Abstract
Kathleen Eisenhardt made numerous theoretical and methodological contributions to the fields of entrepreneurship, organization theory, and strategy. This interview focuses on her perspectives on how organizations in high-velocity environments can navigate technological uncertainties in fast-paced markets. In addition to clarifying her research contributions, she provides rare insight into her own academic development, her belief in teaching and mentoring, and her stance on intriguing issues future research should address.
Introduction
In today’s fast-paced world, constant environmental changes require quick strategic decision making and continuous renewal of capabilities. Kathleen Eisenhardt has devoted much of her academic career to studying how organizations and entrepreneurs cope with such dynamism. At Stanford, throughout her PhD and as a professor, she witnessed the technological disruptions in Silicon Valley and the renaissance of organization theory firsthand, which both heavily influenced her intellectual development. Keen to investigate the context of high-velocity industries, her work shed new light on boundary conditions around traditional economic activity. Today, she is renowned for having focused attention on the complexity and speed of technological development as contingencies to traditionally held beliefs about organizations. In nascent, fast-paced markets where classic theories do not necessarily hold, she had the merit of using unconventional approaches to generate new theories. Rather than limiting her research, the newness of the topics spurred her to push the frontiers of qualitative research. Her efforts created a framework and guidelines for case-based qualitative studies in the field, offering an invaluable instrument for inquiry which has, to date, received close to 45,000 citations (Eisenhardt, 1989).
This article is dedicated to Kathleen’s scholarly contributions in an effort to bring the academic community closer to one of the founding scholars of our field. In addition to honoring her academic achievement, we celebrate the 20th anniversary of her groundbreaking article “Building Theories from Case Study Research,” an influential paper that legitimated qualitative research methods (Eisenhardt, 1989). We interviewed Kathleen at Stanford’s Department of Management Science and Engineering in October 2016. What follows captures the essence of the conversation, allowing readers to see the genesis of her scholarly approach, as well as her perspective on rigor, relevance, and endurance in the academic environment, and on future research opportunities. As such it provides valuable insights for academics in the early stages of their career.
On the Influence of Stanford’s Organizational Theory Renaissance
In the late 70s, you witnessed Stanford’s organizational theory renaissance. Agency theory really took off around that time, and so did others such as institutional theory, resource dependence theory, learning theory, and population ecology. How did that time at Stanford during your Ph.D. influence your work?
At the time, I don’t think any of us students appreciated what was going on. We used to have an annual conference down at the beach and there was one year when we had the working paper for population ecology (Hannan & Freeman, 1977), the working paper for resource dependence (Pfeffer & Salancik, 1978), and Meyer and Rowan’s working paper on institutional theory (Meyer & Rowan, 1977). Those were the three big papers, and I don’t think we really recognized what a time that was.
I think that time certainly taught me about the role of different kinds of theory and underlying assumptions within the theories that drive their propositions. Although I’m not sure whether I was always theoretically oriented, I think I became more theoretically sophisticated and aware of the power of theory.
On the Silicon Valley Effect
You also witnessed the rise of technological ventures in the Silicon Valley that evolved in parallel to this theoretical renaissance. How did you realize that this proximity to Silicon Valley could feed into your research?
My dissertation on the agency theory was actually done at the Stanford Shopping Center. My nanny and I went over and collected data. Then I started doing work on strategic decision making. My colleague Jay Bourgeois and I were debating whether to study banking, which was undergoing disruption, or the computing industry, which was undergoing disruption with microprocessors (Bourgeois & Eisenhardt, 1988; Eisenhardt & Bourgeois, 1988). As I was in the engineering school, I thought it would play better if I worked on computing, not banking. When we started, we realized what an incredible goldmine the tech sector was, because it was a setting where a lot of the static theories—like agency theory or transaction cost theory—really didn’t play out.
Were there any particular challenges of studying the fast-paced entrepreneurial context?
If you’re studying newer companies and firms that are young, and because a lot of the sector is always changing with mobile and social media, it is fairly easy to get access. I’m mostly a field researcher, and I see that executives in companies which are moving quickly and are new on the scene enjoy being studied for a variety of reasons.
