What are some dissertation-worthy topics in behavioral/experimental economics?

Question

To put it another way, what are some areas that seem important but tractable, and therefore might yield productive research questions that could lead to a paper and maybe more?

I’ll open the discussion with one potential answer, below, and I hope others will follow.

Comments

Scholars have extensively looked into behavioral implication of income and wealth inequality. A rich strand of literature is available on that. An interesting diversion of this scholarly work is the behavioral implication of inequal distribution of power. I have been working on this since last few months. Anybody interested, feel free to drop a line.

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Does anyone want to look into why Eminent Domain was not utilized to avert any perceived need for our Civil War?  

Eminent Domain should have prevented our current biases and bigotries that resulted in our Civil War and segregation, and some of our current "racial problems".

Answer 1

I’ve long been interested in _repugnant transactions_(Roth, 2007), which are transactions that some people would like to engage in but others think they shouldn’t be allowed to. The most interesting cases are those in which there aren’t easily measurable negative externalities that impinge on those who would like to ban these transactions.  Sometimes the addition of money makes repugnant a transaction that otherwise wouldn’t be: e.g. paying for sex, or for a kidney.

Lots of transactions are banned, in some places and times, like charging interest on loans in Europe in the Middle Ages.  But these bans are far from universal: e.g. prostitution is illegal in California, but commercial (paid) surrogacy is legal, while the opposite is the case in many places -- only unpaid surrogacy is legal in Canada and England (where, for some reason, it is rare :-), and it is entirely illegal in much of Europe.

Black markets are often active: transactions that influential parts of society find repugnant may be hard to suppress (think of the market for narcotics).

The economics literature is largely new, and in its infancy.  See e.g. recent impressive work by Ambuehl, Lacetera, Macis, and Slonim.  We need to understand better what is going on…

(For a host of examples, browse http://marketdesigner.blogspot.com/search/label/repugnance  )

Comments

I am also interested in these topics - and the related question of normative constraints.  Many more market activities are occurring algorithmically, and many online platforms use algorithms to direct transactions, attention, etc.  For example, many firms dynamically and adjust their prices over time based on both signals of demand and capacity, and in individual characteristics.  However, this potentially runs into concerns about fairness from customers, platform verndors, etc.

Online platforms also raise some interesting questions about engagement - how to facilitate it without being exploitative.  This matters not just for users, but also for content/capacity providers.  Uber and Didi wants to make sure their drivers are logged in and available as often as possible.  Youtube wants to encourage channels to upload good content frequently - and there have been some recent stories about creator burnout, and how the setup of Youtube's platform encourages that.

Finally, there are application and policy areas that are well established areas of research but are increasingly important.  Health care and sustainability are major areas where we need further investigation of how to encourage behavioral change: not just in patients/customers, but also employees, suppliers, etc.

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For an interesting recent paper on repugnance see https://www.nber.org/papers/w26119,
Projective Paternalism
Sandro Ambuehl, B. Douglas Bernheim, Axel Ockenfels
NBER Working Paper No. 26119

Answer 2

I think there is much more to be done with using the lab as an "organic" data generation process (as opposed to simply simulating data) to study the performance of applied econometric approaches. I have in mind exercises such as those in:

- Bajari and Hortacsu (2005) https://www.jstor.org/stable/10.1086/432138?seq=1#page_scan_tab_contents
- Frechette, Kagel, and Morelli (2005) http://cess.nyu.edu/frechette/print/Frechette_2005c.pdf
- Salz and Vespa (2017) http://www.columbia.edu/~ts3035/websitefiles/salz_vespa.pdf

This is not really an area of study, but I think an under-developed way to use experimental data that could prove very informative for a variety of applied methods and topics.

Answer 3

There are many exciting open questions in behavioral market design, especially with regard to matching markets.

I mean for example the question of how people form preferences, e.g.,  over schools or university programs. This is pretty much a black box up to now, and it is often simply assumed that people have well-defined preferences when a centralized matching procedure is run. However, there is evidence that people search for information, that the process of discovering the preferences can be influenced by the market design, that people re-order their preference lists over time etc. (see for example the work by Narita and by Dwenger, Kuebler, Weizsaecker). Static mechanisms require people to submit their full preference list at once, but there are also dynamic mechanisms, e.g. in the sense of providing additional information as time elapses, requiring applicants only to provide their most preferred option within a certain set etc. Such mechanisms seem to gain importance, and have also only become feasible due to widespread internet access (see e.g. Bo and Hakimov, Gong and Liang).

A related topic that I believe deserves scrutiny is the question of what makes it simple to choose the optimal strategy in a (matching) mechanism and what makes it difficult. Strategy-proofness, that is, having a weakly dominant strategy to truthfully report one‘s preferences, does not seem to be sufficient according to evidence from actual matching markets and from experiments. Relatedly, how can market participants be convinced to report their preferences truthfully if this is in their best interest? Which type of advice works better than other? What type of information should be provided to the participants? (Some papers in this area are by Ding and Schotter, Guillen and Hakimov, as well as Pais and Pinter).

Answer 4

From looking through any behavioral economics class or textbook, I get the impression that we know quite a lot about what people want (time preferences, risk preferences, etc.), but we know much less about how people think, especially outside of strategic contexts.

