(Note: Look for an upcoming article by @kman about a research program for adult human intelligence amplification. If you are interested in working on this, please do reach out.)

S: So, where are we with adult intelligence amplification?

T: Unfortunately, there aren't any clear pathways right now. There is no biotechnological intervention that we know of, where there's a clear argument that if you do that intervention, it would likely significantly increase the general cognitive capacities of an adult human. There are several approaches that are hopeworthy, but each one would be very expensive to pursue.

T: On a strategy level, I'm most hopeful about more roadmapping work. Past drive-by efforts at roadmapping haven't worked. But it seems plausible that there are ways to significantly accelerate adult intelligence amplification, and it's just hard to tell what they are without thinking about it a bunch.

So, I'd want us to collate a bunch of information about brains, intelligence, and various technical areas like brain-computer interfaces, brain surgery, brain genetics, neurophysiology, drugs, and so on. Then we'd ask big ambitious engineering questions with all that stuff at our fingertips, come up with ideas for how to do adult intelligence amplification, bounce ideas off each other and off of domain experts, break the ideas, go back to the drawing board, learn more, and so on. That way we might come to understand where to invest larger amounts of resources, in order to accelerate adult human intelligence amplification.

Existing technoscientific investigation might be somewhat efficient in a forward-chaining way, but it seems likely that it's quite inefficient with respect to the overarching goal of meaningfully increasing adult human general intelligence or other cognitive capacities. There has been very little concerted effort to increase general intelligence in healthy adults through biotechnological interventions. As a consequence, gathering the relevant information into one discourse, and asking questions from the perspective of adult human intelligence amplification, is not something that's been done before, anywhere, by anyone. This sort of roadmapping seems not unlikely to produce a lot of insight into how to accelerate HIA.

S: Ok thanks. I was more interested in hearing concretely what approach you think has a decent chance of working.

T: It's really hard to say. There's currently no good way to know what sort of intervention someone could do to their adult brain to noticeably increase their general intelligence, let alone hugely increase it. So there's a big strategic problem of "What even would be the technical intervention I want to technologically enable?"; we don't even know what kind of technology we'd want to develop. And then you have to actually implement the intervention, which will be its own big difficult technoscientific project.

S: Ok... But it seems like there's a lot of levers one could pull. There's a lot of surface area (literally and figuratively) on the brain. And we could explore this somewhat efficiently, maybe? And then hill-climb on combinations of interventions. For example, there's a bunch of genes associated with higher IQ, right? So we could maybe edit a bunch of those genes and hope that many of them can still take effect .

T: Yeah, much of my hope in adult cognitive amplification comes from the fact that there are several different kinds of interventions, and lots of surface area within a given kind of intervention.

T: Definitely. I mean, it's definitely possible that it might be a good approach to investigate.

S: Ok. Is there a project working on this? Should we make one?

T: At least given the information I have, it doesn't seem like the thing to do at the moment.

T: Concretely, one main reason is that it's hard to get into the brain. To edit neurons in the brain, you want to get molecular complexes, such as CRISPR-Cas9 plus RNA, into the brain and into neurons. You want to do that repeatedly, into many or most cortical neurons. To get stuff into the brain, one natural method that people have tried is to put the stuff into the bloodstream, and wait for the stuff to be carried by the blood through the brain. But the body wants to protect the brain from viruses, waste, toxins, etc., so there's a barrier of tightly packed cells that encases blood flowing through the brain. Only specific kinds of things can pass through that blood-brain barrier. It's not easy to make the gene-editing molecular complexes pass through the blood-brain barrier and into the brain tissue. See [1] :

There are methods to deliver molecules to the brain that don't involve passing molecules through the blood-brain barrier. For example, spinal taps have been tried, though that method applied specifically to gene editing is still in early development [2] .

S: That makes sense, but do you think that's an insurmountable obstacle? Couldn't we make progress by, like, trying? Human intelligence amplification seems really important, so even if it's hard, it seems worth some people working on it.

T: There are already people working on it, for some value of "it".

A general lesson to understand, beyond the concrete obstacle of the blood-brain barrier, is that bottlenecks tend to be convergent subgoals .

If you have some ambitious goal X, you might notice that no one else has announced "I am trying to do X". You might therefore think that your efforts to achieve X will be highly decorrelated with other technoscientific investigations. If no one has been working on X, then you aren't duplicating the efforts of other investigators because your work doesn't overlap with their work.

Indeed, it's plausible that no one, or very few people, have been working on X. However, [ an abstract spiel about why you'll probably end up duplicating efforts anyway ; see the subsection " Appendix: Bottleneck subgoals tend to be shared across ultimate goals "]. Basically, many of the problems you'll get stuck on, as you work toward X, are probably problems that other people are also stuck on, even if no one else was working toward X specifically.

S: This is a bit abstract. Could you illustrate the idea more with an example?

T: For instance, we might have the goal of massive brain gene editing, or massive stem cell editing for reprogenetics. Starting from either of these, we have the following subgoals, each a subgoal of the previous subgoal in the list:

S: I'm not totally sure I buy the example. I feel like in your progression down subgoals, you also make each subgoal more broad, which explains why more people are working on it. But anyway, I think I at least get what you're trying to say. Popping up the stack, for brain gene editing, you're basically saying, people are already working on crossing the blood-brain barrier?

