(Note: I was unsatisfied with a draft of this, heavily edited it, and I'm still unsatisfied. The notion of "weak HIA method" here is muddled, maybe conflating multiple things that shouldn't be conflated here. It may be used a bit inconsistently, and may make some arguments tautological or contradictory depending on local interpretation of the notion. I think most of the reasoning is still useful, so it's better to publish, but beware, and please critique. Or more importantly, please investigate HIA.)
Summary
People sometimes ask:
Why not prioritize human intelligence amplification methods that will provide small increases in intelligence, over stronger methods? They'll be easier to develop.
The two main reasons to prioritize strong HIA methods are:
There are increasing returns to higher intelligence, so strong methods unlock much more value.
Empirically, weak HIA methods don't seem that much easier than strong HIA methods.
There are other structural issues with weak methods. For example, they seem likely to be hard to make legible, and therefore hard to test and to scale up to lots of people; and they tend to provide a way to avoid the hard problem of strong HIA without much benefit. A key challenge is simply to have a good reason to think a method will genuinely increase general intelligence at all; once you have that, you probably have a method that can be developed into a strong HIA method anyway.
That said, weak HIA methods would be fantastic. I mainly want to suggest that someone who wants to pursue weak HIA methods should keep in mind the pitfalls described in this article.
Context
Why not weak HIA rather than strong HIA?
A promising idea is human intelligence amplification (HIA), i.e. enabling people to be smarter if they want. I generally focus on HIA methods that would have large effects on intelligence; see e.g. this overview of strong HIA methods.
A question people sometimes ask is:
Wouldn't it be strategically better to develop weak HIA methods first rather than strong HIA methods? Since we're asking for less, it would be easier to develop, and therefore faster and more impactful.
This argument does hold some water. In particular, it partially successfully argues that if you actually have a weak HIA method, scaling that method up quickly is valuable. But, this article will explain why efforts aimed at developing new strong HIA methods are generally more promising than efforts aimed at new weak HIA methods.
Weak vs. strong HIA methods
These terms are vague, but to give some arbitrary cutoff points:
weak HIA: add <1 SD of intelligence.
medium HIA: add 1—2.5 SDs of intelligence.
strong HIA: add >2.5 SDs of intelligence.
(This article leaves aside the important question of: What other aspects of cognition, besides general intelligence, would it be good if people were enabled to amplify in themselves?)
An HIA method is some core technological principle. (Analogously, the core technological principles of a jet engine are "propulsion via Newtonian reaction" and "combustion under high pressure".) Examples include "adult brain gene editing", "BCIs to massively increase internal connectivity", "BCIs to network people together", "signaling molecules to induce fast learning", and so on. An HIA method could be developed into a body of technoscientific knowledge, protocols, and institutions which can give people weakly or strongly amplified intelligence.
I'm not totally sure what I mean by "research specifically aimed at a weak HIA method". I mean to point at a cluster including:
Plans that come from a theory of HIA that visibly couldn't extend to strong HIA.
Or more generally, plans that don't have a good theory for how they could extend to strong HIA.
Plans that don't have a good justification for why we should expect them to produce genuine increases in general intelligence.
(It may seem strange to call this "research aimed at a weak method", but I think in fact people often make this substitution—they say they want to pursue a weak method, and then settle for weak motivating evidence.)
Plans where the justification is that we're intervening on some aspect of the brain that's probably related to intelligence somehow; and therefore it's plausible we can slightly increase intelligence.
Plans where the justification is that we have some very weak (noisy, small, based on subjective report, hard to interpret, not clearly general) evidence of an effect of some intervention on intelligence.
Plans where the justification is that the intervention does noticeably improve cognitive ability in a group that has a specific impairment, by alleviating the impairment.
Main statement
In general, relative to investing in strong HIA, I'm somewhat unenthusiastic about investing much in attempts specifically aimed at developing weak methods for human intelligence amplification.
The central reasons:
There are significantly increasing marginal returns to more intelligence, in terms of benefit to humanity.
Someone can increase their net expected benefit to the world by a much larger amount if they go from 130 IQ to 160 IQ, compared to if they had gone from 100 IQ to 130 IQ [citation needed]. This implies that a change in probability of having strong HIA is worth significantly more than a change in probability of having weak HIA (which would be the conversion if gains were linear in IQ points).
