The Death and Rebirth (?) of International Business Research

My motivation for this essay extends from my three views on the state of international business (IB) research. The world of IB is vibrant and stimulating. Current IB research is not. Managers engaged in IB are energetic, creative and risk-taking. Modern day IB scholars are not. Media stories covering IB are novel, engaging and eye-catching. Recent IB journal publications are not. At its birth, IB research galvanized a generation of inspired scholarship. This first wave of IB research breathed life into our understanding of the multinational corporation (MNC), which until then was characterized as a foreign demon. Unfortunately, the initial success of this MNC focus anchored subsequent generations of researchers to the identical research questions concerning why MNCs exist, how they grow and how they are managed. At the same time that IB research became stultified; the practice of IB became more international, more nuanced and more challenging to understand. The consequence is that I have an intense dislike for new research in IB. In strict counterpoint to the real world of IB, contemporary research in IB is outdated, staid and boring: helpful for sedation, but uninformative for knowledge generation. Contemporary IB research has been suffocated by its fetishistic focus on the MNC. IB research has become detached from new phenomena in the globalizing world. It fails to explore anything new. Further, a stifling fixation with quantitative methods has squeezed the life out of IB research. Notably, the IB scholarly community has been complicit in the institutionalization of these two features of IB research; by making an MNC empirical focus the gold standard for journal publication. If these trends continue, IB research will exhaust its relevancy, with no one other than cloistered academics reading IB research. This descent into a research coma need not happen, nor should it happen. The practice of IB pulsates with never-ending energy. Researchers in IB need to curtail their incestuous pursuit of research by taking their noses out of journals and lifting their eyes away from the seductive numbers on their laptops, to re-engage with the real world so as to connect strongly to modern day trends in IB. The IB research community must eschew convention in research and publishing to develop knowledge and publish research in ways that reflect the novelty and complexity of IB phenomena. In this way, IB research can be reborn and thrive again as a dominant, path-breaking management discipline. The IB research agenda was born in the 1960s and 1970s, with successive sets of work on the MNC by scholars such as Buckley and Casson, Hennart and Rugman, among others. A reader solely conversant with the 21st century IB literature would be surprised to find that this trailblazing research was fascinating in its theoretical and contextual richness. IB's forefathers blazed this trail. They then coerced others to follow it devotedly. In several fresh treatises addressing the future of IB, IB's leading scholars identified the most exciting research themes in IB as MNCs, FDI and internationalization, thereby compelling IB's newest generation of scholars to investigate these same well-trodden research questions. The power of this advice has been profound. In studies of IB in China, IB scholars have been zealously researching alliance formation and MNC investment into and out of China. More compelling issues such as the rapacious behaviour of the local partners of foreign firms, or the fundamental competitive inequities for foreign firms in China, as created intentionally by biased local policy makers, were hardly explored. Similarly, MNC research in all regions of the world has been consistently linked to the sub-themes of entry mode, location choice, entry timing, international diversification, and joint ventures. I would say the list goes on, but it does not. These research topics, which were so exciting to me when I was a PhD student 20 years ago, still constitute much of what we see published today in IB journals. By now, the IB scholarly community should accept that we understand these phenomena. We need to recharge the IB agenda. This recharging is not about adding an extra dimension to culture, or adding two new variables to measures of distance. Adding variables at the margin brings us close to kitchen sink regression. Without question, we can better predict movements in the same tired sets of dependent variables, but at the end of the day, what have we learned? IB researchers are infatuated with a quantification of the world of the MNC. Even at a time when the rest of the academic world questions the value of kowtowing to the 0.05 deity, IB research has sharpened its attention to quantification. Indeed, vibrant debates rage across academic disciplines about p-values and our 21st century deification of 0.051. The debate has swung to a strong critique in our use of ‘p’ and 0.05, which at one time, might have been cast as heresy. Yet, the critics, safe from a modern day reincarnation of the inquisition, have made substantive headway in their efforts to recast how we use, but not abuse, empirics. In this era of big data and p-hacking never has this debate been more relevant. Statistical analysis, good empirics and large data, have a place in IB research. However, the ease of data access, the good nature of data that compels it to cooperate with IB researchers’ hypotheses, and the Windowing of opaque, code-dense statistical routines, have dragged IB researchers away from trying to understand the exciting world in which their studies are situated. Excessive quantification damages IB because the interesting in IB is to be found in new non-quantifiable phenomena. To reduce the seductive power of empirics, we need to understand that very peculiar phenomenon known as the IB researcher. IB researchers often act as if they fear the world of IB. When attending a