Boundary-expanding OR/OM Research

For a large part of my academic career, I have let my interests rather than methodologies guide my research, and learned and applied a wide array of methodologies needed to model and analyze interesting problems. In this article, I will share with you a specific route that resonates with me most in my pursuit of research – finding research that crosses some boundaries or domains. In particular, I’ll discuss some general thoughts on how to find research directions and my experience in working on what I consider new, domain-expanding research projects, including the risks and rewards, and lessons learned. I hope my experience can provide insight and encouragement for researchers, especially junior ones, to work outside their comfort zones. 

The OR/OM Landscape

If we think about who we are as operations researchers, and what we contribute to society, the framework that has guided our research typically looks like the following: We can try to enhance some existing methodologies, e.g., optimization, applied probability, stochastic models, applied statistics, etc. However, those theories have been around for a long time and, unless you have already invested heavily in a specific methodology, it is probably hard to make a significant progress. The most exciting opportunities probably lie in applications, regardless of research background.

Alternatively, we can use our methodologies and modeling skills to work on new or existing problems, including those from other fields. Most applied work falls into this category. We have seen economic models for contracts and mechanism design, statistical and machine learning tools for business analytics, and applications of game theory, computer science, behavioural economics and bandit algorithms applied to operations management (OM) problems. Multi-armed bandit models and algorithms combine data, models and analytics (minimize regret). It is both art and science, and can be more powerful and efficient than the traditional approach: data, model, estimate, optimize and apply.

We can also look for applications that have not yet been explored, which is the focus of this article. These opportunities often emerge due to technological changes and are often at the intersections between OR/OM and other fields such as finance, marketing, economics, and even some hard engineering disciplines such as computer science and electrical engineering. According to Harold Larnder [1], operations research (O.R.) emerged or was conceived as a science of operations in the early years of World War II. An O.R. group was established to defend Britain from air attack and was composed almost entirely of scientists who had previously been engaged in the development of radar. Research on demand and supply analytics is motivated by two-sided marketplaces or platforms enabled by marketplace technologies (basically software). Websites such as Airbnb, Fiverr (for freelancers to offer services to customers worldwide), eBay and Uber bring buyers and sellers together to create and exchange value. These platforms make it significantly easier, faster and cheaper for both sides to find each other. Research on fintech (financial technology) is motivated by an emerging industry that uses technologies such as the internet, mobile devices, software technology or cloud services, and blockchains to perform or connect with financial services. 

Therefore, following emerging technologies is a way to identify new O.R. applications, which often require new models and/or approaches, and have great research potential due to its domain-expanding nature.

The Evolution of Research Domains

O.R. and OM have brought about significant improvements to operations in diverse domains, including military, manufacturing, services and the knowledge economy. Every technological advance in the modern world has been met with the pursuit of new models by the OR/OM community, often providing fundamental understanding of, and significant improvements to, its deployment. 

With increased complexity of production and manufacturing largely as the result of the Industrial Revolution, early OR/OM research aimed to improve productivity through more efficient use of resources. Thus, early research focused on inventory, scheduling, assembly lines, capacity, quality and reliability, etc.

With the digital revolution came the mass production of semiconductors and its derived technologies including computers, mobile phones and the internet. In the 1980s and 1990s, a great deal of effort was directed to semiconductor manufacturing (stochastic scheduling, random yields), logistics and supply chain management.

With the internet boom came the information age with abundant data and cheap computing power. Early this century, OR/OM researchers shifted efforts to service industries such as healthcare, call centers, financial services (financial engineering), pricing and revenue management.

In today’s knowledge economy, growth is dependent on the creative use of information and technology rather than on physical means of production. Research shifted to new problems on social network and the sharing economy (e.g., two-sided markets), mechanism design (not between suppliers and manufacturers, but among platforms, service providers and users), fintech (e.g., shadow banking, blockchain) and EdTech. 

Broadening OR/OM Domains: Methodology Driven vs. Problem Driven

There are two approaches to finding new applications that broaden the OR/OM domain. All researchers have a set of tools that they are familiar and comfortable with (e.g., math programming, complexity analysis, inventory theory, robust optimization, queueing theory, heavy traffic analysis, statistical analysis, machine learning, etc.), all of which have wide applications. Finding new applications to apply those tools directly is ideal. However, if you constrain yourself by the methodologies, you may miss some opportunities. Another approach is to worry about the methodologies later and go for new and relevant problems that interest you. I have used the second approach several times – ideas first, methodologies later. You can acquire the methodologies by yourself, or collaborate with the right talent. I often work with different people who have complementing rather than duplicate skills and interests. If you have interesting ideas, you will be able to find good people with the right skills to embark on a new journey with you. 

