Tl;dr: My model for science is that it is like mining outwards from a point. This offers predictions that extend beyond Scott Alexander’s foraging metaphor and sometimes disagree. The mining metaphor emphasises the fact that research exposes new research problems; that research is much slower than learning; and research can facilitate future learning. The model offers actionable advice to researchers (e.g., “avoid the piles of skeletons” and “use new tunnels to unexplored rock-faces”). In part II, I also object to the idea that it is concerning that a smaller proportion of people are now “geniuses”, arguing that this would be true even if the importance and difficulty of intellectual feats achieved was constant because of the way in which genius is socially constructed.

This post is a response to some recent interesting posts that are well worth reading:

Why we stopped making Einsteins by Erik Hoel
Contra Hoel on Aristocratic Tutoring by Scott Alexander
Follow up: Why we stopped making Einsteins by Erik Hoel
The Low-Hanging Fruit Argument: Models and Predictions by Scott Alexander

I. Science as Mining

Scott proposed a neat model for how research happens, which is similar to mine but has some important differences.

Imagine some foragers who have just set up a new camp. The first day, they forage in the immediate vicinity of the camp, leaving the ground bare. The next day, they go a little further, and so on. There’s no point in traveling miles and miles away when there are still tasty roots and grubs nearby. But as time goes on, the radius of denuded ground will get wider and wider. Eventually, the foragers will have to embark on long expeditions with skilled guides just to make it to the nearest productive land.

He adds the idea that some people are taller (smarter) than others and can reach higher branches. There’s also a time limit (death), which means speed matters.

Scott explains that this model makes some predictions:

Early scientists should make more (and larger) discoveries than later scientists.

Early scientists should be relatively more likely to be amateurs; later scientists, professionals.

Early scientists should make discoveries younger (on average) than later scientists.

These trends should move more slowly for the most brilliant scientists.

These trends should fail to apply in fields of science that were impossible for previous generations to practice.

I actually disagree with 1 and we’ll see why in a bit. I basically agree with the next three of these, so I won’t focus on them. But where I think it gets interesting is the fifth one, because we can easily build a similar model where this isn’t an exception but a core part, but which has different predictions.

Imagine that at the dawn of time humanity is placed in a small cave in the middle of a vast expanse of rock. Through a happy coincidence, for some reason they have some picks and shovels. They get to work digging in all directions, removing rock, finding ore, and turning the ore into useful stuff. Research is that digging, and the social value of the research (the utility generated) is the value of that ore.

Here’s the key. Removing rock and mining ore doesn’t just give you material to work with. It exposes new rock! When researchers do their work, they don’t just generate results, they provide new questions/techniques/tools/equipment which future researchers can work with. It is not an accident that we can now work on problems that Newton didn’t have access to, nor that we have TPUs and he didn’t. It’s part of the plan.

And this means that research can get harder over time, but it can also get easier, especially if you’re good at spotting the newly exposed easy rock or if you’re good at guessing where the best ore is.

Let’s think about a few more details of the model before we get to our predictions.

It turns out, the dimensionality of the space is super important.

Imagine the world was 1-dimensional (a line). Digging rock exposes exactly the same amount of rock. Adding extra researchers barely helps, because you’ll always proceed at the rate of the fastest digger.

Imagine now that the world is 2-dimensional (a plane). After humanity has done a bit of digging, the exposed surface is now bigger than it was at the start. The number of researchers can grow with time and you could still always have the same ‘research surface area’ for each of them.

In higher-dimensional spaces, this is even more true. In really high dimensional spaces it goes nuts. There could be many more possible research questions and approaches available now than there were a few centuries ago.

What is the actual dimensionality of idea-space? I don’t know. But I’m pretty sure it’s a lot bigger than one. Discovering a new statistical tool can unlock new discoveries in a thousand other disciplines. Learning how to work a new material can unlock measuring devices that can revolutionize a thousand problems. This isn’t an accident, it’s a core part of science.