In other words, for it to be a good bet to work on a weak HIA method instead of working on a strong HIA method, the weak method would have to be quite a bit more feasible than the strong method.
The ease of developing a weak HIA method that isn't also a potential strong HIA method is somewhat of a mirage.
Of course, logically, it must be easier to do weak HIA than strong HIA, because strong HIA also qualifies as weak HIA.
But, as far as I can tell in advance, weak HIA methods that would plausibly work are just early versions of strong HIA methods. Being able to do HIA that's genuinely general but weak, tends to also mean you can probably do strong HIA by developing that method further.
In the light of these central reasons, on current margins, I'm less enthusiastic about attempts that target the development of weak HIA, compared to attempts that target strong HIA. I'll give a bunch more specific arguments below, but these are the main reasons in summary.
Why weak HIA attempts don't seem so promising
Unpromising properties
There are several reasons that attempts to develop a weak HIA method don't seem like they'll work. Such attempts, at least the ones I've seen so far, tend to have the following properties:
They don't improve general intelligence.
Rather, they improve some narrower faculty such as alertness, focus, need for sleep, emotional regulation, etc.
These improvements can be useful, but seem likely to be qualitatively less useful than increases in general intelligence. For example, they seem unlikely to significantly raise someone's ceiling for how complex an idea they can comprehend or invent, or to change their learning rate by 3x (which we know is possible because existing people do exhibit such differences!).
To put this a different way, if a weak HIA method does have a good case that it improves general intelligence, my guess is that you could figure out how to do that method but more strongly. I.e., you're actually working on a strong HIA method! (This is a way to view the fact that polygenic embryo selection is the first weak HIA method: the strong case that this method is a genuine albeit weak HIA method is also a strong case that strong reprogenetics can be a strong HIA method.)
In yet other words: There's a central barrier to true HIA. The barrier is: How do you get the information you'd need in order to know what interventions actually increase general intelligence in humans? (See examples in the overview of methods.) If you've overcome this barrier, you've probably got a potential strong HIA method.
They probably aren't very stackable.
That is, multiple of these weak HIA methods can't be combined to get a medium or strong HIA method.
For example, many interventions people use are stimulants of various kinds. Taking more stimulants hurts rather than helps past a point.
However, some interventions do seem partly stackable. For example, one can take caffeine plus some other nootropic; and a good night's sleep additionally helps. Someone pointed out to me that it's possible that more substantive interventions could stack if they're interventions of very different types. For example, one could imagine using some BCIs, while also using some brain drug that increases learning rate, in order to more quickly take advantage of the new capabilities possibilized by the BCIs.
So the more precise statement is: to get stackable weak HIA methods, you probably have to develop multiple quite different-in-kind HIA methods. If they are the same-in-kind in the relevant sense (something like, going through the same channel), they're likely to saturate. (Why doesn't this apply to reprogenetic HIA? It could, but probably not, because reprogenetics can access the rich variety of neural / developmental mechanisms controlled by the genome.) Developing multiple different-in-kind HIA methods multiplies the difficulty.
Further, many of these interventions help only as ways to remedy cognitive impairments. To put it another way, they don't stack with already having reasonably well-performing cognition.
They're not very serious attempts.
That is, the attempts seem insufficiently determined, and insufficiently anti-inductive against previous failed attempts.
In other words, the people working on them will probably give up after a while. They won't recurse on solving whatever underlying problems prevented their initial success.
(This doesn't actually argue against you deciding to work on weak HIA. But it does mean that you're in a somewhat down market for philanthropy, so to speak. And it does suggest that you may want to check the extent to which you're serious; my guess is HIA will turn out harder than you currently think. I think it's great if you try a bit to figure out some weak HIA, and then move on to something else. It just might be helpful to be realistic with yourself and with others about your prospects for success, given your degree of determination.)
They're not that easy to experimentally iterate on.
The effects of these interventions are weak, and may be non-general, subtle, noisy, and varying between people. They may also take weeks or months, say, to exhibit themselves.
Further, most or all cheap straightforward measurements of intelligence that exist, such as particular IQ tests, are trainable.
Therefore, it may be logistically difficult for a small group of people to do longitudinal exploratory experiments that get a good read on what interventions help themselves, let alone other people. The feedback loops are not as good as they might intuitively seem.
