At its best, industry focuses people. It demands that people use everything at their disposal to solve an issue. It puts a premium on being lean, humble, agnostic, creative, and rigorous. Industry data scientists use qualitative methods, e.g., directly observe processes and people, do lean experimentation, build novel instrumentation, explore relationships between variables, and “dive deep” to learn about the problem. As a result, at any moment, they have a numerical account of the problem space, an idea about the blind spots, the next five places they want to dig, the next five ideas they want to test, and the next five things they want the company to build—things that they know work.
The social science research economy also focuses its participants. Except the focus is on producing broad, novel insights (which may or may not be true) and demonstrating intellectual heft and not on producing cost-effective solutions to urgent problems. The result is a surfeit of poor theories, a misunderstanding of how much the theories explain the issue at hand, and how widely they apply, a poor understanding of core social problems, and very few working solutions.
The tide is slowly turning. Don Green, Jens Hainmeuller, Abhijit Banerjee, Esther Duflo, among others, form the avant-garde. Poor Economics by Banerjee and Duflo, in particular, comes the closest in spirit to how the industry works. It reminds me of how the best start-ups iterate to a product-market fit.
Ask yourself the following questions:
- Do you have in your mind a small set of numbers that explain your current understanding of the scale of the problem and some of its solutions?
- If you were to get a large sum of money, could you give a principled account of how you would spend it on research?
- Do you know what you are excited to learn about the problem (or potential solutions) in the next three months, year, …?
If you are committed to solving a problem, the answer to all the questions would be an unhesitant yes. Why? A numerical understanding of the problem is needed to make judgments about where you need to invest your time and money. It also guides what you would do if you had more money. And a focus on the problem means you have broken down the problem into solved and unsolved portions and know which unsolved portions of the problem you want to solve next.
How to Solve Problems
Here are some rules of thumb (inspired by Abhijit Banerjee and Esther Duflo):
- What Problems to Solve? Work on Important Problems. The world is full of urgent social problems. Pick one. Calling whatever you are working on as important when it has a vague, multi-hop relation to an important problem doesn’t make it so. This decision isn’t without trade-offs. It is reasonable to fear the consequences when we substitute endless breadth with some focus. But we have tried that way and it is probably as good a time as any to try something else.
- Learn About The Problem: Social scientists seem to have more elaborate theory and “original” experiments than descriptions of data. It is time to switch that around. Take for instance malnutrition. Before you propose selling cut-rate rice, take a moment to learn whether the key problem that poor face is that they can’t afford the necessary calories or that they don’t get enough calories because they prefer tastier, more expensive calories than a full quota of calories. (This is an example from Poor Economics.)
- Learn Theories in the Field: Judging by the output—books, and articles—the production of social science seems to be fueled mostly by the flash of insight. But there is only so much you can learn sitting in an armchair. Many key insights will go undiscovered if you don’t go to the field and closely listen and think. Abhijit Banerjee writes: “We then ran a similar experiment across several hundred villages where the goal was now to increase the number of immunized children. We found that gossips convince twice as many additional parents to vaccinate their children as random seeds or “trusted” people. They are about as effective as giving parents a small incentive (in the form of cell-phone minutes) for each immunized child and thus end up costing the government much less. Even though gossips proved incredibly successful at improving immunization rates, it is hard to imagine a policy of informing gossips emerging from conventional policy analysis. First, because the basic model of the decision to get one’s children immunized focuses on the costs and benefits to the family (Becker 1981) and is typically not integrated with models of social learning.”
- Solve Small Problems And Earn the Right to Saying Big General Things: The mechanism for deriving big theories in academia is the opposite of that used in the industry. In much of social science, insights are declared and understood as “general.” And important contextual dependencies are discovered over the years with research. In the industry, a solution is first tested in a narrow area. And then another. And if it works, we scale. The underlying hunch is that coming up with successful applications teaches us more about theory than the current model: come up with theory first, and produce posthoc rationalizations and add nuances when faced with failed predictions and applications. Going yet further, you could think that the purpose of social science is to find ways to fix a problem, which leads to more progress on understanding the problem and theory is a positive externality.
Suggested Reading + Sites
- Poor Economics by Abhijit Banerjee and Esther Duflo
- The Economist as Plumber by Esther Duflo
- Immigration Lab that asks, among other questions, why immigrants who are eligible for citizenship do not get citizenship especially when there are so many economic benefits to it.
- Cronbach (1975) highlights the importance of observation and context. A couple of memorable quotes:
“From Occam to Lloyd Morgan, the canon has referred to parsimony in theorizing, not in observing. The theorist performs a dramatist’s function; if a plot with a few characters will tell the story, it is more satisfying than one with a crowded stage. But the observer should be a journalist, not a dramatist. To suppress a variation that might not recur is bad observing.”
“Social scientists generally, and psychologists, in particular, have modeled their work on physical science, aspiring to amass empirical generalizations, to restructure them into more general laws, and to weld scattered laws into coherent theory. That lofty aspiration is far from realization. A nomothetic theory would ideally tell us the necessary and sufficient conditions for a particular result. Supplied the situational parameters A, B, and C, a theory would forecast outcome Y with a modest margin of error. But parameters D, E, F, and so on, also influence results, and hence a prediction from A, B, and C alone cannot be strong when D, E, and F vary freely.”
“Though enduring systematic theories about man in society are not likely to be achieved, systematic inquiry can realistically hope to make two contributions. One reasonable aspiration is to assess local events accurately, to improve short-run control (Glass, 1972). The other reasonable aspiration is to develop explanatory concepts, concepts that will help people use their heads.”