How do you see theories that are developed in these fast-paced markets also enrich theories that are about organizations more in general?
Even among mature organizations like Unilever, General Electric, or Johnson & Johnson, the best organizations are blending traditional businesses with newer businesses. Understanding how high-velocity environments work and what you have to do organizationally to compete in them does play a role when managing those companies. The theories that came about largely at Stanford in the late 70s, like institutional theory and population ecology, didn’t have a lot to say to managers. I had less impact on theories like those because they were about organizational environments. They weren’t theories about managing, organizing, and running stuff.
On Simple Rules
Organizations in fast-paced environments have to be rational yet quick in how they make decisions (Bingham, Eisenhardt, & Furr, 2007) and use simple rules to react in a structured way (Bingham & Eisenhardt, 2011). This can be applied to tackle complex problems even outside the world of academia (Sull & Eisenhardt, 2015). Can you briefly outline the origins and development of that idea for us?
It came from work that I was doing with Shona Brown almost 20 years ago (Brown & Eisenhardt, 1997). We had identified the ideas that would be the basis of complexity theory—the notion that adaptive organizations are partially structured and constantly changing. As we developed those ideas, we started to realize that part of the constant adaptation was structural. We also saw that the more effective executives weren’t falling back on routines when everything they saw was new all the time. More adept executives were actually using pretty simple tools—in fact, simple rules and heuristics.
Later I did some work with Chris Bingham (Bingham et al., 2007) where we actually went into companies. We saw that established companies typically have too many rules, never too few. Chris and I then studied entrepreneurs. Their problem is typically that they have too few rules. We were studying internationalization efforts and started to realize that some entrepreneurs would go from France to Germany to Italy to Singapore and not learn anything generalizable across these countries. They would learn that the French like wine and Germans drink beer—that wasn’t particularly generalizable. More astute executives were coming up with heuristics and were taking lessons from one place and applying a small number of them to new places. Over time, they would make those lessons, those rules, more accurate and often more abstract.
How does decision-making with simple rules compare with the decision-making process explained by Professor Kahneman and Professor Tversky (Kahnemann & Tversky, 1979)?
Kahneman and Tversky obviously have been hugely influential, with Danny winning the Nobel Prize. I also knew Amos—we were soccer parents together. However, they had a very negative view of decision-making and heuristics. They were anchored on innate heuristics that we all use to save time and looking at ways in which those heuristics were dysfunctional. To understand the research, you have to consider the time it was done and what it was in reaction to. Kahnemann and Tversky’s work was in reaction to rational economics. It was also very lab-study oriented—taking people out of their natural surroundings where they might actually have really good heuristics, and putting them into a situation where they aren’t really going to have very good heuristics. It was sort of useful at the time, but things have moved on to a more positive view on decision-making: that people in their natural surroundings can actually be quite effective. The Kahneman and Tversky heuristics and simple rules actually do fit together. The heuristics are often where people start in their real life, and if they are paying attention they typically improve these heuristics to become simple rules. So there is a transition there.
Professors James March and Michael Cohen also worked on strategic decision-making, and came up with a model that is sometimes seen as controversial: the garbage can model (Cohen, March, & Olsen, 1972). How does this view of strategic decision-making by simple rules compare to the garbage can model?
I enjoy the garbage can model. I actually teach it. The model is about a world that is highly fluid and uncertain. It is an extreme description of that world and is a reminder to students of the role of timing and luck. That said, I think simple rules is a more proactive and performance-oriented way of thinking. You can do a better job deciding and getting things done by having some rules—simple rules, not too many, not too few, and pretty good ones. I, in my own work and in my own teaching, make it normative. Some rules are better than others. But the garbage can model is fundamentally not normative. Description is great, but relevance is important and description alone cannot quite achieve that. I think the garbage can is clever and I think it’s interesting, but of limited value in real life—it’s more cute and less impactful. It is also somewhat reflective of some of Jim’s experience as an administrator, which he never went back to again, so it may reflect a discomfort with being effective.
You published a book called Simple Rules: How to Thrive in a Complex Environment (Sull & Eisenhardt, 2015). Can you tell us what is it about this topic that makes it important for a wider audience?