In addition to being trainable, measurements of intelligence may be cheatable, i.e. not robust to someone adversarially trying to get a falsely high score. Therefore it may be logistically hard to conduct research distributed across many people. Those people might cheat the test, e.g. because they're self-deceived or because they want to get some selfish gain such as attention for its own sake. I believe that in fact, historically, there has been quite a bit of noise in the marketplace of ideas among amateur investigators trying to find surprisingly easy weak HIA methods. Plausibly, this high noise rate kills some or much of the would-be benefit of very easy experimentation.
They're not cheap and legible enough to easily scale.
The benefits of having an HIA method increase a lot (linearly? superlinearly?) with scaling up to have more people who benefit from that HIA method. Thus, scalability is crucial. Weak HIA methods have some structural features, inherent to being a weak method, that make them probably in the same ballpark as stronger HIA, in terms of difficulty of scaling.
Getting a good night's sleep is a legit weak HIA method, compared to not doing it. So why doesn't everyone do it? Various reasons, but the point is, for most people it's not that hard to make the needed changes. But the changes are too expensive for what they care about. So something like a quarter or more of US adults get poor sleep.
E.g. if you can get some substantive intelligence boost by using transcranial electric stimulation for 40 min / day, that's still kinda inconvenient actually; comparably inconvenient to putting your phone away and going to bed at a reasonable hour.
Further, it's hard to demonstrate weak effects convincingly. This may sound a bit obscure, but I think that in fact the history of weak HIA attempts is littered with many exciting claims which were either false, or true and approximately no one picked up on.
(That may be due to problems other than legibility, such as side effects or the intervention only working on a few people. But we can see from this history that for whatever reason these methods did not end up with huge numbers of people adopting them (unless you count caffeine, nicotine, and a few other things like that). Whatever those reasons are, they make weak HIA methods hard to scale. There is one major exception, which is education. Education definitely increases scores on IQ tests, and we spend a lot on it. But it's unclear how much, how long-lasting, and how truly general those effects are. See e.g. Ritchie et al. (2018)[1].)
(Just to be clear, removing lead from the water and iodizing salt is fantastic and should be done; it's just that you can't remove lead twice, so to speak.)
Without scale, the case for weak HIA feels significantly less strong. If millions of people were a bit smarter, that matters; but if it's hundreds, then it doesn't seem like it matters that much in the grand scheme of things.
They're not on a tech pathway to medium or strong HIA.
That is, the interventions people consider tend to fail to tell us much of anything that would get us closer to medium or strong HIA.
For example, the low-hanging TES / TMS tools may all be very blunt, i.e. stimulate only big sections of the brain in a few ways. Trying to squeeze a bit of HIA out of that doesn't help get you to some hypothetical medium HIA TES equipment; to help with that, you'd ideally be experimenting with more precise TES, or at least figuring out what sort of more precise TES might possibly help a lot more than the current blunt one.
For example, interventions on the level of increasing or decreasing neurotransmitter levels or binding various receptors may all, collectively, be moving within a manifold that doesn't contain easily accessible medium or strong HIA. If so, then learning about various weak HIA regions of that manifold doesn't tell you much that's relevant to a strong HIA method. (Unless it does, IDK.)
For example, you could increase blood flow to the brain. (Korpan points out that caffeine is a vasoconstrictor but doesn't seem to decrease intelligence, evincing that increasing blood flow maybe doesn't help.) Even if that does increase intelligence, what are you learning that tells you how to get medium HIA? You're not going to just keep increasing blood flow and keep getting gains, I don't think. (Unless you are, IDK.)
If instead you're seriously concentrating on building up the deeper understanding needed to get to medium / strong HIA, then I would just call that bona fide medium / strong HIA research.
More reasons
The idea of "do weak HIA now; use that to figure out strong HIA faster" doesn't make much sense to me on current margins.
Of course you keep trying things and take the easy wins.
But if it's a choice between having 5 full-time researchers figuring out strong HIA vs. having 4 of those and also 1 person bothering the other 4 to take piracetam, I'd definitely put the 5 on strong HIA. That seems much more likely to lead to strong HIA quicklier. In other words, deciding to work on weak HIA instead of strong HIA is by default a big hit on the degree to which your cognitive abilities are being put toward developing strong HIA, so if you want to claim that your decision is net accelerating strong HIA compared to the alternative of directly working on strong HIA, you'd have to make up for it with significant boosts to other strong HIA researchers.