T: About more broad subgoals, part of the point is that, as you backchain further from your top-level goal, you have to broaden the subgoal. Unless you know exactly what you need from the subgoal, you have to broaden the scope of pathways you're considering, and so you overlap more with preexisting efforts. And in other ways you'll be duplicating effort with other people working on similar things, e.g. you'll inherit any shared sub-sub-goals that apply to the whole set of similar things.

Anyway, yes, people are working on crossing the blood-brain barrier, because that's how you would deliver any sort of drug to the brain. It's a convergent subgoal. In particular, people want to do gene therapy for brain diseases, so at least some people have been trying seriously to get gene editors into the brain.

More generally, people want to intervene on the brain for all sorts of reasons—implants, drugs, editing, cancer treatment, other surgeries, and so on. For that reason, lots of people want to get into the brain, and lots of people have to deal with the barriers to brain access, including the blood-brain barrier, the skull and meninges, and the immune system. So there are existing methods for getting into the brain, and convergent difficulties with improving those methods.

S: I'm still not getting something... Ok, I accept that getting editors into the brain is an important technical obstacle to brain gene editing, and I accept that people are working on it, so it might be a bit difficult to accelerate... But still, can't we put a bunch of resources into this? We care a lot about intelligence amplification, so we could put more funding and talent into research on this, and be highly determined in our efforts.

But one important part of being truly determined to solve the problem is to take the time to back up and think hard about what approach to the problem will be feasible. In particular, there's nothing stopping you from going down a path that leads to nowhere, or at least, nowhere that's especially relevant to your goal of increasing intelligence. Science is hard, and biology specifically is very hard. I think it's quite plausible that we could accelerate progress in some specific areas, even if someone else is already seriously working on it.

However, because it's simply hard, and because someone's already working on it, it's probably not easy , and specifically not cheap , to accelerate progress in that area. It would take quite a lot of money and/or work. I know I'm being a bit of a downer here. It's just that money and effort are not in fact unlimited, and talent is not unlimited (at least until we succeed). I think we have to think hard about which pathways to invest in, before going deep into one pathway, if we want to make good use of our resources.

In the case of the blood-brain barrier, you might rush off to join the gene therapy people, and see that they are working on adeno-associated viruses as delivery vehicles to carry gene editors into the brain. You could work on that for years, and substantively contribute to technical progress there. And that would be great! But at some point, hopefully quickly, you might realize that AAVs are too small to carry enough DNA specifying gene-targeting RNAs to have much of an effect. You might realize that AAVs are likely to provoke immunity, so they can't be used for more than one or a few rounds of editing. Since you need to do hundreds of edits to even possibly have a large effect on intelligence, you can't achieve that using AAVs. Then again, maybe that's not right; maybe you could use several variations of your AAV to do several rounds of edits! We don't know.

Assuming that investing effort into AAVs was some kind of error, what exactly was your error? One error is presuming that subtechnologies will generalize the way you wanted. Your goal of HIA led to the subgoal of getting gene editors into the brain. You share that abstract subgoal with the brain gene therapy people. But it turned out that their gene therapy requirements (a vector for one round of editing) come apart from your intelligence amplification requirements (vectors for many and/or large rounds of editing).

Zooming out, I think the fundamental error is failing to start out with thinking hard about how to amplify adult intelligence. Before we've understood more about the problem, we are not able to make good decisions about where to invest resources. Once we've understood more, we'll know more about how to accelerate toward that goal.

For example, maybe if we investigated more about the blood-brain barrier and AAVs, we'd realize AAVs won't work, but instead we find out about fetal cell microchimerism in the brain (h/t GeneSmith) [4] . Cells from a growing fetus enter the mother's bloodstream, and some of them (or at least, some DNA from them) end up in the mother's brain. Maybe that turns out to point to a more promising editor delivery method.

If we don't investigate, we won't realize that there are somewhat disjoint technoscientific pathways that predictably have very different expected utilities for adult intelligence amplification. Any one piece of information about a specific pathway might come easily from a day of literature search, but there are very many such pieces of information needed to get a good picture of the relevant technoscientific pathways.

S: Wait hold on. You just said that the AAV thing was an error because subtechnologies don't have to generalize the way I want, so accelerating the AAV research that people are already working on will end up being mostly a waste of my effort. But your argument from earlier was that it's hard to accelerate brain gene editing because people are already working on it. Is this a contradiction? You're saying that the important subgoal is already being worked on, but also that accelerating that subgoal doesn't help?

T: You're right. I'm contradicting a general version of my argument that goes like:

You can't accelerate X because X requires convergent subgoal Z. Other people are already working on subgoal Z and they are probably doing it fairly efficiently. So you can't accelerate X much by working on Z.

But the way I'm contradicting that argument isn't that now I think "Actually you can accelerate solving the Z problem in general .". That still seems directionally unlikely to me. (Of course, how unlikely will depend on the specifics.) What I want to say now is:

Actually, there are different versions of the subgoal . If you think hard, you can distinguish version , which people are already working on, from version , which people are not working on, but which is what you need in order to do . Then you can accelerate and thereby accelerate . If you just try to accelerate , you are liable to try to accelerate the wrong version of , and furthermore you probably won't make much progress because people are already working on in general. (Separately, even if you do identify the right thing to accelerate, you'll still have overlapping subgoals with other people working on .)

S: Is it actually so bad to go down "the wrong" path for a little bit? The way people gain experience and skills is by getting their hands dirty.