Before jumping into a discussion of issues related to the processes facing an emerging entrepreneurship scholar, I wanted to offer the motivations and foundations for this book. As a doctoral student at Bond University, Australia, I was also a full-time senior teaching fellow, teaching 12 one-hour tutorials a week for 45 weeks per year. To survive, I had to try to develop routines for research and for efficiently switching between tasks. When I came to the USA for my last year of dissertation work (Northwestern University), the experience confirmed my suspicions that I was definitely not going to be able to âcruiseâ based on talent; I was going to have to work very hard. However, more than that, I was going to have to learn how to publish. That is, rather than relying on a passive and implicit understanding of publishing research, I took active steps to learn this process, thought about it deeply, and developed a series of heuristics to help improve my performance.
In taking active steps to learn, I submitted papers and worked with peers. Although it could be considered a disadvantage that my dissertation committee did not include highly published scholars and could not help a great deal in crafting my entrepreneurship research for publication, I believe that in the long run, this has been a blessing. Rather than vicariously learning from a senior scholar in the process of crafting a paper and guiding it through the revise and resubmit (R&R) process, I actively learned with peers (other junior scholars) by submitting our co-authored papers to journals. Who knows how things would have turned out if I had done my dissertation in the USA under the mentorship of, say, Jeff Covin, Harry Sapienza, or Howard Aldrich. However, I do not begrudge doctoral students who publish early and often with senior colleagues. My main point, I think, is that by working with peers, the sole responsibility for a paperâs future fell on me. I (and my peer co-authors) became actively aware of what worked and what did not. Because we, the authorship team, were at the same career level, we learned how to discuss publication issues and were highly motivated to improve and try again.
Indeed, everything was viewed through the lens of âWhat can I learn from this feedback?â Believe it or not, I was even excited when I received a rejection letter (but I no longer feel that way). Because I had not received much feedback on my dissertation research, I was excited that three scholars had read my work, found something interesting in it, and provided me feedback so that I could not only improve the paper at hand but also learn skills that I could use to become a better scholar going forward. I know this excitement over a rejection is strange, which became particularly apparent to me through a discussion I had with Harry Sapienza. In a doctoral seminar, I was talking about the publication process and the reasons you should celebrate when you receive an R&R decision letter from a journal. When someone asked me about how to deal with the negative emotions associated with such a decision letter, I thought they misinterpreted what I had said and assumed I was talking about a rejection. Apparently, they were talking about an R&R. As Harry pointed out to me later, I should not assume that everyone thinks and feels the same way as I do about research. Still incredulous, given the shift in odds from an initial submission to an R&R, that someone could have a negative emotional reaction to an R&R letter, I asked around. I found out that I was wrong and Harry was right. Inspired by my conversation with Harry Sapienza, I offer this blanket caveat for the book: the approach, thinking, and feelings expressed in this book are those that I have learned (and am still learning) and use; all aspects of the book may not (and probably will not) always apply to all people all the time. I also realize that my path is only one path and is likely different from those taken by others. Hopefully, by providing one perspective (without millions of contingencies), you can decide what directly applies to your career, what can be adapted, and what can be discarded.
Returning to the issue of excitement in receiving feedback on a rejected paper, I used that excitement to drop other work and immediately begin to interpret the letter and the spirit of the reviewersâ comment to improve the paper and resubmit it to another journal. I thought about a paper as having momentum and believed it was important to keep the momentum rolling. On the flipside, I felt that if a paper sat, it lost momentum and required more effort to âstart the ball rollingâ again. Fortunately, having peers as co-authors and choosing to work with people with similar values, I was able to quickly learn, enhance the quality of each paper, and put them âback in playâ at journals. Speed came from energy and momentum, not from cutting corners.
Through speed and working with colleagues on papers out of our dissertations, my colleagues and I were able to generate a reasonable number of papers in the first couple of years post-dissertation. We believed that having a âreasonableâ number of papers âin playâ (i.e., at least three or four papers under review at top journals) was important for two primary reasons. First, we believed that the more papers we worked on, the more feedback we would receive. Feedback not only helped us improve the quality of the specific paper but also provided the basis for a deeper understanding of what reviewers were looking for and how to address these issues and follow their recommendations. Upon reflection, we were engaging in deliberate practice and hopefully building expertise. We certainly had many opportunities to learn from our failures, but fortunately, we also had some successesâsome small winsâwhich allowed me to start to believe that maybe I could make a career as an entrepreneurship scholar.
The second reason we believed it was important to have a sufficient number of papers in play was because we came to realize that there is a random component to publishing. That is, the same paper could be rejected or receive an R&R based, in part, on the âluck of the drawââthat is, based on who is assigned as a reviewer (although, as I will discuss later, there are ways authors are not completely helpless in the selection of reviewers). We did not use recognition of this random component to dismiss reviews that rejected our work (because that would distract us from learning), but we realized that a way to âcombatâ or âmanageâ this randomness is to have a âsufficientâ number of papers in play. That is, with only one or two papers in play, a bit of bad luck could mean zero publications on the CV. We did not want to put all our energy into only one or two papers. This being said, I do not want to give the impression you should create many mediocre papers rather than one good paper. Rather, I am suggesting that you âhave your cake and eat it tooâânamely, that you generate and circulate numerous high-quality papers for feedback (for doctoral students, this might be two or three papers, and for junior scholars, this might be between four or more papers). I also realize that this is easier said than done, but I think that a focus on learning from the process (rather than being overly concerned with the outcome of a specific paper in a specific journal) is the key to moving in this direction.