It is a key part of my intuitions, but something I can’t really prove, that the dimensionality is high enough that humanity can’t ever learn all the things. We have to pick and choose which problems to solve, so our exploration of the mine will look more like a block of cheese with some big holes and other small ones and less like a giant hollowed-out sphere.

One last detail. In this story, some rock is easier to dig through than other rock. Also, some ore is much more valuable than other ore. There is no a priori correlation between the value of ore and the hardness of rock around it.

Note also that your travel time is dominated by your digging time. Research is much slower than learning something from a textbook. And doing the research is a necessary first step to writing the textbooks that others can learn from. We’re digging tunnels that others can use and some tunnels are more direct than others. (This is in contrast to the foraging model, where covering ground is no easier for future generations than the first.)

Here are our predictions:

Over time, unanswered questions that are easy to ask will be hardest to answer and progress on questions people have cared about for a long time will be slow.
The highest return-on-effort will be exploring questions that are only just now possible to work on.
Over time, the skill of identifying problems-worth-solving will dominate the ability to solve problems.
(Disagreeing with Scott) Early scientists might make more (or larger) discoveries per researcher. But they might not, especially in aggregate (because of surface-area scaling).
We might be very wrong about how hard it is to learn any given new thing (‘lost in the tunnels’).
Over time, it becomes extremely hard to judge the rate of progress in science.
Early work will generally seem like it was more important than later work, and this is partly a mistake.

Let’s go through those in turn.

1. Over time, unanswered questions that are easy to ask will be hardest to answer and progress on questions people have cared about for a long time will be slow.

Even though we assumed at the start that there isn’t any correlation between the value of ore and the hardness of rock, it will quickly look like there are patterns. Distance to the rock-face is something like ‘how hard is it to ask this question’ (maybe because you need to learn a lot before you know how to ask it, or because your concepts block you from framing the right question). If you come across a problem quickly, it’s probably really hard to solve. That’s because if it weren’t someone else would have already mined the rock away from the ore. So only the really hard rock is left near your starting room.

An archetypal example of this might be Fermat’s last theorem. It turns out it was possible to prove, but by the middle of the 20th century it was already easy to deduce that it was very hard to prove.

This will make it look a lot like all the easy stuff has been done, and there’s a sense in which that’s true. This is the core intuition behind Scott’s model, which this one shares.

Critically, it will make it seem like progress is incredibly slow on attacking the ‘great questions’, which are the questions that are so persistently and obviously important that people have been working on them for centuries. Yes, progress on these questions will be very slow. But it’s a failure of imagination to think that these are the questions to which the answers are most important. I think when people have the intuition that research progress is getting harder it is because they are anchored on questions which are already widely acknowledged, but these are outliers.

(I want to clarify that it isn’t always a waste of time to work on these questions, partly because working on them might be a wisdom-generating procedure, rather than a scientific procedure.)

2. The highest return-on-effort will be exploring questions that are only just now possible to work on.

A corollary of the last result is that your time is best spent on rock-face that hasn’t been exposed until recently. Ideally this will be rock-face that doesn’t take too long to get to, but which people haven’t spent a lot of time working on.

There might seem like there’s a problem. If the rock-face has only just now been exposed, won’t it take forever for me to get there? There are some fields like this. For example, in theoretical physics you really don’t become able to do interesting work until after your PhD (at least according to my theoretical physics tutor, which is part of why I chose not to go into theoretical physics).

But, it is entirely possible to have problems that took ages to be accessible but which aren’t actually hard for individual researchers to reach. Someone has built a new tunnel which reveals that the rock face isn’t even that far away anymore, even though the original tunnel was pretty long and windy. Machine learning is one of these fields. Building TPUs was ridiculously hard. Inventing Transformers was, in contrast, pretty easy. Right now, learning how a Transformer works well enough to contribute to the state-of-the-art probably takes about a year or two for a smart person with the right aptitude and good mentors.

