How to choose a research topic: An interview with Anders Sandberg

Ben and I spoke with Anders Sandberg, a James Martin research fellow at the Future of Humanity Institute, about his career, how to make a difference through research and how to choose a research topic. We’re going to be writing in more detail about some of this in the near future, but here are some highlights from our conversation:

  • General advice for students interested in doing high impact research: spending a lot of time thinking it through can make a big difference, and sometimes small or unglamorous innovations can have the most impact.
  • Some heuristics for finding high impact research areas: look for under-researched fields, find problems that affect a lot of people, try adding a new twist to a big problem, being a generalist
  • Things to be careful of: some problems seem huge and important but might be ill-posed and so hard or even impossible to solve. “Solving consciousness” or “curing cancer” are good examples of this.
  • More specific ideas of what research questions might be promising: certain areas of neuroscience focused on improving human well-being, communication and cooperation, anything that makes it easier to acquire or multiply human capital.
  • Why scientists aren’t working on these things and general barriers are to doing high impact research: inheriting the research agenda of your professor seems a big problem, as well as aversion to risk and uncertainty.

Formula

A quick biography

Anders’ research focuses mostly on cognitive enhancement and future technologies, with particular interest in cognitive biases, technology-enabled collective intelligence, neuroethics and public policy. His background is in computer science, neuroscience and medical engineering. He did his PhD in computational neuroscience at the University of Stockholm, Sweden, focusing on neural network modelling of human memory (the focus of which he tweaked towards memory enhancement). He co-founded Eudoxa, a think tank analysing how society and culture are changed by technology and scientific progress.

What do you wish you’d known when you were a graduate student?

I knew I wanted to be a scientist ever since early childhood. What a scientist was, on the other hand, I had a very uncertain view of. I figured out what science was about the time I got my PhD! Quite often we go through life without getting good advice or knowing where to ask for it. Often people in academia completely lack information about what’s going on around them. I’m still completely baffled by grant writing for example, I’ve no clue how you actually get a research grant. Which is a bit worrisome of course. If something like 80,000 Hours had existed with a subsection on academia I would have been reading that part of the website, talking to the local representative with interest.

What general advice would you have for someone wanting to do high impact research?

By deciding more carefully you can make a lot more difference. Be careful of just inheriting a research topic from your supervisor: this is a big problem and your advisor won’t necessarily choose the best topic for you. It’s also worth bearing in mind that sometimes small findings can do the most amazing things, and unglamorous innovations can matter a lot. Take Norman Borlaug and the Green Revolution for example. What he did had a huge impact but wasn’t totally revolutionary. He just put the pieces together in the right way and convinced a bunch of people.

What do you think are some good heuristics for doing high impact research?

One idea is to go for under-researched fields. Progress in a field is typically a very convex learning curve: rapid progress at first when the low-hanging fruits get picked by the pioneers, followed by slowing progress as the problems get harder and it takes longer to learn the necessary skills to get to them. So the same amount of effort might produce far more progress in a little studied field than in a big one. (Of course, the field better matter too - computational pencil sharpening algorithms could be revolutionized by anybody investigating it, but who cares?)

“It’s going to affect a lot of people” seems to be a good heuristic. Using my own field of neuroscience as an example, it’s pretty obvious that the brain affects a lot of people: it’s a big deal!

If you think you can add a different twist to a new problem because you have experience from another field, that can be particularly useful, as you have a better chance of having a big insight.

It can also help to turn the question around: what aspects of human life matter? Looking at human life, we sleep about a third of the time, and there’s very little research into how to enhance sleep. Understanding the health effects of what we eat is probably worth billions of pounds per year. But there are no financial incentives here. Maybe a simple approach for finding high impact research areas might be to look at the most common google searches: you can get a pretty good idea of what human behaviour matters a lot!

What about things to be wary of: areas that might seem high impact but aren’t?

If a problem has resisted a lot of effort, that should tell you something about it: it might be that people are coming at it from the wrong approach, so it might be high impact. But more likely that it’s a really hard problem or even an ill-posed problem. The “war on cancer” is a beautiful example of that. It made sense for Nixon to declare a war on cancer because he believed it was a problem, but as it was more researched it was realised that it was a lot of problems but there was no cure for cancer. Many of these “big problems” may later on turn out to be pointless, so I’m sceptical of going after them.

Being able to evaluate what you’re working on, having some kind of importance check, and setting your priorities straight is really important. This is a bit like time management: it’s a really useful skill. I’d take being able to do this over an intelligence enhancing pill!

Do you think it’s better to be a generalist and get a broad understanding of a lot of things, or to specialise early and really focus on a single area you think is high impact?

