose to lend to a country that signs a letter of intent. As a consequence, our results can be confounded because we have to separate the effects of the balance of payments crisis on the dependent variable of interest from the effects of the Fund program. Put more bluntly, one needs to control for the effects of self-selection in order to generate reliable estimates of the parameters of interest.

A second problem is that many studies of the catalytic effect assume that the program is fully implemented. This, unfortunately, is rarely the case. In making this assumption, these works overestimate the degree to which a state is actually "under" an IMF program (Kahler 1992:94-96). This measurement error attenuates the magnitude of the regression coefficients, making it appear like the program produces weak economic effects (King, Keohane, and Verba 1994:156,167-168). Thus, for these two reasons, it is perhaps not surprising that the results of previous tests have been so limited.

This paper is designed to address these lacunae. I pose two questions. First, after controlling for selection, do Fund programs produce catalytic finance? Second, does the degree of previous compliance that a state has affect its likelihood of receiving additional finance? The evidence suggests that selection bias is not a problem in this sample. More importantly, though, previous compliance is found to significantly affect catalytic flows. States under adjustment programs are not rewarded for good past implementation. However, states are punished by breaking their agreements, as flows all fall off following a program suspension. These results challenge the notion that the Fund strengthens a state's credibility and thereby induces external flows of lending and investment.

 

Background

Before we can proceed to the heart of the matter, more setup of the problem is warranted. First, the IMF has a panoply of lending programs. The ones that I focus on in this project are termed Stand-By arrangements and Extended Fund Facility arrangements. ₃ These programs are designed to address disequilibria in a state's balance of payments. Thus, it is not surprising that studies of the conditions under which these arrangements are concluded focus on a consistent number of factors: low reserves, high levels of debt, high current account deficits, and often high inflation, budget deficits and rapid growth of the money supply (Knight and Santaella 1997; Conway 1994; Joyce 1992; McDonald 1986).

The conventional justification for Fund conditionality is that states lack credibility, and need to make a commitment to an external agent to bolster their resolve. From the standpoint of a potential lender, this is not hard to understand. Reform produces costs as well as benefits, and because implementing it often involves alienating the constituencies that leaders depend on for support, committing to reform can prove difficult. Foreign observers know this: leaders can promise all the reform they want, but a lender's return is directly related to a leader's ability to implement reform. For this reason, foreign actors may be loath to commit investments or loans ex ante.

Fund programs often entail the introduction of fiscal and monetary austerity. This is because the Fund frames balance of payments problems as emerging largely from problems of domestic profligacy. ₄ In this account, politicians undertake inflationary activities, and given the constraints of a fixed exchange rate, they create pressure on the currency. Thus, the Fund program aims to alleviate the balance of payments constraint by providing reserves, and in exchange the state is supposed to introduce policies designed to reduce the current account deficit. These take the form of fiscal and monetary restraint as well as devaluation to improve the exchange rate. Additionally, so-called 'structural reforms,' such as privatization and the removal of export price supports and subsidies, are often mandated to strengthen the competitiveness of the economy.

Thus, the claim that the Fund espouses is that conditionality serves as a signal of 'borrower credibility' in that it allows external agents to distinguish between 'committed' and 'uncommitted' reformers and allocate their assets accordingly. In other words, observers see that a country signs a letter of intent, and this informs them that a country is adopting credible policies (Rodrik 1995; Dhonte 1997). As a result, one would expect an increasing in flows of capital and direct foreign investment following the decision to sign a Fund letter of intent.

There are two logical problems with this line of argument. First, successful reform is never guaranteed. In fact, implementing reform can sometimes prove politically costly. Implementing the measures required in Fund letters of intent can often upset those constituents upon which politicians depend for support. For this reason, reform is not a simple matter of developing a game plan and then implementing it. As numerous authors have noted, economic reform is politically problematic, and politicians have incentives to renege on their commitments (Nelson 1984; Haggard 1986; Haggard and Kaufman 1992; Bates and Krueger 1993). It is therefore not surprising that IMF programs are prone to break down. One published Fund study noted that of the 59 stand-by and extended programs signed between 1988 and 1991, Fund assistance was suspended in 35 cases, as the borrowing state failed to implement the policies outlined in the letter of intent (Schadler 1995).

The existence of uncertainty about whether reform can be sustained can serve to deter additional loans (Rodrik 1989,1991). After all, potential lenders and investors are concerned about rates of return, and if they think that reform backtracking will reduce their returns, they will not invest in these markets. Because Fund programs are often signed to 'tip the scales' and use international leverage to bolster domestic reform, it is not always a given that the program will be successfully implemented. Thus, what might matter is not merely a commitment to reform in terms of a signed letter of intent, but rather a good prior record of successful program implementation.

Fund programs also carry with them a second problem that may hamper our efforts to uncover evidence of catalytic finance. They are seldom one-shot deals. Between 1980 and 1996, Jamaica spent 16 years under Fund programs and the Philippines spent 14 years. South Africa, in contrast, only spent one year under Fund programs. Because these programs are often prone to foster recidivism, a mixed signal may be sent. It could be that because a state signs a letter of intent, that it is attempting to signal that it is credible, yet if it is the case that this is one of a long line of recent programs, external reviewers could infer that the 'medicine' is not having much effect, and avoid these markets entirely. Thus, the case for catalysis could well be contingent on other factors.

 

Past Studies

The effect of Fund programs on capital and FDI flows has been the subject of a great deal of research. Below, I discuss the contributions of five studies to this research question. What constitutes 'catalysis' often varies with the specific study, though it is generally agreed that the subject to be evaluated comprises both capital as well as FDI and is both public and private in nature.

Each of these studies differs in terms of the temporal domain, yet one thing is clear from these existing studies: there is very little evidence that suggests that IMF programs have catalytic effects. In fact, in more than one study below, IMF programs have the opposite effect: rather than act to attract foreign capital and investment, they deter it.