There are many exciting topics in that area, such as all the work on limited attention (which, for what I think is the first time, has produced a rigorous model of mental accounting -- Matejka & Koszegi), or, more controversially, that on salience. Thinking about choices in the right way affects many important life outcomes, such as education, financial investments, etc. And once you study the way people think, and realize that not all choices are optimal (see, e.g. default effects), you'll quickly find yourself thinking about questions of welfare economics (Allcott and Taubinsky have some very nice applied work on this).

Answer 5

Three of the more established subfields in behavioral/experimental for individual decision making are non-standard time preferences, non-standard risk preferences, and reference-dependent preferences.  There are other (some might say more important) areas of research, but these are the three that I have some perspective on. There is still a surprising amount that we don't know in each. Valuable, literature-driven, dissertation topics could be:

1)  Time Preferences: Who treats money like consumption? Why? When?: This topic could speak to a conflicting experimental literature on the prevalence of behavioral intertemporal phenomena as the unit of elicitation changes.

2) Time Preferences: Evaluating Pessimism and Optimism for Future Behavior. The core policy implications drawn from behavioral models of time preferences rely on the relationship between beliefs and behavior. Facts in this area are scarce and would benefit not only the academic field but also policy.

3) Risk Preferences: Evaluating the Predictive Power of Elicited Behavioral Parameters. It is known that the extent of measured risk tolerance (including behavioral parameters) is sensitive to measurement techniques. This is problematic as these narrow sensitivities suggest a lack of external validity for field behaviors. Correlational evidence relating different elicitation techniques to previously determined out-of-sample environments could enrich researchers' understanding of what lab behavior is actually capturing.

4) Risk Preferences: Assessing Rank and Sign Dependence for Probability Distortions.

5) Reference Dependence: Synthesizing the Body of Research on Expectations Based Models. The empirical research testing comparative statics for expectations based models has not generated a clear message. Research discussing why could help move the needle in this sub-field.

I noted above that these are literature-driven topics. This means they are grounded in current discussions and space exists for more than one perspective to get the ball rolling. I think for PhD students this has pluses and minuses. The pluses will be on immediate impact and likelihood that your research topic will be well understood by others. The minuses will be on assessed creativity... that the contribution may seem plodding or incremental. In my opinion the pluses out-weigh the minuses.

Answer 6

Some thoughts that resulted from talking with Ryan Oprea about the relatively small experimental literature on bandit problems.  Bandit problems are decision problems in which agents are uncertain about the payoff consequences of their actions and must experiment to find out how to optimize.  These problems have become an important part of economic theory in the last 15 years but experimentalists have (surprisingly) done little work on how people experiment.  A few papers have directly studied bandit setups in the lab (e.g. Banks, Olson and Porter ET 1997) and a relatively recent discussion of the literature is in Anderson TD 2012). But many questions regarding how humans deal with the exploration- exploitation trade-off are still open and seem ripe for study in the lab.

Related opportunities are also in strategic settings.  For instance, most game theoretic experiments follow a protocol in which subjects are provided with an exhaustive set of primitives of the game (e.g. the payoffs of others).  But relatively little is known about how people  behave in games in which agents do not know all of the primitives, which may be learnt through exploration (though there is a small literature on the topic).  This is could be an exciting area for exploration because (i) this is often a more realistic setting for studying strategic interaction and (ii) there is a rich body of theory (much untested) describing how behavior should evolve in such settings (both the strategic experimentation literature and the theoretical learning in games literature).

Comments

Agree on bandits!  In many ways this is the canonical decision problem and it forces an understanding of exploration vs exploitation which is not a concept that exists under static utility maximization.  

Fortunately, a tremendous amount is known about bandit problems from decision neuroscience, where typically people are given no priors and learn bandit reward parameters (see Nathaniel Daw, Peter Dayan and many others more recently (e.g. http://gershmanlab.webfactional.com/pubs/SchulzGershman19.pdf) . Often the bandits are "restless" so underlying reward distributions ares shifting.  there are on the order of 100+ papers (perhaps many more). In many cases subjects are incentivized with $ (or animals with primary reinforcers like food/drink) because decision neuroscience has taken up many of the formal approaches and norms of experimental economics.

Answer 7

Related to several insightful answers upthread is the idea that the types of data gathered in experiments has continued to expand. It is now possible to gather process data related to nearly every aspect of the decision-making process without access to expensive equipment. Belief elicitation has of course become commonplace and widely accepted, both in the lab and in the field. Still, most of the literature has focused on first-order beliefs while higher-order beliefs can be of first-order significance in many strategic situations, e.g. beliefs about whether others' beliefs are biased or beliefs about beliefs-related norms. Most of the existing experimental research involving higher-order beliefs has been related to psychological games, but there are now many new possibilities to explore.  

The recent use of response times to understand behavior in strategic environments rather than just individual choices is also very promising (see Frydman and Krajbich; Schotter and Trevino; Rubinstein and others for examples). With technological advancements, there are now so many naturalistic options for studying topics such as attention, exploration, etc.: gestures and biodata on mobile phones, every mouse hover and click (e.g. hidden information), screen sharing. I am omitting many other examples, and invite others to fill those in. While there is never a substitute for good experimental design, a lot of good, available data that is generated by the time a players makes a decision is still being left on the table.