conference in an exotic location, conference attendees seldom observe anything about the country other than the quality of the hotel's furnishings and the English fluency of the hotel staff. Rather than enriching themselves in the novelty of the country, and learning by exploring the country, IB scholars swaddle themselves in the comfort of the familiar. This behaviour stands in contrast to the curiosity that drove our senior colleagues in the IB field to actively engage with, understand and explain novel IB phenomena. The newest generation of IB researchers, and a good portion of established scholars, now eschews phenomena to enmesh themselves in literature that has become more dated than a rotary dial phone. Where is the curiosity that led Dunning to first explore why MNCs exist, that led Beamish to invest heavily in understanding joint ventures when they were an organizational pariah, that led to the race across numerous research teams in the 1990s to investigate and explain headquarters and subsidiary relationships? Curiosity should be as much an endogenous trait of researchers as an inculcated one. Curiosity is fundamental to academic success. But curiosity in the newest generation of IB scholars manifests itself in the belief that novel inquiry means finding that one missing predictor variable, and then acquiring the statistical prowess to model a simple problem as one filled with endogeneity and sample selection bias, using a statistical routine that consumes more computing power than that necessary for Apollo 8 to circle the moon. This form of research edges forward a debate a variable at a time, with a result that is unsurprising, and appealing to no one. Being unimaginative should not be a precursor to publication, yet true curiosity is absent from the current IB generation. Instead, excitement comes from tedious methodological discussions, spiced with the quantitative word of the week, while the research becomes more incremental. Publishing marginally novel research, and I am being generous here, should be anathema to a genuinely curious scholar. But the trappings of academic life – conferences, low workloads, and the pleasures of being experts on never changing research topics – ossify academics. Even with the pressures to publish, coddled academics eschew risk-taking and let expediency trump creativity in research. The comforts of academic life mute curiosity because the risks in publishing incremental research are low as compared to trying to understand something fundamentally new. Forgoing the new for the expedient is self-serving to the researcher but ill-serves the profession. The world of IB is in a constant state of change. Researchers need to match that change. The world of IB can morph quickly. MNCs from Japan leapt into prominence, and then fell into obscurity. China sat first paradoxically as a country of weak institutions but vibrant FDI, then secondly as one that eschewed economic progress for political self-gain. Business across Europe and the world changes in a day of voting, where Brexit provides no insight to IB scholars other than to show them that media can come up with even more tortured neologisms than academics. The world of global business activity is sited in mutating environments; where borders are ambiguous, innovations spread globally, and where daily life in one corner of the world is tangibly affected by actions in other corners. Yet, how many in our IB community invest time to substantively understand these transformations, to bring originality into IB research? It takes an ostentatious scholar, which is more of an impossibility than an oxymoron, to be bold enough to risk immediate academic career satisfaction, with the ground-breaking endeavours necessary to investigate emergent IB phenomena. Only if we consider new ways to motivate, design, write, and publish can we unleash coddled and conservative scholars to publish research that has curiosity as its core. To guide our new generation of IB scholars on their quest to satisfy their own career goals, while modernizing the knowledge base of IB, we must step back to redefine what constitutes good academic research in IB. Scholars design and execute research, but whether their research is published is a decision that rests with the people who staff positions of power. Senior scholars sit on promotion and tenure committees. They chair hiring committees. They govern academic conferences and edit journals. They define what work is acceptable and what is not. In efforts to seek academic legitimization for IB research by mimicking publication practices in economics, strategy, marketing and other related fields, IB's senior scholars led this shift to quantification. Now IB's leaders must direct the reconstitution of what is valuable academic work. IB's leaders need to encourage a reengagement with IB phenomena. Further, the publishing model needs to be reformed to motivate rich writing that reports present-day phenomena in ways that engage a reader, not enslave the reader to the task of slogging through another heavily templated piece of research. This reformation occurs through three leverage points: context, journals, and the design of research and inquiry. In developing research, we should start with the questions: What did the researchers themselves learn? What was learnt about theory? What was learnt about context? To develop context, IB scholars need to enter the nether regions of the countries in which their research is situated to generate a visceral feel for the important issues of the country. By engaging tactilely with organizations and people in the settings being studied, real learning can occur, and be passed onto IB colleagues through vivid writing about the context. Reporting context adds colour to our writing. We do not want to read another study that quantifies the factors that influence MNC localization. But we will want to read a study that describes in detail how foreign mining companies in