 

Table One: Previous Studies on the Catalytic Effect
Author	Specifics	Findings
Conway 1994	Sample of 74 LDCs from 1976-1986	No evidence of a "credentialing effect" for growth, current account, inflation, investment/GDP
Hajivassiliou 1991	Sample of 79 LDCs from 1970-1982	Fund programs are negatively related to new debt/exports and level of debt service in arrears
Bird and Rowlands 1997	Sample of 90 LDCs from 1974-1989	Fund programs are negatively related to net commitments over exports. Only positive in the case of official lending.
Bird and Rowlands 1999	Sample of 115 low and middle income countries from 1971-1995	Low income country sample: EFF/ESAF positively related to FDI and official source, negatively related to private debt. SBA positively related to official source. Incompletion negatively related to official source. Middle income country sample: EFF positively related to portfolio flows, negatively related to private debt. Incompletion positively related to official source.
Adji et al 1997	Sample of 23 LDCs from 1970-1981	EFF/CFF programs have no effect on nominal/real FDI.
Rodrik 1995	Sample of countries from 1970-1993	No evidence that IMF lending affects private transfers/GDP.
Unless otherwise indicated, only relevant significant findings are reported.

 

Exactly why this is the case is not that hard to understand. Potential lenders and investors either may understand the effects of Fund programs, and may discern that implementing austerity may, over the short run, reduce their returns rather than increase them. For this reason, they do not commit additional resources after a letter of intent is signed. Alternatively, they may also regard the commitment to Fund backed reform as incredible, and for this reason they refuse to make additional commitments. Each of these lines of argument bring with them important inferential implications that many of the above studies ignore. I address these in detail below.

One of the problems with these studies is that they essentially regard the decision to select into Fund programs as a random one. Thus, they essentially operate as if LDCs parceled themselves into a control group without Fund programs and a treatment group in which these states signed Fund programs. In reality, we know that this is far from the case. We know that states seek help from the Fund when they face balance of payments crises. This poses inferential problems because we cannot easily form a counterfactual. Assuming that states randomly select into Fund programs causes a problem because we have to make the argument that if the state had not entered the adjustment program, it would have behaved the same as the other states that did not have adjustment programs. In practice, this means that the flows to states in economic crisis that do not undertake Fund programs are the same as those in states that are not suffering from economic crisis. This is counter to our understanding of how lenders think. As a result, if we are comparing non-Fund states without crises to Fund states with crises, then this means that we have to disaggregate the effects of the crisis that brought the country to the IMF from the effects of the program, and then assess their joint effects on catalytic finance.

An example from Greene (1997:981) should help make this clearer. Suppose that we want to understand the effect that a college education has on one's earnings, and we run the following regression:

The x term is a shorthand for a vector of independent variables that predict earnings. We use a dummy variable for whether someone went to college or not. The key question that we have to answer is this: does , our estimate for the effect of college attendance, accurately capture the causal effect we seek to estimate? Our answer depends on the counterfactual: what are we assuming about the typical individual that goes to college? If we assume that they would possibly (owing to their above average gumption) have high earnings even if they did not go to college, then our OLS regression will actually overestimate the effect of college on earnings.

Why is this the case? One of the classic assumptions underpinning the standard regression model is that the independent variables are not correlated with the error term. In this example, we suspect that this assumption is violated, since there may be unobserved factors that determine whether or not a person goes to college that have an independent effect on earnings. If we run a regression, our coefficient will capture both the effect of education on earnings and the effect of unobserved variables on earnings. Eliminating these confounding effects is one reason to use a random sample.

Of course, the real world does not generate random samples. In our case, the problem is the opposite from that of the above. Existing studies on catalytic finance use the following model:

and a similar problem exists in these studies, since we know that the same variables that affect financial flows also affect whether or not a state goes to the Fund, such as high debt. This compromises one of the assumptions that we make in regression, which is that the factors that are not in the model do not systematically affect the dependent variable. ₅ Since we would suspect that the sample of Fund client states will be less likely to attract catalytic finance even if they didn't go to the Fund (owing to their weak macroeconomic fundamentals), a regression model based on the above form will underestimate the effects of the Fund. Given this, it is not surprising why the results of previous studies have been so meager. Thus, to generate reliable parameter estimates, we have to take sample selection seriously.

Another problem with some of the above studies is that they assume that all programs are fully implemented, which as we noted above, is seldom the case. This assumption complicates attempts to assess whether programs produce catalytic finance, because it means that we essentially overestimate the duration of the program, and as a result, its effects. This modeling decision also brings with it adverse consequences. By assuming that all programs are fully completed, these studies introduce measurement error—by overestimating the amount of time that a state is under a program in the event that the program is suspended for noncompliance. By adding an error variance to the estimate of the coefficients, this results in reduced estimates of causal effects. (King, Keohane, Verba 1994:166-167).

I address these liabilities through a two-fold strategy. First, I employ the techniques developed to handle non-random selection to better assess the effects of Fund programs (Goldstein and Montiel 1986; Ul-Haque and Khan 1999). This allows us to separate the effects of the state's economic fundamentals from the effects of the letter of intent. Following this, I turn to operationalize compliance and look at the impact of both signing and keeping commitments on investment and loan flows. We find very different results at each stage of the process.

 

Research Design

In order to shed some light on this issue, I created a dataset of 106 states that negotiated Stand-by or Extended Agreements between 1979 and 1995. In order to proceed in this project, we have to do three things. First, we have to better understand the factors that cause states to select Fund agreements and understand how to control for the effects of selection. Second, we need to develop a model of loan and investment flows. Third, we need to build a model of compliance and control for variations in compliance on our dependent variables of interest.

