Authors:
Christopher B. Yenkey – University of Chicago Booth School of Business

Interviewers:
Ryann Manning – Harvard Business School
Stefan Dimitriadis – Harvard Business School

Article link: http://asq.sagepub.com/content/60/4/561

Question 1. We were excited to see your paper was based on research in Kenya, as research on African settings is still quite rare in top journals in organization studies. Kenya seems an ideal setting to examine the questions you pose in this paper, but we understand this paper grew out of your dissertation. How did you decide to undertake dissertation research in Kenya? Was it driven by a personal interest in Kenya or an interest in particular phenomena or theories that you thought you could best study there? Or was it a matter of access to, as you say in your conclusion, “unusually high-quality data”?

Oh, it’s definitely not realistic to head to sub-Saharan Africa expecting easy access to great data! I’ll talk about how I got data access below, but to answer your question, I went to Kenya specifically for the phenomena. I knew I wanted the dissertation project to focus on the social construction of markets, and the global diffusion of stock exchanges caught my eye: more than half of the world’s 200-plus stock exchanges are new since 1985, and the vast majority of these are in developing countries, especially sub-Saharan Africa. It’s one of so many examples of the spread of neoliberalism, but the “if you build it, and if you get the price right, investors will come,” approach failed in most countries, so clearly there is more to be understood in how to mobilize a critical mass of participation in these new markets. Kenya struggled to recruit investors for many, many years, but a wave of new investor recruitment started in early 2006. So Kenya was an example of a market with enough investor recruitment to measure and study, but also with plenty of frictions and failures to juxtapose against. The project was first funded by the NSF as a comparative study of market development in Kenya, Uganda, and Tanzania. But I spent a month at the Dar es Salaam Stock Exchange, and there was so little activity that it would have been hard to develop anything but a journalistic account of what was going on. My phone calls to Kampala suggested Uganda would be about the same. With so much action in Kenya, it became the obvious focus.

You asked if data access itself was part of choosing Kenya. Definitely not- data access was a result of committing to the study, not the cause for doing so. My access to the NSE’s electronic platform actually came at the end of a five-month stint of field work in 2008. I struggled for months to collect enough hard copy records (literally digging through closets and storage sites around the NSE for 3-ring binders) to build a valid empirical account of share ownership at the firm level. Two weeks before the end of my visit, I was offered access to the electronic platform, complete with the town of residence of each investor (which I geocoded and used to measure diffusion). You don’t get that kind of access ahead of time- you have to earn it by building relationships with market officials around shared research questions (which I’ll speak more about in the next question).

Question 2. Do you have any advice or tips for young organizational scholars interested in pursuing research in Africa?

You have to embed yourself. You have to know your context. If you aren’t thinking first about the people and organizations you’re studying, working to see and understand them for who and what they are, then you’re probably thinking first about some other context or earlier research (probably North American) which feels like it’s similar enough to guide your thinking. If you’re doing that, you’re more likely to import a set of foreign ideas to your new context rather that creating a space for learning or discovering new things. If you find that earlier work from North America indeed fits with what you see in Africa, that’s just fine. Africa isn’t the dark side of the moon, and we shouldn’t automatically assume radical differences in decision making criteria. But we also shouldn’t assume radical similarities, either. The best approach is to get a clear, objective explanation for what you see, then use that explanation to either connect with or add to the set of explanations we collectively share in the literature. By doing so, we build a larger understanding of what aspects of organizing are similar and different across contexts, and that is a very valuable.

Much of my field work (January-June 2008) coincided with several critical events in Kenya and at the NSE. Kenya was racked by inter-ethnic violent conflict that teetered on a civil war until late February stemming from a failed presidential election in December 2007 (my university’s risk management department threatened to cut off my funding unless I left, but I eventually won that argument), the NSE was at the height of a push to recruit investors that began in early 2006, a fraud that affected more than 100,000 investors was discovered in March, and the largest IPO in sub-Saharan African history began in April. Many decades of Kenyan social tensions came to a head during my months in the country, and these coincided and even clashed with a concerted market development initiative. As a result, I got more direct exposure to the core issues than would have been possible otherwise. It left me with a sharper understanding of how this society and economy are intertwined, and I try to bring that understanding into my work so that organization theory can help build a broader, deeper understanding of the social foundations upon which markets are constructed. Kenya’s dynamism is repeated elsewhere all too frequently in some form or another. Globally and historically, they weren’t that out of the ordinary, even if they felt extreme to me at the time. My point here is that it’s unlikely I would have been able to provide the kind of explanation of how social relations influence this market unless I had committed to embedding myself in this place at that time. I don’t want to put too fine a point on things, but on my second day in country in January 2008, my wife, a senior NSE manager, and I watched violent post-election protestors being tear gassed by the police from the front window of the NSE. This country was unraveling at the same time they were working to build a market. That kind of raw intensity forces itself into the research. If you are willing to listen, your context will tell you what fundamental issues you need to deal with.