Crucially, this isn’t an accident or a violation of the model. People doing research will open up new tunnels that expose new rock and you should use this fact.

3. Over time, the skill of identifying problems-worth-solving will dominate the ability to solve problems.

For really early researchers, there was just one room. You could dig at the north wall, or the south wall. But basically you were here and didn’t have that much choice.

For researchers today, you can quickly get lost in the sheer variety of questions that can be posed and answered. Say you buy a shiny new genetic sequencer. You could sequence anything. And then you’ll have tons of genetic data. And you can correlate that with any measurable phenomena. Humanity could probably devote its entire research-effort to this one research programme for the entirety of its existence and never run out of questions to answer.

Of course, a lot of those questions will be pointless.

For researchers today, and even more so for future researchers, there is so much rock-face available that merely walking up to the closest rock and getting to work is a bad plan. In fact, it’s a terrible plan because of our first prediction (it’s likely to be really hard). But even once you avoid the obvious failure mode of trying to solve the ‘great questions’ that people have been working on for centuries, you have a ridiculous wealth of options to pick from. And most of them either have no ore behind them or low-value ore.

The real knack will continue to be for guessing correctly which rock is easy to dig and which rock has valuable ore behind it. This will grow increasingly true as the rock-surface-area grows, which it will as more research gets done. (Strictly speaking, you need an extra effect to change the probability that any given piece of rock is less likely to be worth digging into, which is that the people before you have already exercised judgment about which rock is worth digging and were on average more right than not.)

This will give the impression that there is a huge amount of competition in the obviously hot spots, because researchers will swarm around these areas in a feeding frenzy, ignoring spots where the rock/ore proposition is uncertain.

But if people aren’t aware of this fact, and keep working on areas that were historically valuable, they will indeed have the impression that ideas are harder to come by than they used to be. They will be right, in the context of that limited field. If they really only care about that field, fine. But an alternative choice is to move on to new fields!

4. (Disagreeing with Scott) Early scientists might make more (or larger) discoveries per researcher. But they might not, especially in aggregate (because of surface-area scaling).

The contrast here has partly come out in the above points already. We shouldn’t assume that the rock near the start is any easier to mine than rock further away, or that the ore near the start is more valuable. The important thing for the individual productivity of each researcher is the ratio of rock-difficulty to ore-value.

There are two mechanisms for this ratio getting worse over time (like in Scott’s model). First, as you dig more it takes you longer to get from home-base to the rock face. Second, early researchers can get rid of all the easy rock.

But the early researchers also wasted a lot of time on hard rock. This gives later researchers a massive head start because you can avoid the piles of skeletons. Just don’t waste your time on the questions people have been beating their heads against for centuries. For some reason we focus a lot on people like Newton and don’t spend nearly enough time learning about where the skeletons are piled high.

Researchers on fresh rock-face can make good progress. And if they are clever about using new tunnels they can get to new rock-face easily. This is because of the second big difference to the foraging model - that traveling is much faster than digging.

Are the discoveries are larger? There are a couple different senses of magnitude. One is whether the ore itself is more valuable. I basically think there’s little reason to think that the ore near home is most valuable. There’s a slight bias in that questions which are easier to ask are probably more fundamental to the human condition, so answers to them might have deep value. But the answer to “How can I cheaply manufacture ammonia?” turns out to be much more valuable than the answer to “Is birch bark stronger than cedar bark?” despite being ‘further from home’.

So is it actually true in reality that early researchers made more and larger discoveries? I honestly don’t know. It can look like that when you read histories of science. But I’m suspicious. First, because we don’t include people who wasted tons of time on dead-end pseudo-scientific investigations in those histories. For every Newton there were countless forgotten researchers asking questions which later turned out to be incoherent or unimportant not to care about at all (for example, Newton). Second, we’re really bad at the recent history of science. If you read a good history of science in the 20th century you’ll find it’s mostly a history of science 1900-1950. That’s not because all the good research was in the first half of the century - it’s because it takes a huge amount of time to digest all that progress and tell a coherent story about what happened.

