Should people go to university?
Chris Olah: I applied for the Thiel Fellowship, which is a program that provides financial support for people under the age of 20 to go and work on ambitious projects or do unusual things, and I got it, and I was like, “Well, I have two options. One is to go back to university, and the other is I can work on whatever I want for two years.” It turns out that wasn’t a difficult decision.
Chris Olah: I had a lot of experience in doing things cutting against pressure, from the previous stuff. But I think at the time, I framed it — and especially framed it to other people — as, well, I can do this for two years, and then I can still go back to university. That seems like an amazing opportunity. One other thing that comes into play here is it’s actually much easier to do unusual things when you’re validated by a third party. I think people, when they hear about the Thiel Fellowship they’re like, “Ah, the high-value thing is that they’re providing funding.” That’s certainly part of it, but I think that actually the higher value thing was actually like, adults in my life totally came around once I was given $100,000 to go and work on stuff, in a way that they really were not supportive in beforehand. I think there’s also just a really big effect in terms of legitimizing an untraditional path and making it easier.
Chris Olah: I get a lot of emails from people asking me if they should go to university. I think it’s maybe the single most common question I get asked. I think for almost everyone who emails me, they should go to university. The reason that I think that is I think that if you want to benefit from going and doing something else, you have to have a lot of, I think, self-discipline and willingness to go and work hard on things, and self-motivation to work hard on things without an external forcing function. I think that often people don’t have this, and then this kind of thing doesn’t work as well for them.
Chris Olah: On the other hand, I think for the people — and maybe to give some more context, — I think a lot of the people who I saw really thrive in the Thiel Fellowship, some had already before the age of 20 done undergrad degrees. So there were those ones. But I think a lot of people had done really significant personal projects involving software or science or something like this. I think that’s actually a pretty good test. If you have been able to, out of self-motivation, go and do your own large personal project — and obviously you are in a privileged enough position to be able to support yourself — then you’re likely to be able to do well in something like the Thiel Fellowship, or taking a year off, or taking a few years off. But if you aren’t, it’ll be much more challenging.
See also Chris’ essay on whether people should go to university.
Lessons from Chris' unconventional career track
Chris Olah: I think probably the most useful thing I’ve extracted has been thinking about the Pareto frontier of skills. For example, a lot of my early contributions to machine learning were basically being able to create these really helpful illustrations of complicated ideas. What skills did I need to do that? Well, I needed both to understand machine learning, and I needed to be able to draw. I wasn’t an exceptionally good artist or scientific illustrator, and I wasn’t exceptionally knowledgeable about machine learning. But very plausibly, for a while, I was the person in the world who was the best of the intersection of machine learning and drawing. If you think of these two-dimensional plots of different skills, or three-dimensional plots of different skills, and you think about the Pareto frontier, very often society is good at producing people who are optimized for a particular skill set or set of skills that society has really validated as useful.
Chris Olah: We create entire pipelines training people. But I think that often, if you can find useful intersections of skills that aren’t these couple of standard skills, there can be a lot of value. And it’s much easier to go and have a big impact, and often have a big counterfactual impact. When I’m talking to people about their own careers, I often try to frame it in terms of, what are the skills that they’re cultivating, and what do we think the Pareto frontier with regards to these skills looks like? Do we think that there’s places where, rather than going and becoming the world’s best at one skill, they can produce a lot of value by being at an intersection of skills that other people don’t have?
Rob Wiblin: Yeah, that’s really interesting. Thinking about it theoretically, I suppose part of the reason is just that there’s so many combinations of two different things that you could throw together. So the space of possible combinations is vastly larger, and so you have a lot more to choose from. It also means that you could be the only person who’s interested in X and Y, if you choose two things that are sufficiently distant. Then you have a truly unique skill set, and you might just stumble on something that no one else has even tried to find.
Chris Olah: Exactly, and now the problem is the space is exponentially big, and you want to not just find an intersection, but the intersection has to be useful. So you have to have some taste in picking the skills that you develop. But I think that there are lots of opportunities like this, and that often it’s much less competitive than going and being good at one of the skills that society already really values as a thing to optimize for.
Developing research taste and technique
Chris Olah: I think it’s often helpful to divide being a good researcher into two parts. One is taste. So your ability to go and pick good problems and go and pick good avenues to attack those problems, and things like this. The second you might call technique, or execution. Maybe if you picture a chemist working with vials and pipettes and weird things, it’s pretty clear that there’s a whole technique to going and manipulating that laboratory equipment.
Chris Olah: I think that it’s subtler in other fields, but I think that there is something — certainly in machine learning, of the technique of training models, and even just being a good programmer, and doing very minute things of manipulating your code editor, or going and manipulating distributed systems, and stuff like this — I think that there’s a question of how do you develop both of those skills. And for taste, I think that’s probably the hardest one to develop. I tried to come up with a list of exercises that one could do. An example, and I think probably the most useful one, is just write down a list of problems that you think might be important to work on, and then have somebody else, ideally your mentor, go and just rate them one to 10.
Chris Olah: Because one of the really hard things about developing taste is that you have such a slow feedback loop on learning lessons, because you have to go and do the entire project. What you want to do is use a mentor or use somebody else as a cheap proxy for getting feedback, and then if you disagree with their feedback, you can either talk to them about it, or maybe you even want to go and do that experiment. I think that could be useful. I think there’s lots of other things. I think reading about the history of science is helpful. I think going and trying to write just about why you think things are important is helpful. In any case, I think there’s a bunch of exercises there. Then, on the technique side, I actually think the most valuable thing here is working closely with people who have good technique.