The above preamble to the book is simply to say that as someone with limited ability and training, I was going to have to think about how I think about research (i.e., be meta-cognitively aware). I had to learn as much and as rapidly as possible, and I was going to have to be disciplined in how I approached work. However, I also want to note that while the above discussion implies a very instrumental and pragmatic approach to research, it belies the underlying motivations driving my research. I am passionate about the phenomenon that we, as entrepreneurship scholars, study, and as a result, I obtain many intrinsic rewards from engaging in the process. Wanting the outcomes of these processes to be published is not, I believe, necessarily an extrinsic reward (one that could possibly undermine intrinsic motivation and, therefore, creativity). It is intrinsically rewarding to ask interesting questions and to offer potential answers to them, but I also find that interacting with others (including reviewers and editors) to further develop and refine these ideas can also be a rewarding activity (although I recognize that many people find the back and forth of the review process to largely be a waste of time as well as overly intrusive on the authorsâ âvoiceâ). However, even if the R&R process provides little to no intrinsic rewards, publishing research can generate feelings of pride and achievement, especially when others find your ideas interesting and you influence their research projects.
I also realize that extrinsic rewardsâparticularly promotion and tenureâare important, but I tried to make sure that these thoughts and considerations did not become the driving force behind my research. If they did, I felt that creativity would suffer. I am not trying to hold out my research as the most creative or anything like that, but these are the things I told myself to make sure I continued to enjoy my career. Regardless of intrinsic or extrinsic motivations, I hope that this book on thoughts about the process faced by entrepreneurship scholars is helpful in some wayâperhaps mostly to stimulate thought and discussion among junior and senior scholars about the processes involved in developing a successful career as an entrepreneurship scholar. From this book and the discussions that it hopefully stimulates, you will be able to construct a more successful career as an entrepreneurship scholar.
Okay, so maybe this is self-delusional, but I think of scholars, at least the good ones, as highly entrepreneurial (at least in an analogical sense). Taking this perspective provides a basis for finding or generating a research opportunity. By a research opportunity, I refer to situations in which new knowledge can be introduced through new theory, new methods, and/or new combinations that fill important gaps in our understanding of entrepreneurial phenomenon. The question then becomes how does one identify or generate these research opportunities. I want to start a discussion on this topic by highlighting approaches that are unlikely to yield attractive research opportunities.
As the editor in chief of the Journal of Business Venturing, I am often asked what is âhotâ at the moment. Presumably, the questioner believes that my insight into what is hot (through seeing early and in-press articles) will reveal research opportunities for him or her. However, I think this is an unproductive path to identifying a research opportunity, a research theme, or a career. Although something may be hot at the moment and the first papers about this topic are particularly important, by the time the questioner develops and executes a study, the topic may no longer be popular, or his or her paper may end up being among many others trying to follow the trend. This approach could still work if the study provides new and interesting insights to the new stream. However, an opportunistic approach to follow what is hot may be taking the scholar away rather than closer to important contributions to the field. That is, by following what is hot rather than what one knows and/or is passionate about, it becomes more difficult to generate the sort of insights required for a substantial contribution.
One possible way to pursue what is hot and still say something interesting is to investigate the flipside. For example, if social entrepreneurship is popular, then perhaps investigate the flipside of social entrepreneurshipâif there is such a thingâfor instance, unsocial entrepreneurship, anti- (rather than pro) social motivation, harm rather than preserve. Such an approach has the potential to offer an important counterweight to the new stream of research and thus contributes to that conversation by increasing our understanding of its boundary conditions.
So, where should scholars look for research opportunities? If we return to the perspective (or delusion) that as researchers we can think and act entrepreneurially, then we can at least think about what we know about the identification of entrepreneurial opportunities to approach the identification of research opportunities. In explaining the formation of opportunity beliefs, McMullen and Shepherd (2006) highlighted the importance of knowledge and motivation in both third-person opportunity beliefs (i.e., an opportunity for someone) and first-person opportunity beliefs (i.e., an opportunity for oneself). I draw on the importance of knowledge and motivation to think about where to look for (i.e., where to generate) research opportunities.
Knowledge and the Identification of Research Opportunities
The identification of research opportunities likely depends on knowledge. Just as entrepreneurs have idiosyncratic (i.e., individual-specific) knowledge such that different individuals can see the same technology and come up with different opportunities (Shane 2000), scholars can use (or rely on) their idiosyncratic knowledge to generate novel insights. In contrast to junior scholars who are often paralyzed from developing âtheirâ model because they have not yet reviewed all the literature, my good friend Evan Douglas had a different approach. When I asked him when he stops his review of the literature before concluding that there is indeed a gap to be filled, he told me he does not start with a review. As a junior scholar, I was horrified and asked him, âBut how do you know that the model you develop has not already been done before?â His response was, âThe way I think about these things, I would be shocked if someone would head down the same path and come up with the same solution/story.â If you know Evan, this is certainly true; he has a unique way ...