A disclaimer is in order. Some may argue that I have misspecified the model, and that the linkage between compliance and aid flows is more complex than I make it. Certainly we can imagine scenarios in which leaders fail to achieve their goals in terms of foreign financing, and as a result break the agreement. However, it should be clear that we cannot answer that question without thinking first about the impact of sample selection. Not surprisingly, even in econometrics, there is no such thing as a free lunch. Compliance may well be endogenous to aid flows, but we should start by specifying the least complex model first, and then add detail.

 

Getting to Yes: Understanding Selection

In order to assess if selection matters, we have to first develop a set of independent variables that predict to it. Fortunately, the existing literature already suggests a number of relevant variables, which we use for the first step in the process. Using the existing literature as a starting point, I used the following variables to predict whether a state will be under a Fund program: debt service ratio, change in net domestic credit of the banking system, GDP growth, terms of trade, budget deficit/GDP, inflation, and reserves measured in months of imports. These variables reflect the conventional wisdom, and are supported by a number of studies (Knight and Santaella 1997; Conway 1994; Przeworski and Vreeland 2000). All variables are lagged one year to avoid simultaneity.

Our conjecture is that these variables serve as a proxy for the overall robustness of the economy. As a result, they should affect the expected returns that potential lenders and investors receive, and therefore affect the level of flows that occur after the state signs a letter of intent. How, then, do we control for selection? To go back to the earnings example from Greene, all that we need to do is understand what factors encourage people to go to college (or select into college), and use the information that we obtain from this model to estimate our equation of interest.

Below, I employ two different techniques to assess whether and to what extent selection bias is a problem. The first is a maximum likelihood estimation (hereafter MLE) using Heckman's (1979) selection model. The second is a more traditional approach used in the Fund's writings on the policy effects (Goldstein and Montiel 1986; Ul-Haque and Khan 1999). The first technique tells us whether and to what extent selection bias is a problem, and the second generates the policy impact of Fund programs on our dependent variables of interest. The use of both techniques serves as a check on the findings.

A Heckman selection model is a two equation system, in which one regression models whether or not selection occurs, and the second equation models outcomes, given selection. In our case, we need to also develop independent variables that predict investment and capital flows. Here we rely on a model developed in Bird and Rowlands (1997, 1999) that includes the following independent variables: per capita GNP, GDP growth, inflation, investment/GDP, exports/GDP, debt service, and international lending rates. ₆ As for the dependent variables, we focus on three: commitments, net Foreign Direct Investment, and net official flows. Commitments comprise new pledged public debt and publicly guaranteed private debt. Official flows measure multilateral and bilateral loans.

Thus, the model below predicts both selection (whether a country was under an IMF stand-by or extended program in a given year) and outcomes (one of the three dependent variables). Of critical importance in the model below is the estimate of rho, which is a variable that measures the extent to which the error terms in each equation are correlated. Put more succinctly, the estimate for rho indicates whether a selection effect exists in this data, and in which direction it operates. We would expect that if the catalytic effect exists, that the estimate for rho would be positive and significant. This tells us that Fund programs produce catalysis, because the flows to Fund clients are greater than those accruing to non Fund clients. In other words, if a state signs an agreement, then it is more likely to receive greater inflows of each of these three measures. In order to guard against autocorrelation, I added a cubic spline to correct for it following Beck, Katz, and Tucker (1997). These results appear below.

 

Table Two: Heckman MLE estimation of selection and catalysis
Model		Commitments	Official flows	FDI
Outcome	GNP per capita t-1	-8.84e-06***	-.0000209****	8.64e-06
	GDP growth t-1	-.000569	-.000348	.000139
	Inflation t-1	.000041****	.0000836****	-8.62e-07
	Exports t-1	.00081***	.000937***	.000213***
	Investment t-1	.000528	-.000082	.000426**
	Lending-LIBOR t-1	-.000155	.0000411	.0000884
	Debt Service t-1	.00026	.000343	.00017**
	Constant	.0567****	.0471***	-.0153*
Selection	Debt Service t-1	.01539***	.0154***	.0154***
	Growth t-1	-.02348**	-.0236**	-.0237**
	Reserves t-1	-.04381**	-.04289**	-.047**
	Terms of Trade t-1	2.37e-14***	2.31e-14***	2.18e-14***
	Change in Net Domestic Credit t-1	.0605****	.0597****	.0592****
	Budget Deficit/GDP t-1	-.00769	-.002	-.0023
	Inflation t-1	-.0011****	-.000107****	-.0011****
	Constant	.4634***	.4840***	.4943***
Rho Rho Model		-.17706 0.1930 0.0000	-.0321 0.8722 0.0000	.1420 0.1522 0.0016
Number of observations: 546 Dependent variables scaled over GNP. Uncensored observations: 242 Spline segments not shown. Censored observations: 304 *, **, ***, **** represent levels of significance at the .10 level, .05 level, .001 level, and .0001 levels, respectively.

 

These results merit some discussion. First, focusing on the selection results (the bottom half of the table) we see that this model reflects the conventional wisdom, which is that states seek assistance from the Fund when they have low growth, low reserves, and high levels of debt. Moreover, the factors that drive states to the Fund are not entirely exogenous to the policies adopted by leaders of these countries, as they are also prone to turn to the Fund when they exhibit periods of monetary overheating. The on the cubic spline segments was 209.38, which tells us that we certainly have autocorrelation in this model. Including these segments controls for it (Beck, Katz, and Tucker 1997).

Turning to the top half of the Table, we note that a number of variables are significant. For official flows and commitments, flows are directly related to inflation and exports. We also note that these flows are more likely to go to states with low per capita GNP, which certainly makes sense for official flows. Turning to FDI, we note that increases in exports, investment, and debt service increase FDI flows.