I was motivated—for once in my career—to write a book that wasn’t for academics, a “Malcolm-Gladwell-type” book. It turned out that Malcolm Gladwell writes better than I do—there is a level of professional writer that most of us in academia are not, a phrasing and a spin that a truly outstanding writer can do that Don and I couldn’t do. We almost got there. “Simple Rules” was very popular and we were a Wall Street top 10 read for the summer and Bloomberg’s nerd book of the summer—but we didn’t quite crack the top 10 New York Times list, which was my personal stretch goal. I don’t think it was the topic, I think we just didn’t quite have that level of writing that it takes to do that. But it was really fun to be interviewed on a beer and sports show and the New Age show and have libertarians like Rand Paul say “We loved your book.” It opened up of all kinds of parts of U.S. society over TV and media that I don’t normally travel in. It was really interesting. I wouldn’t do it again, but I’m glad I did it.
Perspectives on Inductive Research: Qualitative Research, Simulation, and Big Data
Your seminal piece from 1989 on case studies (Eisenhardt, 1989) has 40,000-plus citations. Why do you think it became so influential for researchers?
It did a couple of things. My work to some extent legitimated the method. I do not mean to say that Glaser and Strauss (1967)—who I was obviously building on—weren’t legitimate; but they weren’t well known in our field. They were maybe also writing a bit more obscurely than I was. People could cite me and say that their work was legitimate—it had the value of being a roadmap that people could follow. The method also took off because it lets you answer certain questions that you can’t answer econometrically, yet it didn’t have a math barrier. A method I’m playing around with now is formal models, and formal models have a massive math barrier that people just won’t go over, whereas cases didn’t have that barrier. Good case study inductive people are good writers. You don’t have to be an amazing writer—you just have to be a good writer. It opened up a whole research realm for people. It was a very accessible method and becoming legitimated—I helped people see a path for doing it. I think was the confluence of those things as to why it took off.
Some challenges are particular to the qualitative research method. One might be conflict of interest—when you approach an organization, it ultimately may not be in their interest for the findings to be shared. How do you deal with that?
Companies or executives let you in because they enjoy being studied or because they want to help education. Or maybe they’re affiliated with Stanford, or they want to find out about themselves or want to benchmark themselves. You go in with all of those possibilities and then figure out what it is they want and then sell that. Usually they don’t let you in if they don’t want you there for one of these reasons. We always offer feedback and our results to the companies. The executives at the good companies always want to know, and the bad companies never want to know—I don’t know why that is, but that’s empirically true. I don’t feel that I ever have a conflict of interest. Bias is a different question.
How do you tackle bias?
The bias is trickier. I usually try to have a lot of data from a variety of points of view. For example, when Sam Garg and I (Garg & Eisenhardt, 2017) were studying boards, we had the CEOs, board members, top management team, and had data on them over time—observational data, interview data, some archival data. I try to have a lot of data. The data are what keep you honest; you can’t pretend something was there if you can’t build up the data and show that it was. Just as math creates honesty in a formal model, data creates honesty in inductive research. I think where the bias comes in is probably my choice of topic.
You have also published to clarify some of the misconceptions that qualitative researchers have dealt with (Eisenhardt & Graebner, 2007). Do you think there are still misconceptions that qualitative researchers struggle with?
Yes. There are struggles in dealing with deductive researchers. The biggest challenge is having the mainstream econometrics people understand theoretical sampling versus random sampling, i.e., that you are choosing a case for some theoretical reason, for instance, because it fits some theoretical category that you are trying to fill. For example, you’re sampling a really good firm and a really bad firm, and you’re skipping the middle, which is not a random sample but allows you to see the extremes and the contrasts between them. That is a fundamentally different way of thinking that econometrics people are not used to. You periodically have to remind them that you are building a theory and the correct comparison is with armchair theorizing, or maybe with formal models. It’s not a comparison with proofs—you have to remind them of that.
