Nick Bostrom, Direktor des Future of Humanity Institute in Oxford, spricht über seine Karriere und High-Impact-Forschung. Eine Auflistung der bedeutendsten Erkenntnisse:
- Meta-Forschung ist äusserst wichtig. Wir sollten die Gesamtsituation betrachten und die wichtigsten Fragen identifizieren. Hier gibt es noch grosse Unsicherheiten.
- Schon allein das Nachdenken über den Impact unserer Forschung bewirkt etwas. Die meisten WissenschaftlerInnen scheinen sich nicht darum zu kümmern, wichtige Forschung zu betreiben; jedenfalls denken sie nicht gross darüber nach.
- Für die Förderung von High-Impact-Forschung sind vermutlich junge ForscherInnen die beste Zielgruppe. Es ist allgemein schwierig, etablierte AkademikerInnen zu einem Umdenken zu bewegen; junge Forscher sind offener.
- Geldmittel in wichtigere Forschungsgebiete zu lenken ist eine weitere Möglichkeit, eine grosse Wirkung zu erzielen.
- Grosse Unsicherheiten bestehen auch darüber, welche Forschungsfragen die wichtigsten sind. In dieser Situation können wir uns auf solche Meta-Fragen konzentrieren, um die Unisicherheiten zu reduzieren, oder uns mit Fragen beschäftigen, die in jedem Fall wichtig erscheinen, unabhängig davon, in welche Richtung sich die Unsicherheiten auflösen (safe bets).
Das Interview mit Nick Bostrom wurde von Jess Whittlestone und Rob Wiblin von 80’000 Hours durchgeführt.
Tell us a bit about how you ended up where you are now
For as long as I can remember, I’ve been interested in the potential for changing the human condition in some fundamental way, and how this could have a huge impact. This was back in the days before the internet was popular though, so I had no idea of anyone else who was interested in this. In the meantime I just tried to learn enough to put myself in a better position to work on these things later on. Later when I came to London as an exchange student I discovered there were other folk out there discussing similar things.
I had a bit of an intellectual awakening aged 15 or 16; before that I hated school. The realisation that there was a world of learning, ideas, culture, art and philosophy much more interesting than what we were being taught made me hate school even more! I felt like I needed to make up for lost time, so I started to guide my own studies: picking up lots of different subjects that seemed relevant. Once at university I tried to study many things in parallel. But there was a cap on how many subjects you could enrol in. At one point I actually got expelled from the psychology faculty for studying too much!
How did you get to setting up the Future of Humanity Institute in Oxford?
After my PhD I went to Yale, and then came to Oxford as a British Academy postdoctoral fellow in philosophy, where I met more people interested in the same things as me. I tried to find topics in philosophy that would be acceptable to academic philosophers while still being relevant to the world, such as anthropic reasoning and applied ethics. The circumstances that led to me creating the FHI were very fortuitous: the Oxford Martin School was just in the process of being founded which made it possible. There was a huge amount of luck here: if the money for the Martin School had been given to Cambridge instead, for example, it might not have happened.
What do you think are some of the best ways to find high impact research areas?
There could be very high leverage opportunities looking at the bigger picture and trying to figure out what is important and what should be researched, because there are still very large uncertainties involved here. You could come at this from a variety of different disciplines: philosophy, computer science, maths, economics, neuroscience etc.
Something else to bear in mind in terms of your impact is that in some fields the problems are pretty much predetermined, so your efforts go to speeding up progress on these problems; in others there’s more room for manoeuvre and you can actually change which problems are dealt with. The humanities, philosophy, and interdisciplinary fields seem to fall into this second category, whereas in science it’s often clearer where the big problems are.
Why do you think certain really important questions get neglected?
This is a difficult question. One way to answer it would be to turn the question around: why do the things that do get studied, get studied? Often it’s because they’ve been studied before and a discipline has been established, which can lead to a great deal of inertia. The concept behind some of the questions that are important now are fairly new, which explains why they haven’t been studied in the past. The opportunity to develop artificial intelligence, nanotechnology and cognitive enhancement haven’t been around for that long. Another factor is that a lot of these questions are very interdisciplinary and there’s no standard protocol for investigating them.
An even more frugal explanation for why people don’t focus on the most important questions is just that they don’t care that much. There are plenty of people who might care if they thought about it more, but they just don’t reflect on the importance of their research. This is where you can make a big difference just by encouraging people to think about the world in terms of impact.
How important is your choice of thesis topic?
There’s a risk of getting pigeon-holed by your PhD, and it’s easier to write one more article when you’ve already done a lot of research on a topic, so your choice of thesis area is important in this respect. It’s also four years of your peak intellectual period so you don’t want to squander this time unnecessarily. On the other hand, few people will ever actually read your PhD thesis.