BUT, if there were, like, 15 focused on strong HIA as such, then maybe the 16th person should work on weak HIA, or something like that. In particular, if the strong HIA researchers are building up deeper understanding, that might start to be cash-out-able in easy-ish weak HIA methods; you'd want to pick up those gains.
That said, this argument is a real cost to working on reprogenetics rather than an adult HIA method. The early weak gains from an adult HIA method (even one aiming to be a strong method) could become available to HIA researchers themselves much faster than the early weak gains from reprogenetic HIA (e.g. polygenic embryo selection or weak embryo gene editing).
Weak HIA methods have been tried a bunch with not much apparent low-hanging fruit, beyond things like sleep, not over- or under-eating, maybe caffeine, and similar.
I worry that weak HIA is a kind of off-ramp or cope, in response to the difficulty of strong HIA. That is, weak HIA might be pursued by people who are bouncing off of the harder problem of strong HIA. I would rather those people reconsider whether they might want to more determinedly pursue strong HIA after all.
As an aside: Someone might say, "It sounds like you made a fully general argument against weak HIA methods; but you also said that polygenic embryo selection for intelligence is such a method!". I would point out that in fact, polygenic embryo selection for intelligence has been somewhat slow to scale, partly due to some of the reasons I list:
It's not that cheap.
It's not that legible, especially the intelligence benefits.
Why has it scaled as far as it has, up to now? Probably the main reason is the disease risk reduction benefits, rather than the intelligence benefits.
This does suggest that a non-HIA motivation is a good way to develop technology building up to an HIA method. For example, BCIs are proximally aimed at alleviating conditions such as paralysis or blindness. As another example, stem cell transplantation into the brain is being worked on to treat Parkinson's disease.
The question is, to what extent is there a gap between what will be developed for non-HIA reasons, vs. what would be needed for HIA? If the gap is zero or tiny, there's not much to accelerate. If the gap is small but substantive, it may be tractable to significantly accelerate. If the gap is large, it may be intractable to accelerate much.
Caveats
HOWEVER, all these reasons, and my overall conclusion, could easily be wrong, or not right enough. E.g.:
Caveat: Any specific argument could easily be wrong
Maybe a bit of creatine, plus lion's mane, plus transcranial electric stimulation, plus dual n-back, plus non-invasive brain readouts, plus a few different designer drugs, plus et cetera, could stack up to medium or even strong HIA.
Maybe someone could just decide to be very persistent about trying lots of different things and getting good reads on how well they are working.
Maybe someone could use weak HIA methods as wedges to learn more about the brain and intelligence, getting some kind of grounding in praxis while building up the intellectual background to tackle medium and strong HIA.
Maybe it's not that hard to develop a usefully repeatable measure of intelligence.
And I do weakly suspect there is medium-hanging fruit of weak HIA.
The next thing to test would be a very determined (and strategic, well-organized, publicly-documented) effort to find such interventions. (One theory for why previous attempts haven't really helped: the g factor is the result of many different brain elements, each of which wants to be tweaked very slightly. Each beneficial intervention has a very small effect, but if you successfully hit different pathways, the interventions can stack.)
Caveat: Weak HIA would be great!
To be clear: please don't take this as an argument against the absolute value of research on weak HIA. I'm saying all this for two main reasons:
To explain why medium / strong HIA methods seem relatively more promising to work on, compared to weak HIA methods.
To lay out some context for someone who does want to work on weak HIA methods anyway.
In other words, I would think it's somewhat likely to be a false and harmful outcome of this article, if someone gets discouraged from working on weak HIA methods! I would instead encourage such a person to consider:
You could instead work on medium or strong HIA.
You could work on weak HIA, and try to prove this article wrong and/or use the constraints and obstacles described here as guides for what to falsify or work around.
(And obviously you could just ignore and/or disagree with this article's assertions.)
Caveat: Weak HIA may have surprising beneficial effects
Some of my arguments depend on the assumption that the main benefit of an HIA technology comes from the contributions of the people who received HIA. But, there may be major benefits that come from even a weak HIA method, that change the overall calculation.