There’s another sense of “larger” which might be important. Is it true that earlier discoveries have more counterfactual impact because of their downstream consequences? I’ll discuss that below.

While I am unsure about whether individual research productivity is higher now in new fields or was historically in new fields, I’m fairly sure that the aggregate progress in research now is higher (and especially that it could be higher if we invested more in it and if we stopped wasting time on questions that we have really good evidence are very hard). This is because the exposed surface-area of rock-face is so much larger and we can usefully employ more researchers without them doubling-up. However, this does require actually coordinating to not all focus on the same new problems, and also avoiding traps.

5. We might be very wrong about how hard it is to learn any given new thing (‘lost in the tunnels’).

One consequence of the tunneliness of science is that you can’t see very far. You quickly become disoriented. You might have been traveling for days, but maybe you’ve been going in circles. Your travel time is also dominated by digging time, so you could spend a lifetime just on making someone else’s journey faster.

As a result, our intuitions about distance in the mines are terrible. It might be that there’s a shortcut that someone is about to build, and that other people will learn in an afternoon what we spend a lifetime discovering (and think it trivial).

That’s actually a good thing for research. The quicker we can get other people to fresh rock-face, and the more we can guide people to promising bits of rock-face, the quicker people will make research progress. (I’ll pass on whether that is good, but it’s something a lot of people want.)

6. Over time, it becomes extremely hard to judge the rate of progress in science.

There are two main problems with judging progress in science. One is that distance is so shifty. A huge contribution to science is to build a new tunnel that makes an under-explored bit of rock-face quicker to get to. But in doing so you actually cause new researchers to perceive that there has been less progress so far than they would have otherwise thought. (This is one reason that researchers often obfuscate their work to highlight how long their journey was, not how far they have come.) Over time, as you get better and better at bringing new people to the rock-face you’ll actively be hiding some of your hard work by bypassing it, and this is good. It also makes the historical journey falsely look very smooth in comparison with current research, which again contributes to the mistaken impression that modern research is much slower and worse than historical research.

The other is that we can’t see very far, and the bigger our mines become the less of the overall picture any one person can have. I try to read pretty broadly and do my best to keep up with wide-scope journals like Nature, but I’d be lying if I said I understood a quarter of what I read there. Even worse, I have a pile of literally hundreds of papers in my specific sub-field that I think I really ought to read but haven’t quite gotten around to yet. How on earth can I comment on the rate of progress in science generally when I literally don’t even know all of what is currently happening in my little corner? More disturbing again is the knowledge that there are new fields emerging that I ought to know about but I don’t even know enough to know I’m behind on reading this. I think basically all curious researchers feel this way.

This comes back to the difficulty of constructing histories of recent science. It’s just super hard, and we should be wildly suspicious of anyone who claims to know what the rate of scientific progress is even in any one field, let alone taking into account the emergence of new fields over time.

7. Early work will generally seem like it was more important than later work, and this is partly a mistake.

There are two advantages early work can have over late work in importance. First, early work can be used sooner, thereby generating value over a longer period of history. Second, early work unlocks future work and becomes important in that way.

I think this is super subtle. One thing going on is that counterfactual impact is hard to assess. E.g., if Newton hadn’t discovered calculus it would probably have barely mattered since Leibniz had a very similar discovery at about the same time independently. And even if you needed non-Euclidean geometries to discover special relativity, presumably some of the value of relativity still accrues to Einstein?

But our brains are bad at subtlety. So we’ll end up giving all the credit to the person who happened to be first, even if they only sped things up by a year or so. And we’ll pick out a few salient good stories and assign the credit there. And salient good stories are easier to construct when the underlying dynamics are simple. That means we’ll tend to overweight credit for things that happened a long time ago, because this gives us time to simplify the histories through intellectual effort and convenient forgetting. So I think we’ll tend to feel like early work was generally more important than it was, just as we’ll tend to think it was easier than it was.