I think the more difficult audience is within the qualitative camp, and there are unhelpful arguments which become more ideological. Those, I think are more problematic, for example, how grounded theory building is really only for interpretivists, which I think even Abraham Strauss disagrees with. People get hung up on writing format in the sort of qualitative inductive work—who gets to do grounded theory building—and on telling the journey of how you got there. Twenty years ago inductive research methods were super short. Nobody was telling you the story of their life as they did the research. What you want is a theory with well-defined, well-grounded constructs, logical connections between those constructs that are theoretically robust, with theory grounded in data about something interesting—that’s what great research is about. These superficial arguments are taking us away from what unifies authority or unifies interpretivists or unifies people like me who are more realist, or even, dare I say it, positivist in their point of view. We are all doing a lot of the same things. Whether we’re doing a good job or not is around Is the theory strong? Is it grounded? Is it interesting? And that’s kind of it.
In your ASQ piece with Professors Jason Davis and Christopher Bingham (Davis, Eisenhardt, & Bingham, 2009) you used simulation methods to probe how simple rules and organizational structure improve entrepreneurial performance, which complemented your previous work based on case studies. How do you think this interplay between simulation and case studies enrich our understanding of research?
I’m a fan of doing that. Simulation was something I had done as an undergraduate and I never did for a long time, but I thought it was really interesting. Jason was my doctoral student and quite good at simulation. In our paper (that won the ASQ contribution award), we could see the interplay between the fundamental ideas that came out of simple rules and then that simulation. What do simple rules look like in a high-velocity environment, a high-ambiguity environment, a high-complexity environment—how does that play out? We could play with basic ideas in different environments in a way that you couldn’t have done in real life or with cases. We also wrote a methods article at the same time (Davis, Eisenhardt, & Bingham, 2007). If you read that article and my 1989 article on building theories from cases (Eisenhardt, 1989) you’ll see a high degree of structural similarity since it was the same process in a sense. It was a very synergistic interplay of method and theory and fun.
Could other combinations of methods fulfill a similar task? Have you thought of other pairings?
There’s the case and the econometrics. Ben Hallen’s dissertation was about fundraising by entrepreneurs; more theoretically it was about how do low-power actors begin their networks. The original work was actually the fieldwork, where he interviewed entrepreneurs about the strategies they used to raise money. He realized that depending on the entrepreneur there were two different strategies: if you were already a well-known entrepreneur or if you were a nobody. He saw that in the cases and built up a data set where he tested that. That was really an example of being able to unpack the behavioral tactics in the cases, seeing it, and then testing it econometrically.
I’m currently working on a methods paper on formal models with one of my students, Douglas Hannah at University of Texas, who is writing a couple of formal models. He’s got a case dissertation on solar system ecosystems, but also formal models that unpack very narrow aspects of ecosystem performance. I’m very big on crossed method research, although I don’t know if any particular individual can be poly-cross method.
On Striving for Relevance and Impact in Research
Your research clearly has implications for managers. There’s a lot of debate about relevancy and impact in our field. What does it mean for you and how we should strive to be as relevant as possible as scholars?
There used to be a rhetoric around “you are either rigorous or relevant,” and I always thought that was wrong. I thought the really great research was both, and I always strive to do both. I think relevance is important. I think something is relevant when people in the so-called real world don’t know the answer, are interested in the question, and believe what you say.
There was a time when I set a goal to have an article published in ASQ and the Harvard Business Review, to take the same research and put it in those two premier places but in different worlds. I did do that—and I’ve done that a number of times—and that’s my personal way of how I think about it. I don’t think that’s a good goal for a junior researcher or that’s a great idea pre-tenure, because people think that you’re still learning how to do the research part. But as you go into an associate and certainly as a full professor, one does want to be relevant. In particular, in professional schools it’s part of our job to be relevant.
You get a lot of recognition for excellence in teaching. What is your philosophy in the classroom?
I take teaching very seriously. Our students have a big opportunity cost to be here, and you owe them the best you can do. My philosophy is that I pack all my teaching into a certain time period, doing all my teaching in the fall and I don’t really get much research done. I split the two activities. I think it’s very difficult to do research even if you’re doing only a little teaching. My philosophy is also around multi-method. When I am teaching undergrads, I may teach the same concept with a lecture, with a role-play, with some sort of exercise such as watching a movie—I mix it up.
