The charge that Political Science (or other non-STEM disciplines) is lacking relevance and does not produce interesting research is made then and again, with two new pieces published these days. One is written by a political economist, stating that most research is boring; one is written by a German political scientist echoing this claim and arguing that political science lacks relevance (written in German). The underpinnings of these claims sound familiar: the discipline and publishing system does not reward innovative, new research; it is all focused on journal publications; research is a means for getting third-party funding; (junior) researchers are not courageous enough; political science focuses too much on the rigor of their methods instead of relevant research questions.
I have some sympathies with these claims and it is not bad if the discipline gets stirred up from time to time. Leaving aside that I find these claims a little bit disrespectful vis-à-vis all the political scientists who do good research day-in day-out, I think there are multiple issues that make these charges too simplistic and deserve more scrutiny (the German contribution in particular because it raises more points). I have a couple of lose thoughts referring to different dimensions of the debate.
1) What is the reference point?
It is not obvious to me that political science was more relevant 20 years ago or so. If it comes to big names and relevance in Germany, one can immediately think of Habermas, Scharpf, Dahrendorff and others. Admittedly, I cannot tell who the Habermas of our times is, but there are researchers such as Münkler and Rainer Forst who are engaged in public debate on a regular basis. I also see a lot of political scientists on TV on different channels (such as Korte and Faas on elections) and do not believe we have a problem here. At least, it is far from obvious that political scientists had more screen time 30 years ago or were more relevant in any other respect. The perception of the past might be biased by a small number of truly outstanding people who had great influence and which make us overlook that many political scientists are engaged today.
This might also be a matter of a changed media environment. If you wrote something in the FAZ or appeared on ARD 30 years ago, you could reach many more people than today with a more scattered media landscape.
2) What kind of relevance?
With the current rise in skepticism regarding the establishment, which includes people in academia, one can question whether relevance should be measured in terms of media appearances because the “mainstream media” is also considered to be part of “the establishment”. There have been some calls that science should stand up to the establishment criticism, but this can hardly be a matter of junior researchers alone. Certainly, it would be useful, if not necessary to launch some initiatives (although I could not tell at the moment of what kind). Since the current situation is an unprecedented one for most of us, it might simply take somewhat more time to develop ideas and bring them to life.
3) Rigor isn’t the problem
If one measures ‘relevance’ as media appearances, the increasing rigor of political science cannot be the sole problem, if at all. In Germany, economists dominate the public debate, even on topics that fall right into the field of sociology or political science. These are economists publishing articles that usually are at least as rigorous as political science articles (and as boring, by the standards of the critics). This indicates that you can do methodologically sophisticated research and be publicly engaged at the same time. In German political science, it might be a problem of the discipline in the sense that public activities are considered as “non-scientific” or a waste of time. I do not know whether this holds true, but I believe this is not an issue as long as one keeps a balance and continues doing research.
4) Big questions need time
Big research questions cannot be addressed within a couple of years. I do not know, but I imagine that Piketty worked for more than ten years on his book because of his impressive data collection effort and its broad coverage (I guess this a study the critics would consider relevant). Because of the very nature of big questions, it is impossible for PhD researchers to try answering them. The same holds for Post-Docs and tenure track researchers who have up to six years or so to get a professorship. If at all, then, tenured researchers can approach the big issues of our time. (Maybe junior researchers can start such a project on the side, but the actual output will not be ready until they are senior researchers.)
5) Complex issues might require small questions
It seems fair to argue that the focus on small research questions reflects the idea of cumulative research where we get the broader picture by bringing together the results of multiple small studies on the same topic. (I leave it open here how well the idea of cumulative research works in practice.) However, there is also a substantive reason for partitioning big questions into smaller ones (Geddes has written about this). For what we know today, big questions deserve complex answers, not simple ones. If we were accepting Piketty’s conclusions about income and wealth , we might want to address the question of how the state can redistribute wealth and decrease inequality. It would be nice to have a big theory of redistribution, but it is quite a challenge because you have to account for the tax system, the welfare state, capital mobility, political institutions etc. So why not decompose the big research question into a smaller one and approach one manageable question at a time? Answering big research questions does not require a big one-shot project. (I do not know how many researchers do this, I just want to raise the option here.)
6) The era of collaborative research?
Because of the complexity of many political issues and the rising standards in terms of theory and methods in our field, it might be useful to discard the idea that one researcher can do this. Piketty shows that one person can pull off a big project, but I think this is getting increasingly demanding because the low-hanging fruit has been picked. Here, I particularly think of the “fruit” as data because data such as welfare expenditure of OECD members have been used a zillion times. The V-DEM project is a good example of a collective endeavor covering generating new data and insights that could hardly be done in the same way by a single person.
7) There is no rigor-relevance trade-off
On a more substantive dimension, I want to argue against the idea of giving up some rigor in favor of higher relevance. (The German article reads like this in the last paragraph, but I am not sure whether this is the message.) If you want to address a big research question, you might need to work with data of questionable validity and do not have a sound identification strategy. This is not a problem per se because this is then the data and design you have to live with. However, this should not undermine the rigor of the analysis because rigor depends on taking into account the data quality and quality of the design when drawing conclusions. What is affected is the uncertainty of your conclusions that should be higher compared to a study with more valid data and a better identification strategy. If you do proper research when answering a big question, you might face a relevance-certainty trade-off, not a rigor-relevance trade-off.
All in all, I think a healthy, productive discipline needs a mix of people working on big questions and smaller questions that build on each other’s work. In any case, achieving the highest possible standards during the analysis should be the common denominator of all political science research.
P.S.: In the initial post, I called it a relevance-uncertainty trade-off. I noted this is not a trade-off, but a positive association. I therefore modified the post and now coin it a relevance-certainty trade-off.