The parameters in the last row of the table, however, merit our attention. Overall, the models are highly significant, but the estimates for rho are not significant for any of the dependent variables estimated here. This is an important result, for it suggests that no selection effect exists in this sample. In other words, no difference exists between Fund states and non-Fund states in terms of their level of investment and debt flows. Thus, while we thought that selection bias may have been an issue in previous studies which helped to explain the weak effects of catalysis, based on this sample we cannot support this claim. In this sample, selection bias is not a threat to inference. We do note that the rho coefficient is positive only in the case of FDI, which suggests some catalysis, but this is not even significant at a .10 level.

While the use of maximum likelihood Heckman techniques is common in political science, it is less common in economics, and much less common in the literature on the analysis of Fund programs (Ul Haque and Khan 1998; Bordo and Schwartz 1999). Thus, as a doublecheck, I reestimated these models using the Generalized Evaluation Estimator (GEE) procedure employed in the IMF's scholarship (Goldstein and Montiel 1986). This model is similar to the one above, but it involves two separate stages. In the first, we estimate a probit model of the decision to select an agreement or not. We then take the predicted values from this model and form the hazard rate, which is a variable that captures the effects of all of the independent variables on selection. When used as an additional variable in our estimation of the equation of interest, in this case, aid and investment flows, this 'controls' for the effects of selection. ₇ The GEE allows us to control for selection, but it allows us to generate a separate coefficient for the impact of Fund programs. It is thus a bit more interpretable than the Heckman MLE.

The independent variables in both models are unchanged. I present the probit results first.

 

Table Three: Probit Selection Model
Variable	Coeff/S.E.	P value
Debt Service t-1	.0174 (.0045)	0.000
Change in Domestic Credit t-1	.0571 (.0122)	0.000
GDP growth t-1	-.0312 (.0111)	0.005
Budget Deficit/GDP t-1	-.0046 (.0124)	0.711
Reserves t-1	-.0644 (.0234)	0.006
Inflation t-1	-.0010 (.00022)	0.000
Terms of Trade t-1	2.30e-14 (8.70e-15)	0.008
Constant	.6894 (.1653)	0.000
Number of observations: 641 Model : 0.0000 Estimates for cubic spline segments omitted.

 

Again, these results mirror those above, and confirm what we know: both internal and external factors are at work in driving states to the Fund. To estimate the effect of Fund programs, I generated the hazard rate from this probit model, and include it as a variable in an OLS regression. I make appropriate corrections for a time-series cross-sectional research design by including a lagged dependent variable on the right hand side and use panel-correct standard errors (Beck and Katz 1995). These results appear in the table below.

 

Table Four: Impact of the Selection of IMF programs on flows
	Commitments	Official Flows	FDI
LDV	.4818**** (.0947)	.7968**** (.0923)	.59022**** (.1383)
GNP per capita t-1	-6.62e-06**** (1.86e-06)	-4.39e-06** (1.61e-06)	3.06e-07 (4.53e-07)
Growth t-1	-1.89e-06 (.000479)	-.00069 (.00057)	.000127 (.000123)
Inflation t-1	.000018** (7.33e-06)	.000017** (7.12 e-06)	-1.23e-06 (1.54e-06)
Investment/GDP t-1	.000522 (.00038)	-.000285 (.00020)	.000105 (.000104)
Exports/GDP t-1	.000268 (.00019)	-.000086 (.00019)	.000171** (.000059)
Lending-LIBOR t-1	-2.39e-06* (1.37e-06)	-8.06e-07 (1.30e-06)	8.10e-08 (1.57e-07)
Debt Service Ratio t-1	-.0000254 (.000286)	-.000341 (.000274)	.00014** (.000056)
Fund program dummy	.01072** (.00576)	-.01294** (.00539)	-.0011 (.00164)
Hazard Rate	-.00119 (.0064)	-.00041 (.00537)	.0022* (.00136)
Constant	.0216 (.0153)	.0484** (.0157)	-.00699 (.0046)
Number of observations: 468 Model : 0.0000 (for all three) Panel-corrected standard errors appear in parentheses. *, **, ***, **** represent levels of significance at the .10 level, .05 level, .001 level, and .0001 levels, respectively.

 

For the most part, the results from these models parallel the MLE estimation. For the commitments and official flows models, both GNP per capita and inflation are appropriately signed and significant. Exports were not significant for either of these models in this estimation. In the FDI model, exports and debt service are appropriately signed and significant, and investment is not significant, though it was in the MLE above.

Turning to the other coefficients of interest, we note that the hazard rate is only significant in the case of the FDI model, though at a .10 level. These results are slightly different from the MLE estimation of FDI reported in Table Two, where the rho coefficient was .15. This suggests a slight selection effect does exist, but the dummy for Fund program is not significant, implying that signing a letter of intent does not affect FDI flows. In order to properly interpret these results, we need to remember what each variable tells us. We are trying to address two issues: are there unobserved variables correlated with the decision to enter into agreements that affect flows, and what is the effect of the Fund program on these flows? In the FDI model, Fund program states, owing to their decision to enter into programs, are more likely to receive positive FDI flows. This result, however, is attributable to their economic fundamentals rather than a direct result of the Fund program. The hazard rate is not significant in either commitments or official flows, which tells us that selection bias is not an issue in estimating these models. This is a surprising result, because if we accept that states go to the Fund when they face economic crisis, then we would expect that the sign on the hazard rate would be negative.

These models also generate coefficients for the Fund program dummy variable, which tells us the effect of signing a Fund letter of intent. In the case of commitments, we note that signing a letter of intent has a positive and significant effect. However, it has a negative and significant effect on official flows. It has a slight negative effect on FDI flows, but this is not significant.

Thus, we find very weak evidence that selection effects might compromise attempts to generate valid inferences, and we find mixed results for the catalytic effects of Fund programs: catalysis seems to exist in commitments, and the opposite seems to hold in the case of official flows. For FDI, there is a slight negative effect associated with signing a Fund program.