The arguments I gave above abstract over several different approaches to weak HIA. They're somewhat empirical arguments; they're abstracted from specific proposals that I've looked at, rather than some solid theoretical logic. So maybe, just, no one has happened to think of or try out the weak HIA method that would work.
Thus, I'm not very confident in any of the conclusions, and a near-totally devastating counterargument to this whole article could plausibly come in the form of "here is a novel, scalable, legibilizable, weak human general intelligence amplification method", and that would be great.
Caveat: Scaling a working weak method is a medium priority
Summary of section:
Weak HIA methods are beneficial, especially if scaled up to apply to many people, because nudging the distribution increases the high tails. However, to get the same increases on the high tails, a weak method requires, very very roughly speaking, 100x more scale than a strong method.
See "The power of selection" for some information about intervening on normally-distributed variables. The way I'm actually computing things is by memorizing rarities for integer SDs 1 to 7, and then in between I linearly interpolate of rarities. This is surprisingly accurate [graph generated by Fable-written code]:
Now: If you have a weak method that does actually work to increase general intelligence in humans, then it can be quite impactful to scale it way up. If you shift the distribution of g up by 0.5 SDs, you also shift the tail up. (This is assuming your method actually works on people already in the high tail, and gets taken up somewhat by those people.)
As a quantitative example: Suppose you scale up a weak HIA method so that 10% of people use it, and the people who use it are random (so in particular, lots of smart people use it). Suppose it works equally well on everyone, and adds 0.5 SDs to their g. How many more people with IQ ≥160 do we get?
The rarity of IQ ≥160, or +4 SDs, is roughly in . The rarity of IQ ≥152.5, or +3.5 SDs, is in . Those people become the new set of IQ ≥160 people, so the rarity updates accordingly. The difference in rarity is a factor of . Thus, within the population who uses this method, IQ ≥160 is about 7 times more common. In the overall population, you've made something like a 1.6x increase in the number of people with IQ ≥160.
This is quite a big impact. (I think scaling a method up this much will be difficult. Also, currently no method gives 0.5 SDs on average realistically, though polygenic embryo selection is close, and can do so in some cases.)
However, it's a small impact compared to what you can achieve with a strong HIA method. Suppose instead that, similarly, you have an HIA method that 1% of people use (rather than 10%). Now, this method shifts the distribution up by 3 SDs (rather than 0.5 SDs).
The rarity of IQ ≥115, or +1 SD, is roughly in . The rarity difference with IQ ≥160 is a factor of . Thus, within the population who uses this method, IQ ≥160 is about 5,000 times more common. In the overall population, you've made something like a 50x increase in the number of people with IQ ≥160. This is a far larger impact than for the weak HIA method, at 1/10th the scaling.
(Here I'm anchoring impact as a multiplier. I think this is reasonable because we have intuitions for "how much stuff there is in the world overall", e.g. how much intellectual progress gets made given the current distribution. But I'm unsure and interested in arguments on either side.)
So, there is a tradeoff between scaling vs. strength. What does this scaling look like? I may write this up in more detail later. For now I'll just say that it seems that, very very coarsely speaking, a weak HIA method requires about 2 or more additional orders of magnitude of scaling (i.e. 100x more people using it) compared to a strong HIA method, to get the same results in terms of increasing the high tail. See these widgets demonstrating this.
Thus, scaling a weak method is a medium priority, meaning it's very good but not as high a priority as developing strong HIA. However, if scaling is far easier than developing the technology for strong HIA, it could be a top priority.
Conclusion
Marginal strategically-guided effort towards human intelligence amplification should probably mostly go towards methods for which there are good reasons to think they can feasibly be developed far enough to give increases in general intelligence that are well over two standard deviations.
Ritchie, Stuart J., and Elliot M. Tucker-Drob. “How Much Does Education Improve Intelligence? A Meta-Analysis.” Psychological Science 29, no. 8 (2018): 1358–69. https://doi.org/10.1177/0956797618774253. ↩︎
(Note: I was unsatisfied with a draft of this, heavily edited it, and I'm still unsatisfied. The notion of "weak HIA method" here is muddled, maybe conflating multiple things that shouldn't be conflated here. It may be used a bit inconsistently, and may make some arguments tautological or contradictory depending on local interpretation of the notion. I think most of the reasoning is still useful, so it's better to publish, but beware, and please critique. Or more importantly, please investigate HIA.)