Rewards and Risks 

There are many benefits to conducting domain-expanding research. You get to work on something truly of interest to you. It is an opportunity to learn and reinvent. Throughout a long career, it is necessary to reinvent many times in order to maintain a certain level of curiosity and stay productive, and perhaps even create funding opportunities. Referees for research grant proposals love new ideas. All of the domain-expanding projects that I participated in, e.g., operations in wireless communications [2] and blockchains [3], were granted funding. Such projects have the potential to make high impact and receive many citations. My work with John Buzacott (2004) on joint inventory and financial decisions [4] is the most cited journal article for both of us. In summary, I view this approach as a way to advance careers and the OR/OM field with meaningful and relevant new work. 

High rewards always come with high investment and risks.

• There is a high setup cost for obtaining the domain knowledge, identifying a new model and possibly acquiring new methodologies.
• Such papers are much harder to get accepted in top journals. Unlike well-recognized problems, there will be a lot of questions about the motivation and its relevance. Even if referees find the problem interesting and relevant, there will be questions about the model and results. For instance, contributions often are more about the ideas and modeling, rather than the methodology, which may be fairly unsophisticated in the eyes of an OR/OM expert. The Buzacott and Zhang 2004 paper had been rejected by many top journals (Management Science, Operations Research, M&SOM) before it was eventually published eight years after the project started.
• If a paper is accepted, it may still take a long time to be discovered or never “take off,” even if it is interdisciplinary and provides new insights. This is especially true if the paper does not make it into a top journal.
• Due to the long and uncertain review process, typically many years, researchers are reluctant to continue along the same line without knowing how the first one will turn out. By the time a paper is accepted, possibly after several rejections, it is likely that you have moved on to something else, hoping that someone else will continue the work you started in the initial research paper. However, this is less of an issue today. Researchers were once expected to establish themselves as an expert in a specific area, allowing them to continue to publish similar work in top journals. Now, more and more graduate programs emphasize the breadth of one’s research, and it is almost impossible to publish similar work multiple times in the same top journals.

There are, however, ways to mitigate these risks. (Most of my research that followed in this nature eventually got through the review process and was published in top-tier journals.)

• Always have more traditional research going on while you pursue a new project. 
• If you intend to publish your work in an OR/OM journal, you need to articulate its boundary-breaking nature and relevance to the field. I always approach this type of work as studying the operational issues in a new application, which fits into an OR/OM journal. 
• Having the support of journal department editors is critical. Try to select a department editor who is willing to make a tough decision. We are grateful to Bill Lovejoy, former department editor of Management Science, for his belief in and firm support of our work (Buzacott and Zhang, 2004). There is some good news recently with the top journals in our field advocating new and risky work by establishing fast track, top-down review processes for such work. 
• Make a judgment on whether to involve a graduate student due to possible risks, e.g., a long and uncertain review process.

Conducting problem-driven and domain-expanding work can be one of the approaches to finding interesting, new, relevant research ideas that have the potential to make a significant impact in our field. Through such projects, you learn new domain-specific knowledge, introduce new models, and may even acquire new methodologies. Pursuing such projects is not without risk, but it is an effective way for a researcher to reinvent themselves and add to a fulfilling career.

References 

1. Larnder, 1984, “OR Forum - The Origin of Operational Research,” Operations Research, Vol. 32, No. 2, pp. 465-476.
2. Wu, J. Zhang and R.Q. Zhang, 2018, “Management of a Shared Spectrum Network in Wireless Communications,” Operations Research, Vol. 66, No. 4, pp. 1119-1135.
3. He, G. Zhang, J. Zhang and R.Q. Zhang, 2010, “Blockchain Operations in the Presence of Security Concerns,” under revision.
4. A. Buzacott and R.Q. Zhang, 2004, “Inventory Management with Asset-based Financing,” Management Science, Vol. 50, No. 9, pp. 1274-1292.