I am also a believer in teaching theory. It’s what carries people from today’s example on for the next ten or twenty years. In strategy, I do teach cases since I have demand from students to make them current. But there’s always an underlying theory and we talk about what the assumptions of the theories are. Ten years ago I might have talked about Cisco; today I talk about Air BNB—but the lesson is still the same and on the same theoretical point.
On Overcoming Challenges as a Female Scholar
With your scholarly success you are a role model for younger academics. Who were your role models over the course of your career?
I didn’t have a role model because there was nobody to model. There were older men, who hit it off with younger men, and that wasn’t a spot. The one role model I had was a former provost here at Stanford called William Miller who, as he progressed in his career, started giving back to the university and doing more administration work as he got more senior. He was someone who wouldn’t even show up on the radar of our field. I think I might have wanted a role model but there wasn’t anybody to model on. I sort of figured it out on my own. Bob Sutton was a big help. He wasn’t really a role model—he was my colleague—but he was very helpful to me and I, hopefully, was helpful to him. Certainly, I saw the way he worked, and I got some idea of what to do.
Were there were any challenges you faced as a female academic?
I had kids. I started grad school with one. I had a second one in grad school, and that takes time. There is no ideal time to have children—it’s never convenient, it’s something not everyone wants, but many of us want. That was a challenge that my male colleagues didn’t have. That may be less true now, but that certainly was true when I was starting out.
There were also challenges around some of the older men paying more attention to men. You’d be in a conversation and the men would talk to other men while you would be kind of sitting there. It was a little odd, but I think a lot of that is gone. I’m hoping that the world is better for women at this point. You don’t have to put up with some of those things. You probably know better than I do.
Was there a certain way you overcame that?
No. I decided that there were advantages and there were disadvantages. There were times when I’d be singled out and profiled as being the woman. I decided to take advantage of that and enjoy that. I figured there were good things and bad things, and it didn’t do me any good to worry about the bad things. Better to exploit the good things and move on. I also went part-time for a few years. That was really useful to me. When my kids were little, I was just too busy not to do that.
Simple Rules of Academic Life
A particularly productive way for academics to contribute to research is fostering curiosity among junior academics. Kathleen Eisenhardt has taken this role seriously, mentoring researchers in their early stages of their career—as doctoral students—with an eye for academic talent. We took the opportunity to tap into her knowledge.
Would you change any advice that you have previously given to students, either because it’s not up to date or it turned out to . . .
. . . not be so good? Yes. I used to say “Make sure your paper is perfect before you send it for review. Really get it right, and then you get a much more consistent set of reviews and you get a much higher probability of publication.” The review process is now more random, so now I say: “Get it pretty good, and send it out.” I would have never said that 10 years ago. The process feels much more random to me, much more about the particular three people that you’ve got as your reviewers, so I have come to think it’s better to find out sooner if those three people are going to be your new best friends or not. Make it good, but don’t make it perfect. Get it out there.
Can you give us a set of simple rules for students today?
[laughs] I’ll give you a couple. Three papers make a stream. And you don’t have to love your dissertation to be successful—just get it out. Agency theory, when I was a student, was really taking off. It was all formal models and I said, “Wait a minute. We can actually test this pretty easily.” I figured out how to test that. My dissertation was among the first empirical studies [on agency theory]. That said, I never really liked the theory. It wasn’t my style—it was static, it was way too economics-oriented. But it was a question of getting it done. It was straightforward to do—I had two little kids—and I just did it.
Bob Sutton had this mantra “Three papers make a stream”—so never write fewer than three papers about topic X. That convinced me to push the agency theory into three papers (Eisenhardt, 1985, 1988, 1989a, 1989b), which was helpful because then I became associated with agency theory, and that was a big part of my tenure case. I continued to get manuscripts to review even though I never liked the theory. Once I did my three papers, I was gone. I was never going back to the agency theory.