I’ve found that being a generalist gives you a certain connoisseurship. It allows you to distinguish “good research” from “bad research” to some extent (although maybe not when you get into the nitty gritty details.) You can get a rough sense of what’s going on. It’s also relatively cheap to do as the learning curve is steepest at the beginning: if you just read an introductory textbook as bedtime reading, you can get on this part of the curve. I can’t do any seismology, or marketing or brain imaging, but I certainly have an idea of what’s roughly going on in these fields, which can be very useful later on. I’m very much in favour of learning loads of stuff that’s likely to turn out to be useful. Over the history of my academic career my most useful courses have been linear algebra, all the statistics and probability theory I’ve been able to pick up, some basic computer science, and a course on natural disasters. Linear algebra, for example, is very general and crops up everywhere: if you use it in a field not familiar with it you can do some really amazing stuff. Around here (at the FHI), we’re fairly good at maths and statistics, which means we can do parts of ethics that normally ethicists can’t handle.

Even if you do focus on one field, knowing enough about other fields is good as you can recognise when you need the help of someone from another department. Far too many people have no idea at all that they can make use of other departments. Knowing how to use data is also incredibly useful. In a lot of domains people don’t look much at data. But actually being able to get that feedback from reality is so amazingly useful: that’s of course why randomized control trials are so important!

What are some specific areas of research you think are important?

Neuroscience in general I think: it’s a tough field and there are a lot of people working on it, but there are a ridiculous number of subfields and it’s pretty clear we don’t know much about a lot of areas. There’s a lot of focus on the neurosciences, but it’s under-resourced in the sense that the money isn’t going into the most important places.

Things like dementia, depression: mental illness in general are an enormous drain on humanity, and if we could do something about them that could be a really big deal. Figuring out how our decision making works and making it better, and making our emotional lives better, are also going to have an enormous impact on our quality of life. But it’s a bit unclear what we’re going to find. Anything that improves communication abilities or cooperation abilities of people is going to have a huge impact: on the neural side, figuring out how to better learn languages, or how to make social media work. Plus anything that makes human capital easier to acquire and multiply: better education, cognitive enhancement, downloadable skills. Also risks of wars and democides tend to dominate the tails of my disaster distributions - reducing the risk of lethally bad governance might have a big impact.

I’ve got a specific research question that seems obvious to me and I haven’t found anybody investigating it. You have a learning system building hierarchical representations based on simpler knowledge: this is all standard deep learning stuff you find in typical textbooks. The problem is, as it continues to learn, how do you keep your representations stable? How come we don’t overlearn standard things like walking, familiar faces, or how our own bedroom looks? Typically with an artificial learning system if you show them something like this too much it will crash. How come we don’t crash when we see our own bedrooms? We seem to be completely stable against this. Understanding this would be really useful not just in artificial intelligence and neuroscience but in a lot of domains.

Why do you think scientists aren’t already thinking like this in looking for important research questions?

I think in general scientists are a lot less rational about what they research than they should be! There seem to be institutional reasons why people go for very narrow fields. The problem in neuroscience is that if you get into it it’s very likely your professor is going to try and niche you into some very narrow subfield: this makes for great papers but you’re probably not going to solve any important problems. Inheriting your supervisor’s research agenda is a big problem. I ended up doing several years of memory research because of a deal between my professor and an institute: it wasn’t really my choice. In philosophy of course people typically select topics themselves, but again, do they do it for rational reasons?

What other barriers are there to doing important research?

Looking at some of these under-researched fields, the problem is that a lot of them don’t even exist as fields. Typically you’re unlikely to get funding in unknown fields as well: unless you’re a really good salesman! So one heuristic would be to look at the topics you know, do a matrix and look at the interactions: which areas do you see that have nobody doing anything in?

When I went to a computational neuroscience conference last year, I was slightly depressed as I saw a poster which was exactly the same research topic as my last poster! It was pretty clear the young grad student had reached the same conclusion I did, and had never heard of my research which was published 6 years ago! Many fields have this problem that they don’t have very much of a memory, which affects progress.

Fields like AI are struggling because there’s no good way of comparing progress. How much smarter are current general AI programs than some of the classics? Nobody knows, and you can’t test the older programs because the source code and everything has been lost except a few bizarre papers from the early 70s.

Finally, if you could give just one piece of advice for a student wanting to really make a difference with their research, what would it be?

Many great discoveries have been due to serendipity. But you should try to place yourself so that regardless of whether you find what you were aiming for or something different, it will really matter.

Thanks for talking with us - it’s been incredibly interesting!

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