Conclusions: The future of growth econometrics

In this section, we offer some closing thoughts on the most promising directions for empirical growth research. We are not the first authors to set out manifestoes for the field, and we explicitly draw on previous contributions, many of which deserve wider currency.

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We start with Pritchett (2000a), who lists three questions for growth researchers to address:

• What are the conditions that initiate an acceleration of growth or the conditions that set off sustained decline?

• What happens to growth when policies - trade, macroeconomic, investment - or politics change dramatically in episodes of reform?

• Why have some countries absorbed and overcome shocks with little impact on growth, while others seem to have been overwhelmed by adverse shocks?

This agenda seems to us very appropriate, not least because it focuses attention on substantive economic issues rather than the finer points of estimating aggregate produc­tion functions. The importance of the first of Pritchett’s questions is evident from the many instances where countries have moved from stagnation to growth and vice versa. A paper by Hausmann, Pritchett and Rodrik (2004) explicitly models transitions to fast growth (“accelerations”) and makes clear the scope for informative work of this kind.

In all three cases, it is clear that econometric work should be informed by detailed studies of individual countries, such as those collected in Rodrik (2003). Too much empirical growth research proceeds without enough attention to the historical and in­stitutional context. For example, a newcomer to this literature might be surprised at the paucity of work that integrates growth regression findings with, say, the known conse­quences of the 1980s debt crisis.

Another reason for advocating case studies is that much of the empirical growth liter­ature essentially points only to reduced-form partial correlations. These can be useful, but it is clear that we often need to move beyond this. A partial correlation is more persuasive if it can be supported by theoretical arguments. The two combined are more persuasive if there is evidence of the intermediating effects or mechanisms that are em­phasized in the relevant theory. There is plenty of scope for informative work that tries to isolate mechanisms by which variables such as financial depth, inequality, and po­litical institutions shape the growth process. Wacziarg (2002), in particular, highlights the need for a structural growth econometrics, one that aims to recover channels of causation, and hence supports (or undermines) the economic significance of the partial correlations identified in the literature.

A more extreme view is that growth econometrics should be supplanted by the cal­ibration of theoretical models. Klenow and Rodriguez-Clare (1991b) emphasize the potential of such an approach and note that Mankiw, Romer and Weil’s (1992) influ­ential analysis can be seen partly as a comparison of estimated parameter values with those associated with specific theoretical models.

It may be premature to say that econometric approaches should be entirely replaced by calibration exercises, but the two methods could surely inform each other more often than at present. Calibrated models can help to interpret parameter estimates, not least in comparing the magnitude of the estimates with the implications of plausible models. Klenow and Rodriguez-Clare (1991b) discuss examples of this in more detail. At the same time, the partial correlations identified in growth econometrics can help to act as a discipline on model-building and can indicate where model-based quantitative inves­tigations are most likely to be fruitful. This role for growth econometrics is likely to be especially useful in areas where the microeconomic evidence used to calibrate structural models is relatively weak, or the standard behavioral assumptions may be flawed.

The need for a tighter connection between theory and evidence is especially apparent in certain areas. The workhorse model for many empirical growth papers continues to be Solow-Swan, a closed economy model which leaves out aspects of interdependence that are surely important. Howitt (2000) has shown that growth regression evidence can be usefully reinterpreted in the light of a multi-country theoretical model with a role for technology diffusion. More generally, there is a need for researchers to develop empirical growth frameworks that acknowledge openness to flows of goods, capital and knowledge. These issues are partly addressed by the theoretical analysis of Barro, Mankiw and Sala-i-Martin (1995) and empirical work that builds on such ideas deserves greater prominence. Here especially, research that draws on the quantitative implica­tions of specific models, as in the work of Eaton and Kortum (1999,2001) on technology diffusion and the role of imported capital goods, appears to be an important advance.