Beyond broadly connecting with the context, I think it is important to think hard about how to connect specifically with local practitioners and policy makers. You need to understand how to get past the rhetoric that forms most of the things they are willing to share with an outsider, and you also need to give yourself the best possible chance to access good data. I did this by positioning myself at the junction of critical questions and offering my help in answering those questions. Locally critical questions are rooted in both time and space. Showing up 5 years after a major event runs a real risk of asking about yesterday’s news- in dynamic contexts you can be studying ancient history after just a few years. When I was in Kenya, they had done a good but not great job of recruiting investors, these new investors weren’t trading as much as expected, and a major fraud scandal was questioning the legitimacy of the market. When I got an interview with the Company Secretary at the NSE (their chief legal counsel), she asked me what kinds of things I was interested in. I told her I wanted to understand how investors were recruited into the market, how they learned to trade more effectively once they entered, and how they reacted to bad news like the fraud scandal. I didn’t push any particular answer, and I didn’t suggest that I already knew the answer. I only worked to show that I was a good enough researcher to produce a reasonable answer to those questions if I had the right resources. Four months (and countless hours of hard work at the NSE) later, she offered me access to the electronic platform, which is the best possible dataset for addressing those exact questions. After I got initial access, I returned many times to present my findings, which at first was mostly a set of maps showing the geographic diffusion of shareholding as their population grew. The pattern it showed gave them an entirely new perspective on how investors were being recruited into their market, and now they had hard facts on which to base policy and strategic planning. Furthermore, they recognized that those facts were a result of giving me access to their data. Over several trips back and forth, I presented more results which led to more answers, and they always gave me access to more parts of their database that made the next set of answers possible. In short, we formed a partnership that is critical to the success of this project.

Question 3. The measure of peer effects that you constructed, based on the profits earned by investors in other villages, and the dichotomization of that measure by coethnic and non-coethnic peers is part of the innovation of this paper. How did you settle on these measures and did you also experiment with alternatives?

Actually, the first submission focused on a different dichotomization: profits earned by peers measured by geographic versus social proximity. I measured profits within a geographic radius irrespective of the social identities of peers and then measured profits of coethnics irrespective of their geographic proximity. My thinking was around comparing the magnitudes of peer effects as they are rooted in these two fundamental pathways for diffusion (spatial and social proximity). My reviewers suggested this was overly focused on existing diffusion theory rather than providing the best possible explanation about how this particular practice spread in this particular context. With the great data, I had the enviable problem of being able to construct any number of possible measures. I spent months testing different measures, looking for the best combination of theoretical power with goodness of fit. Eventually, and again with guidance by my reviewers, I settled on the distinction between geographically proximate coethnics versus non-coethnics was the fundamental process at work.

But the story is deeper than just insiders versus outsiders. A critical part of the paper is comparing the effects of non-coethnics that are rivals versus non-rivals and the local context of where they live and make decisions. I find that profits earned by geographically proximate ethnic rivals actually have a negative effect on adoption of shareholding: paradoxically, rivals’ positive performance impedes the spread of the innovation. Then in a later section, I show that profits earned by non-rivals can reverse this negative reaction, conditional on these profitable non-rivals being better integrated with the rival population. Even before looking at the influence of ethnic outsiders, the data let me show that coethnics were only a positive influence in areas of Kenya where banks and other existing financial institutions were distrusted- that was the source of uncertainty that homophilous peers resolve. The richness of the data didn’t do me any favors in terms of finishing the paper quickly, but ultimately it gave me a chance to provide a deeper explanation of market construction in a context that is exceptionally hard to measure.

Question 4. In several places in the paper, you explicitly address the generalizability of your findings to other settings. How did you think about generalizability when starting this project, and did that evolve during the process of writing this paper and in revising it for ASQ? Do you have any advice for young scholars as they strive to balance a demand for generalizable knowledge with a desire to examine unusual, extreme, or otherwise theoretically generative empirical settings?

This is an important question, and I am very pleased to see the term “theoretically generative” in your question. There is growing (but certainly not unanimous) recognition within organization theory, complete with PDW’s and panels at the last few AOM meetings, that theory development is struggling because the requirement of theoretical novelty for publication is often justified through addressing smaller and smaller elements of existing theory rather than expansion into new areas. I think it’s also a reasonable critique to say that academics often lag behind real world developments in organizing, whether at the individual, enterprise, or national levels. So for this reason, I think there is a lot of room for high impact work to start with important but not well understood empirical realities and then use those lessons to generate theory.