In conclusion to this part, I think there’s a natural model for scientific discovery where it isn’t inevitable that we pick the low-hanging fruit. The key assumptions driving this result are that research exposes more research and that learning is much faster than research. Mining is a useful metaphor for this. The model also has important consequences for individual researchers picking problems (e.g., “avoid piles of skeletons” and “look for new tunnels to unexplored rock-face”).

II. Are we missing geniuses?

All of this started with Erik’s argument for aristocratic tutoring as a way to generate geniuses. I have no idea whether or not aristocratic tutoring or any other kind of tutoring is good or optimal for any purpose whatsoever, and I’m not going to comment on that. I agree that finding ways to improve education seems valuable, and learning from how great thinkers were trained historically is probably a good place to start, with the caveat that the current education system is not obviously trying to produce great thinkers.

But what I do take issue with is the idea that we have some big crisis of missing geniuses. The key problem is a confusion about what a genius is.

A genius is not just someone who is super smart. We’re pretty sure we have as many smart people today (proportionately) as we ever did and probably more.

A genius is also not just someone who achieves a difficult intellectual feat. Building some fantastic Minecraft creation might be a work of absurd difficulty, but there’s also a sense in which it basically doesn’t matter and isn’t even quite in the category of art, and not enough people care.

A genius is also not just someone who achieves an important intellectual feat. Imagine you have 100 researchers working in some sub-field, and one of them makes a discovery of tremendous value to humanity. Suppose that’s enough to call them a genius. Now imagine all of the other researchers make discoveries of similar magnitude, just because that sub-field is super hot and practically anyone working there is bound to do something important. Are they all geniuses? Or suppose someone finds a tablet from an alien civilization which clearly states in English the secret to eternal life. Are they a genius?

Maybe? But it doesn’t feel that way to me. It feels like they were in the right place at the right time, and that’s good for us, but not a sign of genius.

So maybe a genius is someone who achieves an intellectual feat that is both important and difficult? I think this is getting there.

But what makes an intellectual feat difficult? Difficulty is a sneakily comparative concept. For weight-lifting, I guess difficulty is how heavy the weight is. But intellectual discoveries don’t come with a number representing their difficulty. To a certain extent the proxy we use for evaluating difficulty is that other people had the chance to discover it but weren’t able to.

So what happens as the surface area of problems gets bigger? We have people attacking new fields that others had no chance to attack yet. Were they geniuses? Or were they in the right place at the right time? We’ll never know.

We have fields that are so far away from each other that nobody in one field is in any position to assess what happened in another one. It becomes almost impossible to generate inter-field consensus about the importance, let alone the difficulty, of problems.

The point is that our capacity to recognize geniuses is constrained by our capacity to acknowledge intellectual feats as being difficult, and this is in turn a hard (and social) problem. In my own sub-field, we might be able to come to the conclusion that some people are doing really outstanding work. For example, I think David MacKay was probably a genius. But probably most people even in the broader fields of machine learning, coding, and climate science, all of which he touched, don’t know who he was. And certainly he will never get name recognition across a wide range of fields. (For those who don’t know, his book Sustainable Energy Without the Hot Air was very influential on early 80,000 Hours and EA thinking about the value of back-of-the-envelope cost-benefit-evaluations and holds up surprisingly well today.)

As fields become more distinct from each other and as the number of people involved becomes bigger, the social-intellectual problem of sorting out which ones completed unambiguously important and difficult intellectual feats becomes harder. We therefore would predict that it becomes harder to identify people as geniuses as science progresses even if there is no change in the difficulty or importance of the work being done.

As a result I don’t disagree with Erik that the proportion of people alive who are geniuses is shrinking, but because of the weird nature of ‘genius’ as a partly comparative socially-constructed label I disagree that this is directly evidence of any problems with the importance or difficulty of intellectual feats being achieved.