Summary
People sometimes ask:
The two main reasons to prioritize strong HIA methods are:
There are other structural issues with weak methods. For example, they seem likely to be hard to make legible, and therefore hard to test and to scale up to lots of people; and they tend to provide a way to avoid the hard problem of strong HIA without much benefit. A key challenge is simply to have a good reason to think a method will genuinely increase general intelligence at all; once you have that, you probably have a method that can be developed into a strong HIA method anyway.
That said, weak HIA methods would be fantastic. I mainly want to suggest that someone who wants to pursue weak HIA methods should keep in mind the pitfalls described in this article.
Context
Why not weak HIA rather than strong HIA?
A promising idea is human intelligence amplification (HIA), i.e. enabling people to be smarter if they want. I generally focus on HIA methods that would have large effects on intelligence; see e.g. this overview of strong HIA methods.
A question people sometimes ask is:
This argument does hold some water. In particular, it partially successfully argues that if you actually have a weak HIA method, scaling that method up quickly is valuable. But, this article will explain why efforts aimed at developing new strong HIA methods are generally more promising than efforts aimed at new weak HIA methods.
Weak vs. strong HIA methods
These terms are vague, but to give some arbitrary cutoff points:
(This article leaves aside the important question of: What other aspects of cognition, besides general intelligence, would it be good if people were enabled to amplify in themselves?)
An HIA method is some core technological principle. (Analogously, the core technological principles of a jet engine are "propulsion via Newtonian reaction" and "combustion under high pressure".) Examples include "adult brain gene editing", "BCIs to massively increase internal connectivity", "BCIs to network people together", "signaling molecules to induce fast learning", and so on. An HIA method could be developed into a body of technoscientific knowledge, protocols, and institutions which can give people weakly or strongly amplified intelligence.
I'm not totally sure what I mean by "research specifically aimed at a weak HIA method". I mean to point at a cluster including:
Main statement
In general, relative to investing in strong HIA, I'm somewhat unenthusiastic about investing much in attempts specifically aimed at developing weak methods for human intelligence amplification.
The central reasons:
There are significantly increasing marginal returns to more intelligence, in terms of benefit to humanity.
The ease of developing a weak HIA method that isn't also a potential strong HIA method is somewhat of a mirage.
In the light of these central reasons, on current margins, I'm less enthusiastic about attempts that target the development of weak HIA, compared to attempts that target strong HIA. I'll give a bunch more specific arguments below, but these are the main reasons in summary.
Why weak HIA attempts don't seem so promising
Unpromising properties
There are several reasons that attempts to develop a weak HIA method don't seem like they'll work. Such attempts, at least the ones I've seen so far, tend to have the following properties:
They don't improve general intelligence.
They probably aren't very stackable.
They're not very serious attempts.
They're not that easy to experimentally iterate on.
They're not cheap and legible enough to easily scale.
They're not on a tech pathway to medium or strong HIA.
More reasons
Aside: polygenic embryo selection
As an aside: Someone might say, "It sounds like you made a fully general argument against weak HIA methods; but you also said that polygenic embryo selection for intelligence is such a method!". I would point out that in fact, polygenic embryo selection for intelligence has been somewhat slow to scale, partly due to some of the reasons I list:
This does suggest that a non-HIA motivation is a good way to develop technology building up to an HIA method. For example, BCIs are proximally aimed at alleviating conditions such as paralysis or blindness. As another example, stem cell transplantation into the brain is being worked on to treat Parkinson's disease.
The question is, to what extent is there a gap between what will be developed for non-HIA reasons, vs. what would be needed for HIA? If the gap is zero or tiny, there's not much to accelerate. If the gap is small but substantive, it may be tractable to significantly accelerate. If the gap is large, it may be intractable to accelerate much.
Caveats
HOWEVER, all these reasons, and my overall conclusion, could easily be wrong, or not right enough. E.g.:
Caveat: Any specific argument could easily be wrong
And I do weakly suspect there is medium-hanging fruit of weak HIA.