My editor (Editor in Chief Jerry Davis) and my reviewers gave me a valuable opportunity to avoid this pitfall. In fact, they critiqued my first submission for falling into the trap mentioned above. As Jerry summarized in the first round decision letter, I was “forcing the paper into a theoretical straightjacket” by claiming a new theoretical argument around diffusion, which of course has been a mature field of inquiry for some time. One of my reviewers wrote that the value of the paper wasn’t in “revolutionizing diffusion theory”; instead, it was in showing how a well understood process works a bit differently in an important but little understood context (i.e. Kenya, Africa, developing economy, etc.). They supported a non-traditional approach to the manuscript and gave me space to let the exceptional data lay out the empirical lessons of how diffusion worked in this novel context, and use those lessons to identify the theoretically novel and generalizable aspects that would inform organization theory more broadly. I tossed the hypotheses and instead used the data to “peel the onion” and drill down to the core issues. If you like the non-traditional format of the paper, much of the credit goes to my editor and reviewers because they gave me the space to do that. If you don’t like it, blame me (but we’ll have a coffee and I’ll try to convince you).

To directly answer your question, I think it is important to begin a project by thinking about how an important but less understood piece of the world works. Once you have an objective explanation, it should be a more clear process to think about how your explanation relates to others’ explanations of other events. The danger with starting with the goal of producing generalizable theory is that it is very hard to escape the orbit of existing explanations, and therefore the project is set on a path that will likely repeat those that came before it. Finding repetition or generalization can be a good thing- it means we’re finding reliable patterns in the world- but starting with the goal of repetition and generalization limits the possibilities for building new knowledge. Now I’ve circled back to some thoughts in Question 2 above, so I’ll stop there.

Question 5. Your paper is impressive in its scope as well as its rigor, but nonetheless we want to ask you about a possible extension. The period of your fieldwork seems to overlap with the introduction (in 2007) of another financial innovation in Kenya, mobile money, which has since diffused rapidly. Have you considered how the mechanisms that drove recruitment into mobile money markets may be similar or different from the mechanisms that drove recruitment into the stock market?

Funny you should mention mobile money- I have a paper on that! Laura Doering (Toronto-Rotman), Pete Aceves (Chicago-Sociology) and I are looking at how Kenyans use mobile money, which I think is a more important angle than how it diffused. Kenya has the largest uptake of mobile money in the world (about 80% of the general population at the moment), but a big part of that explanation is somewhat unique to Kenya. There was (and still is) one dominant mobile provider in Kenya- Safaricom. When mobile money was introduced around 2007, Safaricom was an unregulated joint venture between the Kenyan state and Vodaphone, meaning that they had lots of creative minds, good tech skills, and no one telling them what they could and could not do. Almost 90% of Kenyans used Safaricom’s system, so it made sense they would send money to each other just as they were sending text messages. The CEO who oversaw this dynamic growth (Michael Josephs, an American) has since moved on to more global initiatives that try to recreate the Kenyan experience, though local conditions in other developing countries are never quite as supportive.

But you asked about the parallels with the stock market, so let me directly address that. I think the most useful parallel is in asking how an economic product/tool/technology (shares or mobile money) can be leveraged to help build a more unified economy amidst a diverse and contentious population. We know that diversity can breed contention and contention can inhibit development. An important part of my ASQ paper looks at how to overcome the impediments of ethnic tensions, asking how Kenyans come to identify as members of a common market rather than as agents of their particular social group. I think a similar question can be asked on an even bigger scale when it comes to mobile-based products. Some years ago, I pitched a proposal to a Safaricom Vice President to get the call, text, and mobile money transaction records so I could map changes over time in these forms of connectivity. The basic question was whether or not the technological innovation was changing the social connectivity of the country, or if it was just more efficiently facilitating connections within existing groups. My proposal was not approved, but I think this is a fundamentally important question to address and organization scholars are well positioned to answer it.

Question 5. What was the most enjoyable and/or unexpected part of working on this project?

So much of this project will be with me for the rest of my personal and intellectual life: experiencing the incredible highs and lows of daily life in Kenya; seeing clearly how informal social institutions fill the void left by weak formal institutions; even learning how to ward off lions and hippos while sleeping in the jungle (learn from my first night’s fear: it’s the smell that repels them, not the flame; a smoldering smoke does the trick, you don’t have to lie awake all night horrified of letting the flame go out).

But the unexpected thing is how well received the project has been by the organization theory community. I did this project because I thought the questions were interesting and important, not because I thought Kenya would be an easy sell on the job market or to the journals. But there is a growing appetite for expanding the scope of organization theory research into non-traditional contexts, and there is more openness to considering how lessons learned in developing countries can help us understand hard to observe attributes of organizations in the developed world. I have benefited from this expansion of attention, and I’m working hard to help it grow so others can do the same if they want.