Chris Olah: I think actually, at least in machine learning, and probably other computer science disciplines, going and pair programming with people is immensely valuable. I think that there’s a lot of stuff that’s hard to communicate in other forms, but gets passed along when people are pair programming. I think for developing technique, often pair programming is the highest leverage thing to do.
See also Chris’ notes on building research taste.
Chris Olah: I get a lot of cold emails, and 99% of them are terrible. They’re like, “Can you do my homework for me?” or, “Can you answer this basic question that I could Google for one minute and answer?” I think people get this impression that cold emailing doesn’t work, because of course, if you send emails like that, people are overwhelmed and aren’t going to respond. Or, even if you just very generically are like… If you send a nicely written email and you’re like, “I’m trying to get into machine learning. Can you do a half-hour phone call with me to talk about how to do that?” Even that, you’re not very likely to get a response from. But I think the thing that people miss is that if you write really good cold emails, it’s actually not that hard to be the best email I received that week.
Chris Olah: And I think that if you’re willing to invest energy in understanding what a researcher or a group is working on, and you’re specifically referring to their papers, and you have thoughtful questions about things, yeah, I think that people will pay a lot of attention to that. Then I think that it will… It very often works well. I think there’s a big gap in what people mean when they talk about cold emails, and I think that if you’re willing to put in the work, and if you just genuinely really care about what somebody is doing, and have put in the work to understand it, and can talk about it really intelligently… That’s going to come through. It’s a much more compelling reason for the person to talk to you than other things.
Chris Olah: I think there’s a lot of people who are trying to look at how to get into machine learning, and what they do is they send lots of emails to people, or they email famous people. I think what you should actually be doing is trying to figure out who you would be really excited to work with, and really understand their work. Ideally pick somebody who’s a little bit less famous maybe, and then reach out to that person with an email where you’ve put a lot of work into it being clear that you’ve read their work, and connecting your interests to theirs, and things like this. There’s a number of emails that have been really important for me, where I spent a week writing them. I think that was a totally worthwhile investment. I think that’s not how people usually think about cold emails.
Research as a market
Chris Olah: The general idea is, you think of researchers as investing in different research ideas, and if the research idea pans out, and other people don’t grab it before them, then they get some reward from that maybe. Maybe more resources, or just they get a payoff from that in some way. You can see there being this competition to go and grab promising research ideas. I think there’s roughly two strategies that you can play in this market. One is you can work on things where everyone really agrees that they’re important, and that are really popular.
Chris Olah: And what you’re doing when you do that is you’re going and making that little area of the research market a tiny bit more efficient. You’re going and making it so that ideas that are important to get done, get done a little bit more quickly. And I think that is actually genuinely a valuable thing to go and do. If the thing that you’re doing is really important, and you make it happen in expectation a week earlier or a month earlier, that’s really great. But the other strategy you can do is you can try to beat the market. You can try to work on things where you just can see that something is undervalued relative to what most of the community thinks. That’s the thing that I try to do a lot of the time. And there’s lots of reasons why you might be able to beat the market.
Chris Olah: It could be that you just care about things that other people don’t. If you care about safety, or in other areas, if you care about animal welfare, or if you have weirder goals, or different goals than a lot of people, you might be able to beat the market in that way. I think another way, though, is just, if you have some insight that you really believe is true about a problem, and that’s not a widespread insight, then that could be really helpful. That can be… I feel like that’s a lot of what I’m doing, me personally. I think that you can genuinely understand neural networks if you’re willing to input enough energy into trying to figure out what’s going on. It’s a big bet that I’m making, that most other people aren’t making.
Chris Olah: I think in many fields, achieving a research-level understanding is like climbing a mountain. There’s all of these ideas that you have to understand and build up towards before you can go into research.
Chris Olah: Mathematics, I think, is a really striking example of this, where there’s just years and years of ideas that you’re probably going to spend climbing to the point where you can do research, because there’s just so much that isn’t piled on top. Then when you get to the top, you go and you pile some more results on top, and you make the mountain higher.
Chris Olah: I think a lot of people are proud of this, because they’re like, ah, the fact that it’s this long pilgrimage to go and get to the point where you can do research, that means that it’s especially profound, and it reflects all of the work that’s been done to date. But I think that, actually, it’s often a reflection that we haven’t put enough work into explaining things, building up really good infrastructure for learning about that field. I think this is going to come in lots of forms. It can be poor expositions, just not good explanations to things. Sometimes it’s just undigested ideas. There’s an idea that’s important, but it hasn’t been really refined to the completed version of that idea. I think it’s very common for there to be bad notations, or just bad definitions of things that make things more complicated, and all these things make it harder to go and understand the topic.
Chris Olah: One analogy that I like is sometimes in software engineering, people talk about technical debt, which is you move really fast to get to that point where you can ship some feature or something like this, and in the process, you write lots of bad code, and it’s really messy and gross, and you have bad variable names, and it isn’t documented, and then it’s hard for other people to build on top of. I think something analogous, a kind of research debt, is endemic in science.