When is catalysis important?

As an extension, I reran the regressions with a different variable indicating the first year of the Fund program. This allows us to test the catalytic hypothesis in a more refined fashion by discarding all the observations on the following years of an adjustment program. Of course, if we follow the argument to the letter, these observations are 'most likely' to reveal evidence of catalysis. After all, it could be that the effect is muted by repeated years under a Fund program, and that focusing on the first year gives us the best opportunity to see if it exists. These results appear below.

 

Table Five: Impact of Selection on Catalytic Flows—First Year Only
	Commitments	Official Flows	FDI
LDV	.47806**** (.0958)	.80569**** (.09479)	.502959**** (.137107)
GNP per capita t-1	-6.51e-06**** (1.66e-06)	-4.48e-06** (1.88e-06)	3.01e-07 (4.44e-07)
Growth t-1	.0000596 (.000475)	-.000722 (.000583)	.000116 (.000123)
Inflation t-1	.0000186** (8.45e-06)	.0000148** (7.11e-06)	-1.25e-06 (1.55e-06)
Investment/GDP t-1	.000524 (.000389)	-.000291 (.000204)	.000107 (.000103)
Exports/GDP t-1	.000277 (.000194)	-.000103 (.000202)	.000171** (.000059)
Lending-LIBOR t-1	-2.54e-06** (1.34e-06)	-6.31e-07 (1.33e-06)	8.01e-08 (1.58e-07)
Debt Service Ratio t-1	-.0000365 (.000287)	-.000345 (.00028)	.000143** (.000056)
First year Fund program dummy	.011167** (.00403)	-.001287 (.003589)	-.002751** (.001441)
Hazard Rate	-.00474 (.004959)	.001857 (.00409)	.002375** (.001175)
Constant	.027434** (.013815)	.037054** (.014246)	-.007088* (.00407)
Number of observations: 468 Model : 0.0000 (for all three) Panel-corrected standard errors appear in parentheses. Coefficients identified with *, **, *** , and **** are significant at .10, .05, .001, and .0001 levels respectively.

 

The results in this table support the findings in Table Four. The First Year Program Dummy is positive and significant in the case of commitments, and negative and significant in the case of FDI. Official flows are not significant. This tells us that in following years of a program, FDI flows are not significant, and official flows decrease and become significant in following program years.

We also see added evidence for the selection effect of Fund agreements, as it is both positive and significant in the FDI model. This tells us that states that sign Fund agreements are more likely to receive FDI based on their economic fundamentals prior to signing the letter of intent. The Fund program, in contrast, acts to reduce FDI. Again, this is the reverse of what we would expect.More work is necessary to understand these results, but we can conjecture that some of the states in the sample are adopting Fund programs as precautions or are reforming preemptively. In this instance, it could be that the effects of the economic downturn on FDI are muted.

Thus, we find mixed evidence for catalytic finance dependent on its measurement. We also find some evidence that selection is a problem that we address in our estimation procedures. Now we assess the effects of program compliance to check if these results are robust.

 

Past Compliance and Catalysis

Rethinking the informational rationale for catalysis allows us to better specify the model. Signing a letter of intent is believed to serve as an influential signal of a borrower's intent to adopt responsible reform policies. However, we also know that reform is politically problematic, and that politicians have incentives to defect from the agreements that they sign. Thus, this raises an important issue: when is this signal a credible one? We know from game theoretic models that in an environment of uncertainty, costly signals are informative ones. ₈ Thus, it could be that states with good prior records of Fund program implementation send better signals about their credibility, because these states have paid the costs of adjustment, and thus attract higher levels of catalytic flows.

Thus, it could be that the catalytic effect is contingent, as prior program compliance conveys additional information to a prospective lender or investor; not merely 'We are prepared to adopt responsible policies to address the economic crisis,' but also 'because we have successfully implemented these policies in the past, you can be assured that we will do it again credibly.' Thus, perhaps the catalytic effect is closely related to a state's prior degree of compliance. We have both theoretical as well as methodological reasons for including compliance as an independent variable.

The one previous study that addressed this question, that of Bird and Rowlands (1999), found mixed results. A history of uncompleted programs was found to reduce official source lending in low income countries, but it increased official source lending in middle income countries. They measured nonimplementation by the number of agreements in the past four years of which more than 20% of the total arrangement was left undrawn. The problem with this measure is that it conflates the existence of a compliance problem with the number of arrangements that a country has in a given year. For example, if a state has four agreements in four years and one fails, this is coded the same as a state that has one agreement in four years which fails. One might think that this second state would be better "managed"than the first. Thus, it is not quite clear that the measure they use accurately captures the concept.

I elected to operationalize this variable more simply and avoid the confound of tying compliance with the number of programs in a given amount of time. I gathered information on whether a program was suspended at any point for noncompliance for programs between 1988 and 1995. In 34 of the 144 programs between 1988 and 1995, states were not eligible for all of the drawings either because they missed performance criteria and were unable to obtain a waiver from the Fund or they failed a quarterly review (Schadler 1995a:2 and interviews). In some cases, the state was able to get the agreement restarted. In others, it did not, and the agreement expired. Thus, we still term a state as "under" a Fund program even if there are compliance problems.

Codings for this variable came from the Schadler report and quarterly country reports of the Economist Intelligence Unit. These reports provide detailed quarterly information regarding a country's relationships with creditors as well as information regarding adherence to Fund performance criteria.

If it is the case that catalytic finance is linked to a state's past history of implementing programs, then we would expect that whether the most recent Fund program failed or succeeded would be have significant affects on new flows of lending and investment. However, we must proceed very carefully in this estimation. Because compliance is only observed for selected cases, this creates a collinearity between the selection and compliance variables that can hamper our attempts to generate reliable inferences. Thus, I lagged the compliance variable, so that I estimate whether there was a compliance problem in the previous program year.