The next thing to test would be a very determined (and strategic, well-organized, publicly-documented) effort to find such interventions. (One theory for why previous attempts haven't really helped: the g factor is the result of many different brain elements, each of which wants to be tweaked very slightly. Each beneficial intervention has a very small effect, but if you successfully hit different pathways, the interventions can stack.)
Caveat: Weak HIA would be great!
To be clear: please don't take this as an argument against the absolute value of research on weak HIA. I'm saying all this for two main reasons:
In other words, I would think it's somewhat likely to be a false and harmful outcome of this article, if someone gets discouraged from working on weak HIA methods! I would instead encourage such a person to consider:
Caveat: Weak HIA may have surprising beneficial effects
Some of my arguments depend on the assumption that the main benefit of an HIA technology comes from the contributions of the people who received HIA. But, there may be major benefits that come from even a weak HIA method, that change the overall calculation.
For example, a working, legible weak HIA method could garner much more interest in HIA, thus accelerating strong HIA. It could also help indirectly slow down AGI capabilities research by offering a tangible hopeful alternative to AGI.
Caveat: Flimsy foundations
Further: this is not a thoroughly researched article. I know about reprogenetics, but I don't know that much about other potential HIA methods, especially weak ones. See "Overview of strong human intelligence amplification methods" and "...Human intelligence amplification projects I'd like to see" for my opinions on specific HIA methods.
The arguments I gave above abstract over several different approaches to weak HIA. They're somewhat empirical arguments; they're abstracted from specific proposals that I've looked at, rather than some solid theoretical logic. So maybe, just, no one has happened to think of or try out the weak HIA method that would work.
Thus, I'm not very confident in any of the conclusions, and a near-totally devastating counterargument to this whole article could plausibly come in the form of "here is a novel, scalable, legibilizable, weak human general intelligence amplification method", and that would be great.
Caveat: Scaling a working weak method is a medium priority
Summary of section:
See "The power of selection" for some information about intervening on normally-distributed variables. The way I'm actually computing things is by memorizing
Now: If you have a weak method that does actually work to increase general intelligence in humans, then it can be quite impactful to scale it way up. If you shift the distribution of g up by 0.5 SDs, you also shift the tail up. (This is assuming your method actually works on people already in the high tail, and gets taken up somewhat by those people.)
As a quantitative example: Suppose you scale up a weak HIA method so that 10% of people use it, and the people who use it are random (so in particular, lots of smart people use it). Suppose it works equally well on everyone, and adds 0.5 SDs to their g. How many more people with IQ ≥160 do we get?
The rarity of IQ ≥160, or +4 SDs, is roughly
This is quite a big impact. (I think scaling a method up this much will be difficult. Also, currently no method gives 0.5 SDs on average realistically, though polygenic embryo selection is close, and can do so in some cases.)
However, it's a small impact compared to what you can achieve with a strong HIA method. Suppose instead that, similarly, you have an HIA method that 1% of people use (rather than 10%). Now, this method shifts the distribution up by 3 SDs (rather than 0.5 SDs).
The rarity of IQ ≥115, or +1 SD, is roughly
(Here I'm anchoring impact as a multiplier. I think this is reasonable because we have intuitions for "how much stuff there is in the world overall", e.g. how much intellectual progress gets made given the current distribution. But I'm unsure and interested in arguments on either side.)
So, there is a tradeoff between scaling vs. strength. What does this scaling look like? I may write this up in more detail later. For now I'll just say that it seems that, very very coarsely speaking, a weak HIA method requires about 2 or more additional orders of magnitude of scaling (i.e. 100x more people using it) compared to a strong HIA method, to get the same results in terms of increasing the high tail. See these widgets demonstrating this.
Thus, scaling a weak method is a medium priority, meaning it's very good but not as high a priority as developing strong HIA. However, if scaling is far easier than developing the technology for strong HIA, it could be a top priority.
Conclusion
Marginal strategically-guided effort towards human intelligence amplification should probably mostly go towards methods for which there are good reasons to think they can feasibly be developed far enough to give increases in general intelligence that are well over two standard deviations.
Ritchie, Stuart J., and Elliot M. Tucker-Drob. “How Much Does Education Improve Intelligence? A Meta-Analysis.” Psychological Science 29, no. 8 (2018): 1358–69. https://doi.org/10.1177/0956797618774253. ↩︎