The neglect of open economy aspects of the countries under study is mirrored else­where. Much of the empirical literature uses a theoretical framework that was originally developed to explain the growth experiences of the USA and other developed nations. Yet this framework is routinely applied to study developing countries, and there appears plenty of scope for models that incorporate more of the distinctive features of poorer countries. These could include the potentially important roles of agricultural employ­ment, dualism, and structural change, and in some cases, extensive state involvement in production. This is an area in which empirical growth researchers have really only scratched the surface.

Some of these issues are connected to an important current research agenda, namely the need to distinguish between different types of growth and their distributional con­sequences. For example, the general equilibrium effects of productivity improvements in agriculture may be very different to those in services and industry. Identifying the nature of “pro-poor” growth will require more detailed attention to particular features of developing countries. Given that the main source of income for the poor is usually labour income, growth researchers will need to integrate their models with theory and evidence from labour economics, in order to study how growth and labour markets in­teract. Agenor (2004) considers some of the relevant issues, and again this appears to be a vital direction for future research.

Ideally, research along these various lines will utilize not only statistics, but also the power of case studies in generating hypotheses, and in deepening our understanding of the economic, social and political forces at work in determining growth outcomes. Case studies may be especially valuable in two areas. The first of these is the study of tech­nology transfer. As emphasized in the survey by Klenow and Rodriguez-Clare (1997b), we do not know enough about why some countries are more successful than others in climbing the “ladder” of product quality and technological complexity.

A second area in which case studies are likely to prove valuable is the study of po­litical economy, in its modern sense. It is a truism that economists, particularly those considering development, have become more aware of the need to account for the two­way interaction between economics and politics. A case can be made that the theoretical literature has outpaced the empirical literature in this regard. Studies of individual coun­tries, drawing on both economic theory and political science, would help to close this gap.

Thus far, we have highlighted a number of limitations of existing work, and direc­tions in which further research seems especially valuable. Some of the issues we have considered were highlighted much earlier by Levine and Renelt (1991), and that might lead to pessimism over the long-term prospects of this literature.^[372] This also shows that our prescriptions for future research could seem rather pious, since the improvements we recommend are easier said than done. We end our review by considering some areas in which genuine progress has been made, and where further progress appears likely.

One reason for optimism is the potential that recently developed model averaging methods have for shedding new light on growth questions. These methods help to ad­dress the model selection and robustness issues that have long been identified as a major weakness of cross-country growth research. By framing the problem explicitly in terms of model uncertainty, in the way envisaged by Leamer (1978), it is possible to consider many candidate explanatory variables simultaneously, and identify which effects appear to be systematic features of the data, as reflected in posterior probabilities of inclusion.

Another reason for optimism is that the quality of available data is likely to improve over time. The development of new and better data has clearly been one of the main achievements of the empirical growth literature since the early 1990s, and one that was not foreseen by critics of the field. Researchers have developed increasingly sophisti­cated proxies for drivers of growth that appeared resistant to statistical analysis. One approach, pioneered in the growth literature by Knack and Keefer (1995) and Mauro (1995), has been country-specific ratings compiled by international agencies. Such data increasingly form the basis for measures of corruption, government efficiency, and pro­tection of property rights. More recent work such as that of Kaufmann, Kraay and Zoido-Lobaton (1999a, 1999b) and Kaufmann, Kraay and Mastruzzi (2003) has es­tablished unusually comprehensive measures of various aspects of institutions.

The construction of proxies is likely to make increasing use of latent variable meth­ods. These aim to reduce a set of observed variables to a smaller number of indicators that are seen as driving the majority of the variation in the original data, and that could represent some underlying variable of interest. For example, the extent of democracy is not directly observed, but is often obtained by applying factor analysis or extracting principal components from various dimensions of political freedom. There are obvious dangers with this approach, but the results can be effective proxies for concepts that are otherwise hard to measure.^[373] They also help to overcome the dimensionality prob­lem associated with cross-country empirical work. To be successfully employed, the rigorous use of a latent variable as a regressor will generally need to acknowledge the presence of measurement error.^[374]

Using latent variables makes especially good sense under one view of the proper aims of growth research. It is possible to argue that empirical growth studies will never give good answers to precise hypotheses, but can be informative at a broader level. For example, a growth regression is unlikely to tell us whether the growth effect of inflation is more important than the effect of inflation uncertainty, because these two variables are usually highly correlated. It may even be difficult to distinguish the effects of inflation from the effects of sizeable budget deficits.⁷⁴ Instead a growth regression might be used to address a less precise hypothesis, such as the growth dividend of macroeconomic stability, broadly conceived. In this context, it is natural to use latent variable approaches to measure the broader concept.