The model below has two wrinkles from the previous estimations. First, because I only have compliance information on states in Fund programs between 1988 and 1995, this cuts down our number of years and the number of observations substantially. Because the number of observations is reduced to slightly less than 200, our attempts to estimate these models using the MLE technique reported on Table One were unsuccessful. As a result, the models below are estimated according to the Fund's GEE technique.

Next, I need to understand the factors that allow states to make and keep their commitments. Using the hazard rate from this model, we can then plug it into the same equation that we employed earlier to assess the impact of compliance on flows. Thus, rather than a simple probit of program selection as above, I employ a joint probit model of selection and compliance. Using a different hazard rate makes sense since some states leave Fund programs because of compliance problems, and some leave because the "medicine" seems to have worked. Thus, changing the hazard helps us to better distinguish successful implementers from failed ones. Since we know what Fund performance criteria entail, we can build an appropriate model.

Below I use a probit model with sample selection to assess the factors that produce compliance, given the prior decision to enter an agreement (Van de Ven and Van Pragg, 1981). The selection model is the same as that in Table Three and the model of compliance includes variables that are often the basis of Fund performance criteria: the growth of the money supply, inflation, and GDP growth. These variables are not lagged, because we assume a specific chain of events. Contemporaneous increases in the money supply and inflation suggest that the Fund program is not being implemented, and can often lead to program suspension. Other variables are relevant here, especially fiscal data, but are omitted here because of severe missing data problems. ₉

This model is a joint Heckman model as in Table One, so the rho coefficient will be important here, as it tells us the extent to which the sample of Fund compliant states is nonrandomly selected. These results are shown in the table below.

 

Table Six: Heckman probit model of selection and compliance
Selection Model		Compliance Model
Debt t-1	.01444** (.0043)	Change in Net Domestic Credit	.1249* (.0612)
Growth t-1	-.02661* (.0105)	GDP growth	-.0524** (.0187)
Reserves t-1	-.02933 (.0285)	Inflation	-.00411 (.00048)
Terms of Trade t-1	2.66e-14* (1.07e-14)	Constant	.4452* (.1985)
Net Domestic Credit t-1	-.00022 (.00028)
Inflation t-1	3.30e-06 (.000095)
Constant	-.0680 (.1549)
Rho Rho Model	-.6097 .0073 .0009
Number of observations: 623 Censored observations: 455 Uncensored observations: 168 Splines not included.

 

This model confirms our understanding of surveillance in Fund adjustment programs. These findings suggest that Fund programs break down because states are unable to implement policies of monetary restraint.

Using this system of equations, we can now move to stage two. We start by forming the hazard rate, which is the joint probability of selection and compliance. Then using this as an instrument, we add it to the previous model of flows. As noted above, because we are add a compliance variable to the equation, which is only observed if there is an agreement in the first place, this reduces our number of observations substantially. These results use the same estimation procedure as in Table Four.

 

Table Seven: Impact of Selection and Past Compliance on Flows
	Commitments/GNP	Official Flows/GNP	FDI/GNP
LDV	.7315*** (.166)	.61072*** (.1243)	.55327*** (.1259)
GNP per capita t-1	-7.40e-07 (2.18e-06)	-4.57e-06* (1.98e-06)	2.31e-06** (7.06e-07)
Growth t-1	.00041 (.00066)	-.000241 (.00035)	-.000031 (.00024)
Inflation t-1	-.000036 (.000051)	.0000157 (.0000533)	-1.84e-06 (9.68e-06)
Investment t-1	-.000078 (.00048)	-.0000386 (.000156)	.00121 (.00068)
Exports t-1	-.000166 (.00021)	-.000219 (.000148)	-.000133 (.000181)
Lending-LIBOR t-1	6.13e-06 (.000066)	-.000026 (.000069)	-9.88e-07 (.000026)
Debt Service Ratio t-1	.000136 (.00045)	-.000109 (.00028)	.000098 (.000197)
Fund Program Dummy	-.01243* (.00609)	-.006872 (.00642)	-.00774* (.00311)
Compliance Problem t-1	.00403 (.00636)	.000875 (.00522)	.00146 (.00303)
Hazard	-.0154 (.0165)	-.0131 (.0239)	.00352 (.0144)
Constant	.03588 (.02508)	.0453** (.01648)	-.0154 (.0149)
N=167 Robust standard errors appear in parentheses. Model : 0.0000 (for all three) Coefficients identified with *, **, and *** are significant at .05, .001, and .0001 levels respectively.

 

Several results merit our attention here. First, we note that under no conditions is the hazard variable significant. This confirms our findings above in that in this sample, there is little evidence of selection bias comparing Fund program vs. non-program states. Once we control for past compliance, however, our assessment of the effect of Fund programs changes. When we control for the past noncompliant history of a state, we note three changes. First, the sign on the commitments coefficient reverses, telling us that Fund programs reduce commitments. Second, effect of Fund programs on official flows disappears. Finally, controlling for past noncompliance suggests that Fund agreements appear to negatively—and significantly—affect foreign direct investment. These results are somewhat surprising—after all, we would expect that past compliance would have independent effects on these flows. However, it does not. ₁₀ Nor is it appropriately signed. We would expect a negative coefficient here, as this tells us that prior compliance problems reduce flows. These results lead us to think that noncompliance does not have an independent effect.

We note that the lagged compliance variable and the Fund program dummy are collinear at a .1313 level. Of course, we would expect this, because we only have compliance information on those states that select into Fund programs. However, this means that we need to ensure that these results are robust and are not a direct result of the collinearity. Thus, I performed a number of robustness checks on these results. First, I reran the estimation to ensure that these results were not merely an artifact of changing the sample. I ran the model without the lagged compliance variable, and intentionally restricted the time domain to 1988-1995. The coefficients for the Fund program selection variables were not significant in any of the three models, and they all had the same signs as in Table Seven. This tells us that the results for commitments and FDI are not a result of changing the sample size, but rather are attributable to adding the lagged compliance problem dummy variable.