It can be quite common, at least in philosophy, to enrol in a PhD program before you have a good topic and then spend the first year choosing your thesis idea. But disciplines can vary a lot in this respect: in the life sciences you probably have to chose before you start.
It is possible to shift your focus after your PhD. If you find what you are studying isn’t that useful you should seize that opportunity. Unfortunately it is more difficult to change departmental field.
What about specialising vs. generalising: which do you think is better? Is it best to try and be a T-shaped generalist?
I’ve never made that sharp a distinction between different academic areas: wherever there’s stuff I find interesting I just learn that. But for the most part I don’t think academia rewards this attitude. That said, if you are lucky enough to find the right entry point, there can be good opportunities in multidisciplinary fields.
I think T-shaped generalising might help you in the long run: if you can pull it off you’ll probably be more productive and creative. But in the short term, it can slow down your career. Your chances of getting a postdoc and then tenure might be higher just by focussing exclusively on something that’s fashionable in your field.
It seems like in most fields, the top few researchers often seem to get almost all the attention. Do you have any tips for increasing your chances of becoming one of these top researchers?
In some fields, having a big impact is a matter of doing something unique. In philosophy, doing something slightly crazy is a way to get minor fame. For instance, you could choose an outlandish position and defend it better than people believe is possible. This is not not an activity I would recommend. But to become one of the top people you have to go beyond competent, solid work, and take some risks or go out on a limb somewhat, for example by showing that some common conception is false. I would imagine it’s similar in other humanities and social sciences at least.
If you can get into an elite university I think that can make a big difference. This might seem obvious to people in the UK and USA, but it’s less obvious elsewhere. In Sweden, for example, there isn’t much difference between the various universities, so it’s less clear to people that some universities can be way better than others. Having a “brand name” university is useful not just for intellectual development but also in terms of opportunity: for grants, media impact, collaborations and so on. At a less recognised university these things are possible but it’s more of an uphill struggle. It’s unfair, but nonetheless true.
That said, maybe sometimes there is a case for ending up in a middle rank university and being a “big fish in a small pond.” There might be more flexibility to do exactly what you want, for example.
What about influencing other academics to think more about impact – how easy do you think this is to do?
It’s hard to get established academics to change their views, unless they spontaneously become interested in a topic, or bear a latent interest for a topic they were unable to pursue in the past. If you can show them a way to get funding, they may well look at it again.
Otherwise, there’s probably more leverage in influencing people who are just entering the academic world. At the FHI we’ve done this thesis competition to get people to write a thesis outline on some important topic, with a prize for the best one. They don’t actually have to write their thesis on it, but the idea is to get people spending time thinking about important areas, which will hopefully at least increase the chance of these areas getting researched.
How easy is it to influence what research is conducted by getting into a position of power in an organisation that provides funding and grants?
A lot of the grants in academia actually end up being dispersed by the academics who conduct the evaluations. Even when someone higher up in a funding body is trying to set priorities, it’s hard for them to change how the money is used on the ground. At each stage in the chain of management, the goals are shifted slightly, until the intention of the top-level managers is largely forgotten.
Probably in the natural sciences it is easier to exercise control than in the humanities. Presumably you could get a lab to work on one vaccine rather than another. If you’re funding a big group working on some structured project it’s easier to impose control, but in fields like philosophy where you’re funding individuals it’s difficult to influence what they end up thinking about.
Is there more opportunity to pull funding sideways from within academia, then?
In philosophy it’s hard to pull funding because there’s just not much money. But there are other opportunities for academics to pull money into more important fields, and this is arguably better than getting onto the board of a funding body.
Other things equal, it’s much nicer to take money from some big organisation which has a bad focus. Then you are simply rescuing the funds from being wasted. But in fact I think it should be fairly easy to make much better use of funding than the average academic – even without any particular competence, just caring about getting funding into important areas puts you above the many others who don’t. So there’s no need to go out of your way to try to get your funding at the expense of the least effective projects.
Finally, if you could give just one piece of advice to a student wanting to make a difference through research, what would it be?
There’s a lot of uncertainty in our understanding of the world and it’s really difficult to know what is valuable. This is why working on meta-level questions and trying to figure out what’s important might be a good option. You have to know which direction to start walking before you set out on your journey. Another good tactic would be to focus on projects that are robust in the face of great uncertainty. Making people generally more benevolent and compassionate might be an example of this: it’s hard to see how that would turn out badly. The bottom line is that it’s not all that obvious yet what research is most important, so think twice.