Indonesia manage multi-billion dollar investments when formal and informal institutions are opaque, when national, provincial, local and indigenous authorities each pull the company in different directions suited to their own interests, and when the local workforce has deep-seated enmities that lead to physical confrontations and murders. Reporting on context in this way would enable IB researchers to lead, not mimic, research on stakeholder management. Reporting context makes research meaningful for people to read, and thereby provides an opportunity to learn about a novel business activity. The cost is a shortening of a theory and methods sections that are often too long. If our economics colleagues can effectively report their research in 3,000 words, certainly even the most verbose scholars (or more likely not) in management can report theory and methods in 5,000 words, leaving the remaining few thousand words for enrichment by contextualization. Reporting context leads to new opportunities for idea generation. We gain something from a few starred numbers in a nicely designed table of results, but we gain much more from the raw impressions of our colleagues writing about one of the more than 200 countries in which IB occurs. We require key decision makers to mark deep reports of context as an acceptable form of academic inquiry. Journals need to accept such changes. Promotion and tenure committees need to value such changes. Editors need to lead such changes. The IB community is fortunate because it has the power to police and advance its own. Dedicated IB journals such as JIBS, the Journal of International Management, and International Business Review, are independently owned and administered. The ability to make such changes into a publication reality rests within existing power structures, providing leaders in IB facilitate the implementation of such changes. Journals do change. JIBS has changed before. It had a history of publishing pedagogical and career retrospective articles, before narrowing its focus to research articles. But changes in the business field recently have led to increased homogenization across journals. Thick description has been sacrificed for increased quantification. Research Policy is one example of this transition. Likewise, research published in the American Journal of Sociology and American Sociological Review used to be heavily descriptive, before moving to greater quantification. Coddled and conservative scholars must satisfy their curiosity beyond understanding a phenomenon simply from its patterns in large sample data. We need not convert our William H. Greene idolizing econometricians into the next generation of Robert Yins and John Van Maanens. Yet, IB scholars must go out and engage with the real world of IB. IB has a pronounced impact on the world around us. Management and economics faculty are not the only academics to study globalization. Globalization is a staple of inquiry for anthropologists, sociologists and geographers. Understanding IB requires more than an economic modelling of MNC foreign entry. We need to describe how such entry changes economies and societies in the world. The hard disk drive industry migrated from the USA to Singapore, then to Malaysia and China, and finally to Thailand. As this and other industries locate in industrial zones south of Bangkok, what happens to indigenous industries? How do the lives and choices of rural families in the north change in response to the migration of these industries to Thailand, especially amidst demographic trends in Thailand that have led to smaller and smaller families? Much has been written about the exodus of service workers from the Philippines to SE Asia, the Middle East and other countries. The associated remittances have been well studied, but what has such a large-scale internationalization of the local workforce meant for Philippine society? Children lose one or both parents for years. The definition of a family changes. A culture of dependency descends on the home village of the overseas worker. This in turn has ramifications for the attractiveness of the Philippines for FDI and trade. IB research in the 2000s has had a focus on institutions. The level of abstraction is high. Numbers measure the quality of institutions, which are then connected to a suitable dependent variable. This form of inquiry yields minimal insight. What do we really know about the functioning of these institutions? Singapore, for example, scores highly on legal indicators, moderately on political indicators, and poorly on transparency indicators. But when one sits in a law court in Singapore, it becomes very clear that robust legal institutions strongly favour the state over the individual. Legal representation during police questioning is not a right, the state can hold individuals indefinitely pre-trial, whether they are the accused or a witness. Individual freedoms and rights are less prevalent in Singapore than in other countries ranked lower on legal institutions. Meanwhile in Vietnam, the baby boom generation has reached its 20s. Changing attitudes between this generation and elder generations are sparking a cultural revolution akin to that in the United States in the 1960s, not like in Mao's China. Social attitudes are liberalizing rapidly. Values, morals and desires have leapfrogged centuries, moving from the 19th century to the 21st century in the span of a generation. Baby boomers in Vietnam covet cultural, lifestyle and entertainment products from South Korea, Japan and the USA. Wealthy, educated and worldly individuals populate the Middle East. Yet, outside of the oil industry, the level of internationalization of society and business trails that of other developed economies elsewhere in the world. Regionalization that eschews internationalization is a prominent theme in this region, yet published IB research says next to nothing on this topic. 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