Thus, these results are somewhat puzzling. We suspect that compliance 'matters,' but it only affects outcomes by changing the sign of the Fund program dummy. It does not appear to have an independent effect on flows. Recalling our earlier discussion, however, it should be clear than I have misspecified the model. I noted that because lenders may not regard the signal of signing a Fund program as particularly credible, we have reason to suggest that what matters is not merely the presence of absence of a signed letter of intent, but rather whether a letter of intent is signed with a good past record of compliance. This merits a different specification from the above. Since the effects of an independent variable (the Fund program dummy) depend on the value of the compliance variable, this tells us that our theory calls for an interactive term rather than an additive one. ₁₁

Thus, I added an interactive term to the model, which represents a test of this conditional hypothesis. ₁₂ The model below is

where represents our intercept term, is a shorthand for all our other independent variables, FP is our dummy variable for the presence or absence of a Fund program, PC is our dummy variable for the presence or absence of a past compliance problem, and FP*PC is our interaction term that takes on a value of 1 during periods in which a Fund agreement is selected and the state has had a compliance problem in the past year. For observations in which a prior compliance problem is not present, the value for PC is zero, and this model simplifies to

In contrast, when a prior compliance problem is present, then PC takes on a value of 1, and the model is

Because interactive terms are amalgamations of two different variables, this means that the standard errors are likely to be inflated, and we must proceed carefully. I also estimated the conditional coefficient b₁ + b₃, which captures the relationship between the presence of a Fund agreement and flows when compliance problems are present. Thus, in the models below, the coefficient for FP captures the relationship between the presence of a Fund program and flows when prior compliance is good, and the coefficient for the PC term captures the relationship between flows and noncompliance when the state is not under an IMF program. To reiterate, if we accept the argument that what matters for catalysis is the presence of Fund programs when states have a history of credible adjustment, then an interactive hypothesis makes the most sense.

Thus, I reestimated the models that were reported in Table Seven by including the multiplicative term, and the results from each are detailed below.

 

Table Eight: Conditional Coefficients
	Commitments	Official Flows	FDI
Fund Program	-.001901 (.00921)	.003343 (.00652)	.001939 (.004113)
Past Compliance Problem	.02308* (.01365)	.019458** (.00924)	.019084*** (.003701)
Fund Program * Past Compliance Problem	-.024289** (.01207)	-.023653** (.00865)	-.022424*** (.00336)
b1 + b3	-.026189*** (.00704)	-.020309** (.00889)	-.020485*** (.00281)
*, **, ***, **** represent levels of significance at the .10 level, .05 level, .001 level, and .0001 levels, respectively. N=167.

 

These results bear some discussion. First, we note that in none of the models is there a significant relationship—in either direction—between the presence of a Fund program and flows when states had a record of good compliance in the previous year. We also note that official flows, commitments, and FDI all significantly decrease in those states that are under IMF agreements that experienced compliance problems in the previous year. Finally, as the coefficient for the past compliance term suggests, if a state is not under an IMF program and had a compliance problem during its program in the previous year, flows increase significantly. In none of these models is selection bias a potential problem, because the coefficients for the hazard rate are not significant in any of the formulations tested.

Several implications emerge from these results. First, if we define the 'catalytic effect' of Fund programs as contingent not only on the presence or absence of a Fund program, but on the level of previous compliance under the program, we see no evidence that suggests that it exists. In fact, even in the cases in which states were in compliance in the previous year, there is no increase in flows. States do not appear to be rewarded for good past performance under their Fund program.

Somewhat surprisingly, when a state is under a Fund program and experienced a compliance problem leading to the suspension of the agreement, catalytic flows decrease substantially. This implies that external actors listen selectively to the IMF; they do not appear to enter a state to a significant extent, but upon hearing that a state is suspended, they bail out. This holds for all specifications of the dependent variable: commitments, official flows, and foreign direct investment. The Fund seems, therefore, to send a mixed message: states under its programs are not 'more credible' even when they implement the letter of intent successfully, but they are most certainly less credible when the Fund sanctions them. These states that are sanctioned are still technically 'under' the Fund program, yet no tranches are released.

Thus, the only evidence of a beneficial effect of Fund programs in this study occurs after states leave them. Those states no longer under Fund programs that had compliance problems in the last year of them see an increase in flows of all types. These states seem to be rewarded for 'graduating' from the program, even under less than stellar conditions.

 

Implications

These findings bring with them broader lessons for the study of international institutions and for the analysis of the effects of Fund programs more generally. First, in terms of the IMF, the evidence here points to an 'incredibility effect' in that despite the Fund's repeated invocations to the contrary, little evidence exists to support the so called "catalytic" effect of IMF programs. Thus, though international institutions are created to solve problems of market failure and in this case the 'market failure' is real, since rational individuals won't allocate assets to countries that are macroeconomic basket cases, in this case, we see little evidence that this solution is an effective one.

At the same time, we note that Fund sanctions can be costly. This is somewhat surprising, since the conventional wisdom is that states can return to the Fund with their past sins of program noncompliance forgiven and receive fresh loans. In the Public Choice approach to international institutions (Frey 1984; Vaubel 1991), the Fund is a budget-maximizing bureaucracy that values lending over policy reform. To derive from this that noncompliance is costless, however, is a misnomer, since as the conditional coefficient suggests, all types of flows drop off in the wake of a program suspension.

