Authors:
Daniel Malter – Harvard Business School

Interviewers:
Justin Frake – University of Maryland
Romain Boulogne – HEC Paris

Article link: http://asq.sagepub.com/content/59/2/271.abstract

Question 1. What prompted you to do work on the wine industry? Did you have a personal connection with it? If so, how important do you think it is to do research in settings that are personally interesting?

A friend of mine invited me to my first good bottle of red wine. The difference to the plonk I had been drinking was eye-opening. I started collecting wines at about age 20 with very limited means in Germany, where the legal age to purchase alcohol is 16. Once you really get into wine, Bordeaux is inescapable. So yes, I do have a personal connection to the setting. Writing papers can be a tedious process, similar to what Edison said about the share of inspiration and perspiration. Above all things, the phenomenon and question have to be interesting. But I think it can help emotionally in the perspiration phase if you study a context that is either obviously important or that you deeply care about personally.

Question 2. One of the great strengths of the article relates to the fact that you can rely on the unique and fixed nature of the classification, which subsequently allows to disentangle between status, quality and organizational performance – could you tell us a bit more about how you started working with these data? Which came first: the theoretical gap or the empirical phenomena?

In this particular instance, the empirical phenomenon and context came first, but I was already interested in the phenomenon and theories of social status. I went on the job market twice in two consecutive years. In the second year I needed to write a new job market paper, and it needed to be fast. Around that time, there were a couple of just published and working papers that questioned the causal inference in status studies (Waguespack and Simcoe 2011, Azoulay, Stuart, and Wang, 2013), but they weren’t on the organizational level. I knew that I had a near perfect organizational context to do something with a similarly strong claim to causality. But that wouldn’t have been enough. There needed to be theoretical novelty as well. I believed that this context would be able to tell us something about why we commonly overestimate status effects and why status was valued in the first place. I started writing the paper in June, had a finished draft by the time the Academy of Management Meeting came around, and submitted it to ASQ at the end of September or beginning of October. When I tell this story, people often look at me in disbelief saying that this is incredibly fast. But analogously to what Picasso is storied to have said “it took my entire life [to write this paper].” It would not have been possible had I not been intimately familiar with the context in the first place.

Question 3. As management scholars, causation is really important to us. What is truly amazing with your paper is the robustness of your models. For instance, you used the average rainfall in August and September as well as the average temperature in September as instrument variables. How did you come up with these variables? Did they come late (review process) or early in the paper’s evolution?

The three other aspects of the empirical context and setup are more important to closing in on the causal effect: the fixed nature of the 150 years old classification, allowing for nonlinear quality and reputation effects, and allowing for reputation to be longer-lasting than the literature has typically assumed. So I hope the three things that people will remember of the causality part of the paper are (1) that status effects are probably smaller than we commonly estimate because (2) we underestimate the premium markets place on the pinnacle of quality and (3) because reputations are more durable than we typically think. But knowing that these issues are more important to the status effect estimates than the endogenous choice of quality was only possible in front of the backdrop of the instrumental variable estimator.

The instrumentation itself was actually more complicated than using weather variables. I ended up instrumenting for a chateau’s reputation and its squared term with the interaction terms of current weather and lagged reputation and its squared term. The appendix of the paper describes the approach in detail and why this was necessary. That took me six months to figure out. There was an IV approach in the initial submission, but that approach turned out to be wrong. I was very upfront about it in the letter I sent with the revision.

When submitting a paper, you have to cross the editor’s and reviewers’ thresholds. By crossing the threshold I do not only mean that it needs to be interesting. As a reviewer, I want to feel the pain that the authors have gone through to make it as good an initial submission as it reasonably can be. That pain shows quietly in simple writing, logical flow, research design or data, and methodological care. I think many colleagues feel similarly about it. If you can achieve that, I think you have a good chance that the editor and reviewers become stakeholders in your paper and want it to succeed. At that point good reviewers and editors will even be forgiving if you have to say ‘I was wrong’ like I had to, because they can feel your pain and that getting it right is more important to you than getting it published fast.

Question 4. The work you provided is truly impressive; even more impressive, it is a single-authored paper! You have a working paper about the potential downsides of high-status affiliation. Based on this work and your experience with single-authorship, do you have any recommendations for PhD students regarding the advantages (and disadvantages) of working solo?

On the downside, working solo can be grueling and lonely. It is probably not for everyone. Moreover, the learning curve is probably flatter than if you work with others. Unless you can learn from sources other than co-authorships, this is probably not advisable, in particular not for a doctoral student. In addition, measuring output by the number of publications, it is unlikely that you would be as productive as somebody working with co-authors could be (assuming functional teams and balanced responsibilities). I take that as a given, and it is not clear how many schools are willing to accept that when it comes to promotion. Finally, the empirical evidence suggests that academia is more and more a team sport. Even the biggest impact contributions are increasingly produced by teams (Jones, Wuchty, and Uzzi, 2007). But that’s an average tendency, not an inescapable fact. On the upside, I do get all the credit; I do not have to negotiate and can take any risk I want at the risk of embarrassing myself; and in some instances working solo can be more efficient than working in a team. I think the wine paper is a good example for that. That said, even though the paper is solo-authored, it really is not a standalone effort. It has been vetted through presentations to and discussion with many wonderful colleagues, and it has greatly benefited from the reviewers’ and the associate editor’s comments and guidance.

Question 5. Do you have any advice for PhD students who take the issue of causation seriously? Do you have in mind any technique(s), article(s) or book(s) that inspired you and that are extremely important for us as PhD students?

I have benefited a great deal from the training in experimental methods that I received in Berlin before I entered the PhD program at Maryland. I find it problematic that experimental methods are not a part of the required curriculum in many doctoral programs in the social sciences. Perhaps it is deemed too easy a subject. But how do you start to think about causality and departures from it if you have never learned to think through what the perfect experiment would look like? In some ways, the econometric courses that teach you, among other things, how to fix departures from causal inference take the second step before the first. So what would my advice be? First: get yourself a copy of Campbell, Stanley, and Gage’s (1963) book. Second, arm yourself with my committee member’s (Dave Waguespack’s) favorite question: what would the ideal experiment look like? Third, take it upon you to take the hardest/best econometrics courses you can w/o flunking the program. Finally, read empirical papers, identify what the ideal experiment would have looked like, how the setting and empirical setup departs from that ideal, and think through how these departures from causality could be addressed either through the choice of a different setting, research design, or estimator. If my paper and the other papers in this line of work have one message on this front, it is that you should prioritize a clever choice of setting or research design over a fancy estimator.