Choosing suitable research topics always presents difficulties for researchers. I was interested in food security, so I participated in a research project on the Green Revolution in Asia in the late 1980s. I discovered that the Green Revolution was necessary for reducing hunger but yielded limited employment generation. Therefore, I decided to study industrial development because it can offer employment opportunities to the poor and contribute unequivocally to poverty reduction. In sum, my approach is to first identify critical issues before I conduct careful case studies. I do not want to contend that my methodology represents the only correct stance. However, I would like to highlight the existence of innumerable studies that have selected research topics based on the applicability of advanced research methods.

No Poverty and Zero Hunger

I believe that the achievement of the first two sustainable development goals (SDGs) is the paramount problem development economics must resolve: no poverty and zero hunger. The ideal of zero hunger can be achieved only if food production is increased by employing improved production technology. The goal of ending poverty can potentially be attained through industrial development. As attested by the Green Revolution, increased food production contributed significantly to hunger alleviation in Asia by doubling and tripling rice and wheat production in the 1970s and 1980s. However, the Green Revolution did not exert an equally significant impact on employment. The gain in employment was between 20% and 40% and was subsequently easily erased by mechanization, for instance, through the introduction of tractors and threshers. In other words, agriculture can only generate limited employment opportunities. The reduction in persistent and widespread poverty requires the development of labor-intensive manufacturing industries that can deliver ample employment opportunities for the poor and uneducated. This is why my forthcoming book synthesizes, integrates, and extends my studies in the last four decades, and focuses on the development of both agriculture and industry (Otsuka 2024).

The modern service industry leads some developing economies. Often, the IT-related or financial sectors generate employment opportunities primarily for the educated and wealthy sections of society. Thus, the development of the service industry is not conducive to poverty alleviation. I admit that social welfare programs such as microfinance and conditional cash transfers should function significantly in poverty reduction. Nevertheless, I do not believe that such programs can eradicate poverty on their own. For example, the incidence of poverty declined dramatically in China, not because of the implementation of such social policies but because of the growth of the agriculture and manufacturing industries.

Innovation as an Engine of Growth

Testing the Effectiveness of Training in Agriculture and Industry

It is one thing to argue that innovation is important for the development of agriculture and industry. It is quite another task to show that innovation can be promoted through policy, i.e., means such as agricultural extension activities or management training programs for entrepreneurs. My colleagues and I sought to prove the validity of my arguments. Thus, we applied randomized controlled trials (RCTs) of cultivation training to farmers and management training to entrepreneurs in several countries in sub-Saharan Africa, such as Ghana, Cote d’Ivoire, Ethiopia, Kenya, Uganda, Tanzania, and Mozambique. We confirmed that cultivation and management training programs are highly effective. In other words, trained farmers and entrepreneurs who learned new technologies and management methods would perform significantly better than their nontrained counterparts. Therefore, my new book (Otsuka 2024) concludes that government investments in the human capital of major decision-makers should become the core of effective development strategies to transform poor economies.

Government interventions to train farmers and entrepreneurs are justified because of the spillover of information on innovation or imitation. The private benefits accrued to the innovator from innovation tend to be smaller than the social benefits that accumulate because of information spillover. In other words, investment in innovation tends to fall short of the social optimum because of information spillovers. It would be a mistake to assume that the market mechanism achieves the socially optimum allocation of resources for innovation if information spillovers exist. Government support, in general, is indispensable when a significant gap exists between the private and social benefits of innovation.

Choosing a Research Topic and a Research Methodology

To recapitulate, the criticality of a research topic from the social perspective should be the most important criterion for its selection. I agree completely with Akerlof (2020, p.105) that “economic research ignores important topics and problems when they are difficult to approach in a ‘hard’ way.” Other leading economists (e.g., Deaton and Cartwright 2018; Ravallion 2020) have articulated similar concerns, contending that the choice of research topics is biased if the application of RCT is predetermined.

I have not previously mentioned this point but the significance of a topic can be properly adjudged only if the researcher apprehends the ground realities. Thus, experience in field research and knowledge of ground realities should form integral components of research projects. Therefore, I spent considerable time on informal surveys and literature reviews to identify the socially pivotal issues before conducting empirical studies. The most appropriate estimation method should be selected after the topic is decided. The apt methodology could be an RCT, or natural experiment (NE), or another approach. The publishability of the research paper in leading journals should never be the first criterion for choosing a research topic. I do not want to argue that my recommended approach is the only correct method. However, I anticipate that the next generation of empirical research will be characterized by the prevalence of joint research initiatives that encompass a division of labor among researchers knowledgeable about economic theories, econometrics, and ground realities. As Otsuka et al. (2024) have noted, such transformations seem to be materializing inconspicuously.

References

Akerlof, G. A. 2020. “Sins of Omission and the Practice of Economics.” Journal of Economic Literature 58(2): 405-418.

Deaton, A., and Cartwright, N. 2018. “Understanding and Misunderstanding Randomized Controlled Trials.” Social Science & Medicine 210: 2-21.

Otsuka, K. 2024. Transforming Poor Economies: Effective Development Strategies for Agriculture and Industry. Cheltenham, UK: Edward Elgar (forthcoming).

Otsuka, K., Y. Higuchi, and A. Suzuki. A. 2024. “Challenges in Empirical Research in Economics: The Way Forward.” In Next-Generation of Empirical Research in Economics, edited by K. Otsuka, T. Kurosaki, Y. Sawada, and T. Sonobe, 57-78. Singapore: Springer.

Ravallion, M. 2020. “Should the Randomistas (continue to) Rule?” NBER Working Paper 27554.

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* Thumbnail image: Rice Paddy in Autumn, Toyama, Japan (MIXA / Getty Images)
** The views expressed in the columns are those of the author(s) and do not represent the views of IDE-JETRO or the institutions with which the authors are affiliated.