This evidence stands in contrast to our conventional understanding of international institutions. Recent game-theoretic work regards the formation of enforcement rules as endogenous. In Downs and Rocke's (1995) GATT model, states negotiate the enforcement regime, and as a result, they set the punishment period and the thresholds at a high level, since they know that protectionist demands from interest groups might lead them to one day breach their commitments. As a result, we would not expect noncompliance to be costly. The evidence here suggests that the opposite is the case; Fund sanctions are costly to the extent that they deter additional flows of loans and investments. To be fair, the thresholds at which a program gets suspended may well vary across states. Russia, after all, is considered 'too nuclear to fail.' However, to suggest that the behavior of the IMF does not constitute an "enforcement model" (as do Chayes and Chayes 1995) may be too strong a claim.

This work raises an important question about the conditions under which international agreements are sought. The conventional wisdom is that states do not sign agreements that they do not feel that they can honor if noncompliance is costly. However, in this project, we found no evidence of a selection effect with regard to entering IMF agreements. It could be then, that these agreements are in the aggregate signed when states have no viable options, and that we need to shift our understanding of the conditions under which international agreements are signed and adhered to so as to better appreciate the importance of the no-agreement status quo.

Turning to the literature on the analysis of Fund programs, this project has two important implications. First, analysis of this sample shows no evidence of a selection bias comparing Fund program and non-Fund states. At the outset, I noted that because states select when to enter Fund programs, and that because the reasons why they enter Fund programs may have independent effects on catalytic flows, that selection bias may be a threat to inference. Of course, the potential remains that selection bias is an issue, but this would require a different sort of argument. This argument would suggest that the selection bias stems not from states that frequent the Fund and those who go rarely, but from the differences between the sample of all Fund program states and the non-Fund client sample. ₁₃

More importantly, the main finding of this paper is that one needs to control for the degree of compliance with Fund programs when analyzing their effects. Recalling that a number of the coefficients switched signs when we added a variable controlling for the presence of a compliance problem in the previous year serves to make this point abundantly clear, and underscores the claim of Ul-Haque and Khan (1999) that the degree of implementation is often an important omitted variable. Fortunately, a number of recent studies (Mercer-Blackman and Unigovskaya 2000; Conway 1994) have begun to address the gap and estimate the effects of Fund programs controlling for the degree of compliance with them.

 

Appendix

Independent Variables from World Bank World Development Indicators:

Net domestic credit: Net domestic credit is the sum of net credit to the nonfinancial public sector, credit to the private sector, and other accounts. Data are in current local currency.

GDP growth: Annual percentage growth rate of GDP at market prices based on constant local currency.

Inflation, GDP deflator: Inflation as measured by the annual growth rate of the GDP implicit deflator.

Gross domestic investment (% of GDP): Gross domestic investment consists of outlays on additions to the fixed assets of the economy plus net changes in the level of inventories.

Interest rate spread (lending rate minus LIBOR): Interest rate spread is the interest rate charged by banks on loans to prime customers minus the interest rate paid by commercial or similar banks for demand, time, or savings deposits.

GNP per capita (constant 1995 US$): GNP per capita is gross national product divided by midyear population.

Terms of trade adjustment: The terms of trade effect equals capacity to import less exports of goods and services in constant prices.

Total debt service (% of GNP): Total debt service is the sum of principal repayments and interest actually paid in foreign currency, goods, or services on long-term debt, interest paid on short-term debt, and repayments (repurchases and charges) to the IMF.

Exports of goods and services (% of GDP): Exports of goods and services represent the value of all goods and other market services provided to the world.

 

Dependent Variables are from the World Bank's Global Development Finance:

All these variables are scaled over GDP and measured in US dollars.

Commitments: Commitments are the total amount of long-term loans for which contracts were signed in the year specified; data for private nonguaranteed debt are not available.

Foreign direct investment, net inflows: Foreign direct investment (net) shows the net change in foreign investment in the reporting country.

Official net resource flows: Official net resource flows are the sum of official net flows on long-term debt to official creditors (excluding IMF) plus official grants (excluding technical cooperation).

 

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Endnotes

Note 1: Compliance problems are not new, nor are they only common among short-term Fund lending programs. For example, of the thirty EFF programs initiated prior to January 1, 1985, twenty-four were either renegotiated or had payments interrupted. Sixteen of the twenty-four were canceled outright by the Fund (Haggard 1986:157-158). The recent review of the Extended Structural Adjustment Facility noted that only one-quarter of these arrangements have been completed without interruption (International Monetary Fund 1997:42). Back

Note 2: In some cases, signing a letter of intent is a precondition to a concerted debt restructuring, though this is not always the case. Back

Note 3: Stand-by agreements are generally 12-18 month arrangements, while EFFs are for a longer duration (24 months and up) and for a larger amount. Back

Note 4: Of course, the East Asian crisis was more a banking crisis or a private sector problem than a public sector problem. While increasingly important, the source of the balance of payments problem is not a key issue for this paper, since the domain of cases ends in 1995. Back

Note 5: In other words, we assume that E(u_i|*X) = 0. The problem is that unobserved factors induce a correlation between the error term and the independent variable (Berk 1983; Achen 1986). Back

Note 6: The appendix contains all relevant information regarding the variables. Back

Note 7: It is for this reason that this process was originally referred to as "two-step" estimation following Heckman (1979). Back

Note 8: Rodrik (1991) and Fearon (1994) are exemplars in this regard. Back

Note 9: Adding a budget deficit measure hampers these results, as it reduces the number of cases by more than a full third. Back

Note 10: Reestimating these models by removing the selection variable does not change the sign or significance of past compliance in any of the models. Back

Note 11: An additive term, in contrast, suggests that the effects of an independent variable on the dependent variable are constant across all values of the other independent variables. Back

Note 12: The argument about how multiplicative effects are used is in Friedrich 1982, and the presentation below follows from Clark and Reichert 1999. Back

Note 13: Other studies that evaluate the effects of Fund programs, however, are based on similar designs (Conway 1994; Bagci and Perraudin 1997). TThis is an area that awaits further research. Back