Anothervaluable development is likely to be the creation of rich panel data sets at the level of regions within countries. Regional data offer greater scope for controlling for some variables that are hard to measure at the country level, such as cultural factors. By comparing experiences across regions, there may also be scope for identifying events that correspond more closely to natural experiments than those found in cross-country data. Work such as that by Besley and Burgess (2000, 2002, 2004) using panel data on Indian states shows the potential of such an approach. In working with such data more closely, one of the main challenges will be to develop empirical frameworks that incorporate movements of capital and labour between regions: clearly, regions within countries should only rarely be treated as closed economies. Shioji (2001b) is an exam­ple of how analysis using regional data can take this into account.

Even with better data, at finer levels of disaggregation, the problem of omitted vari­ables can only be alleviated, not resolved. It is possible to argue that the problem applies equally to historical research and case studies, but at least in these instances, the re­searcher may have some grasp of important forces that are difficult to quantify. Since growth researchers naturally gravitate towards determinants of growth that can be an­alyzed statistically, there is an ever-present danger that the empirical literature, even taken as a whole, yields a rather partial and unbalanced picture of the forces that truly matter. Even a growth model with high explanatory power, in a statistical sense, has to be seen as a rather provisional set of ideas about the forces that drive growth and development.

This brings us to our final points. We once again emphasize that empirical progress on the major growth questions requires attention to the evidence found in qualitative sources such as historical narratives and studies by country experts. One example we have given in the text concerns the validity of instrumental variables: understanding the historical experiences of various countries seems critical for determining whether

in the social sciences. Most economists are not familiar with this approach, and this makes the assumptions and results hard to communicate. It is therefore not clear that a full latent variable model should be preferred to a simpler solution, such as one of those we discuss in the measurement error section above.

⁷⁴ As Sala-i-Martin (1991) has argued, various specific indicators of macroeconomic instability should per­haps be seen as symptoms of some deeper, underlying characteristic of a country.

exclusion restrictions are plausible. In this regard work such as that of Acemoglu, John­son and Robinson (2001, 2002) is exemplary. More generally, nothing in the empirical growth literature suggests that issues of long-term development can be disassociated from the historical and cultural factors that fascinated commentators such as Max We­ber. Where researchers have revisited these issues, as in Barro and McCleary (2003), the originality resides less in the conception of growth determinants and more in the scope for new statistical evidence. Of course, the use of historical analysis also leads back to the value of case studies, a point that has recurred throughout this discussion.

In conclusion, growth econometrics is an area of research that is still in its infancy. To its credit, the field has evolved in response to the substantive economic questions that arise in growth contexts. The nature of the field has also led econometricians to introduce a number of statistical methods into economics, including classification and regression tree algorithms, robust estimation, threshold models and Bayesian model averaging, that appear to have wide utility. As with any new literature, especially one tackling questions as complex as these, it is possible to identify significant limitations of the existing evidence and the tools that are currently applied. But the progress that has been made in growth econometrics in the brief time since its emergence gives reason for continued optimism.

Acknowledgements

Durlauf thanks the University of Wisconsin and John D. and Catherine T. MacArthur Foundation for financial support. Johnson thanks the Department of Economics, Uni­versity of Wisconsin for its hospitality in Fall 2003, during which part of this chapter was written. Temple thanks the Leverhulme Trust for financial support under the Philip Leverhulme Prize Fellowship scheme. Ritesh Banerjee, Ethan Cohen-Cole, Giacomo Rondina and Lisa Wong have provided excellent research assistance. Finally, we thank Gordon Anderson, William Brock and Stephen Bond for useful discussions.