Not trying to make it perfect. I have seen doctoral students who get so wrapped up in making it be perfect, so reluctant to share their ideas early on until they are perfect. I remember being that way. I wanted to be good, I didn’t want to be criticized—but you have to get it out there, get in the marketplace of ideas, find out if it’s working or it’s not. Sometimes you’ll think something is going to be really great and nobody else thinks it’s interesting. That’s how complexity theory happened. . . I thought that was so great, and it has been pretty good, but not as great as I think it is.
Try out ideas with people. I learned this from Jeff Pfeffer, a really smart guy, on what to do in terms of marketing. Let’s say in a case study where we have three or four or five findings, I’ll try them out with people: “Here’s our research question—what do you think we found?” I’ll find out what people naively think and then reflect on my own stuff. “Did we find that?—Yeah, we did.” In that case we can already tell that that finding is probably not interesting. Then I’ll say “This is what we did find. Tell me what you thought was cool and what was not.” This is how you start to realize what is interesting—because you’re not that good a judge yourself. It’s what other people think that becomes interesting. Try to understand what findings are really bouncing out, what ideas did they like, what metaphors are really catchy. I guess I’d call it market research, but it’s important to sense what’s working for people. . . and move on to what was really interesting.
What’s Next?
What do you think is going to be the next big puzzle, what are you curious about?
International and developing countries—less Europe, less North America. China is getting a little overrun because there are so many Chinese people studying China, so maybe you need [to study] a different [country]. Indonesia, for example, is an amazing country. . . sort of similar to the United States with a population of around 300 million people and even similar scale in terms of their geography—3,000 miles across.
In the more tech world, we’re just getting started. Think about platforms and ecosystems and how they operate. In the micro world—and this is not hugely new, people have been picking up on it—managing people who are not your employees, like Airbnb, Uber, Lift. I just moved that notion into my undergrad class on organizational behavior. How do you motivate people who don’t work for you? In student organizations they need to motivate people that aren’t employed all the time, but it is new in business. A lot of my work is driven by what my students are interested in. I play with what are they interested in, what’s new, and how to put those together in an imaginative way. Like Spotify and how Spotify is disruptive. . . the interplay of rights and social media. . . there could be some really interesting things to study in there.
I am not sounding very theoretically driven. I’m more of a phenomenon person, although I still go back to theory. For research topics, I guess I would like to make it about why it is more exciting to me and why it drives my research. I think theory is important and I apply theory in class, but I like to make it about phenomena on the research side.
Conclusion
In this interview with Kathleen Eisenhardt, we explored her perspectives on qualitative research in fast-paced environments. She shares her personal experiences of how she studied entrepreneurial firms in nascent markets and emphasizes some distinctiveness characteristics of qualitative research such as the notion of theoretical sampling. She further enriches our understanding of best research method practices by giving us suggestions on how to beneficially pair case study research with other research methods such as simulations, deductive studies, and formal modeling.
We also learn from Kathleen Eisenhardt’s perspectives on simple heuristics to follow in academic careers—the importance of getting ideas “out there,” the benefits of not seeking perfection when submitting articles, and the relevance of building an identity through the mantra “three papers make a stream.”
Through her sharing of her experiences of being a female academic throughout her career at Stanford and an advisor for many PhD students who now have become renowned scholars, Kathleen Eisenhardt also presents valuable lessons for junior researchers around the world. Suggesting more research on new forms of business phenomena, she shares a contagious academic spirit that we hope is conveyed to the readers of this article, triggering intriguing future research endeavors.
Footnotes
Acknowledgements
First, we particularly thank Kathleen Eisenhardt for making time, providing valuable lessons, and allowing for interesting insights throughout the process of conducting this interview. We thank her prior students Jason Davis, Henning Piezunka, and Charles Galunic for providing comments in the preparatory stage of the interview. We also thank INSEAD, Afonso Almeida Costa, Sunkee Lee, Sorah Seong, and Maciej Workiewicz for providing help throughout the interview process. Finally, we thank Steven Schecter for shooting and editing the interview in the film format.
Authors’ Note
The first two authors contributed equally.
Declaration of Conflicting Interests
The authors declared no potential conflicts of interest with respect to the research, authorship, and/or publication of this article.
Funding
The authors received no financial support for the research, authorship, and/or publication of this article.