I’m an economics PhD student. I’ve spent some time thinking about a) how to do good and b) how to succeed in academia.
The holy grail is a project that does good and results in a paper publishable in a peer reviewed journal. But I have struggled with this and I’ve noticed a few other EAs in early stages of academia doing so too.
I’ve come to think the reason is that we are problem-solvers. We want to change people’s lives for the better. When we try to think of a research project, we think about the problems with the world, and how to fix them.
What makes a good academic research paper is fundamentally different. I am far from being an experienced academic, but I understand that research is about pushing forward the frontier of knowledge and understanding. Examples are finding a better way to explain observed phenomena, measuring something previously unmeasured, documenting a previously undocumented connection or relationship, inventing a new technique or using an old technique in a new way, or showing that supposedly separate things are just different examples of a general case.
It’s tempting to say “research is solving the problem of not understanding” or “problem solving is increasing your understanding of how to solve the problem”. But that shoe-horning only de-emphasises their considerable differences. I would rather think of them as two different stages of a process. Research creates the knowledge, and problem-solving applies the knowledge.
A trap for EAs in early-stage academia is to do work that makes the world better, without fully realising its academic potential. For some projects, a small adjustment could unlock huge academic value.
For example, think of trying to answer the donor or policy question “How much money should I allocate to x vs. y?”. I believe that is usually a problem-solving question, even if no-one has tried to answer it before. A more academic question may be “Under what conditions is [general case of x]’s impact potential dominated by [general case of y]’s impact potential?” Then, after making your academic contribution, you can also throw in your x vs. y calculation, as an example, or policy implication.
Thoughts?
"For some projects, a small adjustment could unlock huge academic value." Would you be able to provide examples please?
I should clarify - I don't mean a small amount of work, but a small conceptual adjustment. The example I give in the post is to adjust from fully addressing a specific application to partially addressing a more general question. And to do so in a way that is hopefully intellectually stimulating to other researchers.
In my own work, using a consumer intertemporal optimisation model, I've tried to calculate the optimal amount for humanity to spend now on mitigating existential risk. That is the sort of problem-solving question I'm talking about. A couple of possible ways forward for me: include multiple countries and explore the interactions between x-risk mitigation and global public good provision; or use the setting of existential risk to learn more about a particular type of utility function which someone pointed me to for that purpose.
I understand what you're saying about the tension. As someone trained in psychology, there's a litany of papers that 'solve the problem of not understanding' with little or no 'problem solving' benefit.
Having said that, I think those incentives are changing. In the UK and Australia, universities are now being evaluated and incentivised based on how well they solve problems (e.g. https://www.arc.gov.au/engagement-and-impact-assessment). I think, in general, your motivation and career would not be hurt by doing things that focus on engagement with people who have important problems, and helping to impact their decision-making. Personally, I think even the best 'solve the problem of not understanding' questions start with a problem in real life. I think medicine is a good example of where academic success is often directly correlated with how well your research either solves important problems or has promise to solve problems.
As a fledgling economist, however, I do see you point. There are strong incentives in some fields to come up with some new theory than to solve some existing problem. I guess this is true in medicine too, where there's more money on research for male pattern baldness than malaria (https://www.independent.co.uk/news/world/americas/bill-gates-why-do-we-care-more-about-baldness-malaria-8536988.html).
Still, I never dissuade my students from trying to solve important problems. Even if one of their studeis is something more 'theoretical', I try to ensure they're working backwards from the important problem that's worth solving. To your use example above, even if you do come up with a more general theory of philanthropic portfolio management, you'd hope that your intro and discussion could still speak to how it helps someone answer the policy question: "How much money should I allocate to x vs. y?"
One thing I'd point out is that there are many areas where solving problems does also lead to academic success. Systematic reviews are cited to the hilt because they try to solve an important problem ("what works?"). Knowledge translation is a whole field of taking stuff trapped in universities and getting it out into practice to solve problems. Very very few interventions do economic analyses of their cost-benefit, and those that do often struggle to put a dollar value on the benefit. For example, in this study, we could calculate the cost per bit of childhood cardiovascular health, but couldn't put a dollar value on the bit of cardiovascular health: https://jamanetwork.com/journals/jamapediatrics/article-abstract/2779446 One of my deepest regrets was trying to focus my PhD on something that was theoretically interesting but practically far from helping the most disadvantaged (i.e., do you need to control or accept your emotions to perform under pressure?). I did this because I thought that was what you were 'supposed' to do, and because I thought it was interesting. If I had my time over, I would have started with a bigger problem then worked backwards to find the something interesting and 'at the frontier of knowledge.'
Thanks for your detailed reply. Absolutely, there is some academic reward available from solving problems. Naively, the goal is to impress other academics (and thus get published, cited), and academics are more impressed when the work solves a problem.
You seem to encourage problem-solving work, and point out that governments are starting to push academia in that direction. This is great, and to me, it raises the interesting question of optimal policy in rewarding research. That is supremely difficult, at least outside of the commercialisable. My understanding is that optimal policy would pay each researcher something like the marginal societal benefit of their work, summed globally and intertemporally forever. How on earth do you estimate that for the seminal New Keynesian model paper? Governments won't come close, and (I imagine) will tend to focus on projects whose benefits can be more easily measured or otherwise justified. So we are back to the problem of misaligned researcher incentives. But surely a government push towards impact is a step in the right direction.
Until our civilisation solves that optimal policy problem, I think academia will continue to incentivise the pursuit of knowledge at least partly for knowledge's sake. I wrote the post because understanding the implications of that has been useful to me.