Express interest in an "FHI of the West"
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I think FHI was an extremely special place and I was privileged to get to spend time there.
I applaud attempts to continue its legacy. However, I'd feel gut-level more optimistic about plans that feel more grounded in thinking about how circumstances are different now, and then attempting to create the thing that is live and good given that, relative to attempting to copy FHI as closely as possible.
Differences in circumstance
You mention not getting to lean on Bostrom's research taste as one driver of differences, and I think this is correct but may be worth tracing out the implications of even at the stage of early planning. Other things that seem salient and important to me:
- For years, FHI was one of the only places in the world that you could seriously discuss many of these topics
- There are now much bigger communities and other institutions where these topics are at least culturally permissible (and some of them, e.g. AI safety, are the subject of very active work)
- This means that:
- One of FHI's purposes was serving a crucial niche which is now less undersupplied
- FHI benefited from being the obvious Schelling location to go to think about these topics
- Whereas even in Berkeley you want to think a bit about how you sit in the ecosystem relative to Constellation (which I think has some important FHI-like virtues, although makes different tradeoffs and misses on others)
- FHI benefited from the respectability of being part of the University
- In terms of getting outsiders to take it seriously, getting meetings with interesting people, etc.
- I'm not saying this was crucial for its success, and in any case the world looks different now; but I think it had some real impact and is worth bearing in mind
- As you mention -- you have a campus!
- I think it would be strange if this didn't have some impact on the shape of plans that would be optimal for you
Pathways to greatness
If I had to guess about the shape of plans that I think you might engage in that would lead to something deserving of the name "FHI of the West", they're less like "poll LessWrong for interest to discover if there's critical mass" (because I think that whether there's critical mass depends a lot on people's perceptions of what's there already, and because many of the people you might most want probably don't regularly read LessWrong), and more like thinking about pathways to scale gracefully while building momentum and support.
When I think about this, two ideas that seem to me like they'd make the plan more promising (that you could adopt separately or in conjunction) are (1) starting by finding research leads, and/or (2) starting small as-a-proportion-of-time. I'll elaborate on these:
Finding research leads
I think that Bostrom's taste was extremely important for FHI. There are a couple of levels this was true on:
- Cutting through unimportant stuff in seminars
- I think it's very easy for people, in research, to get fixated on things that don't really matter. Sometimes this is just about not asking enough which the really important questions are (or not being good enough at answering that); sometimes it's kind of performative, about people trying to show off how cool their work is
- Nick had low tolerance for this, as well as excellent taste. He wasn't afraid to be a bit disagreeable in trying to get to the heart of things
- This had a number of benefits:
- Helping discussions in seminars to be well-focused
- Teaching people (by example) how to do the cut-through-the-crap move
- Shaping incentives for researchers in the institute, towards tackling the important questions head on
- Gatekeeping access to the space
- Bostrom was good at selecting people who would really contribute in this environment
- This wasn't always the people who were keenest to be there; and saying "no" to people who would add a little bit but not enough (and dilute things) was probably quite important
- In some cases this meant finding outsiders (e.g. professors elsewhere) to visit, and keeping things intellectually vibrant by having discussions with people with a wide range of current interests and expertise, rather than have FHI just become an echo chamber
- Bostrom was good at selecting people who would really contribute in this environment
- Being a beacon
- Nick had a lot of good ideas, which meant that people were interested to come and talk to him, or give seminars, etc.
If you want something to really thrive, at some point you're going to have to wrestle with who is providing these functions. I think that one thing you could do is to start with this piece. Rather than think about "who are all the people who might be part of this? does that sound like critical mass?", start by asking "who are the people who could be providing these core functions?". I'd guess if you brainstorm names you'll end up with like 10-30 that might be viable (if they were interested). Then I'd think about trying to approach them to see if you can persuade one or more to play this role. (For one thing, I think this could easily end up with people saying "yes" who wouldn't express interest on the current post, and that could help you in forming a strong nucleus.)
I say "leads" rather than "lead" because it seems to me decently likely that you're best aiming to have these responsibilities be shared over a small fellowship. (I'm not confident in this.)
Your answer might also be "I, Oliver, will play this role". My gut take would be excited for you to be like one of three people in this role (with strong co-leads, who are maybe complementary in the sense that they're strong at some styles of thinking you don't know exactly how to replicate), and kind of weakly pessimistic about you doing it alone. (It certainly might be that that pessimism is misplaced.)
Starting small as-a-proportion-of-time
Generally, things start a bit small, and then scale up. People can be reluctant to make a large change in life circumstance (like moving job or even city) for something where it's unknown what the thing they're joining even is. By starting small you get to iron out kinks and then move on from there.
Given that you have the campus, I'd seriously consider starting small not as-a-number-of-people but as-a-proportion-of-time. You might not have the convening power to get a bunch of great people to make this their full time job right now (especially if they don't have a good sense who their colleagues will be etc.). But you probably do have the convening power to get a bunch of great people to show up for a week or two, talk through big issues, and spark collaborations.
I think that you could run some events like this. Maybe to start they're just kind of like conferences / workshops, with a certain focus. (I'd still start by trying to find something like "research leads" for the specific events, as I think it would help convening power as well as helping the things to go well.) In some sense that might be enough for carrying forward the spirit of FHI -- it's important that there are spaces for it, not that these spaces are open 365. But if it goes well and they seem productive, it could be expanded. Rather than just "research weeks", offer "visiting fellowships" where people take a (well-paid) 1-3 month sabbatical from their regular job to come and be in person all at the same time. And then if that's going well consider expanding to a permanent research group. (Or not! Perhaps the ephemeral nature of short-term things, and constantly having new people, would prove even more productive.)
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1Generally agree with most things in this comment. To be clear, I have been thinking about doing something in the space for many years, internally referring to it as creating an "FHI of the West", and while I do think the need for this is increased by FHI disappearing, I was never thinking about this as a clone of FHI, but was always expecting very substantial differences (due to differences in culture, skills, and broader circumstances in the world some of which you characterize above)
I wrote this post mostly because with the death of FHI it seemed to me that there might be a spark of energy and collective attention that seems good to capture right now, since I do think what I would want to build here would be able to effectively fill some of the gap left behind.
As well as thinking about the need for the place in terms of providing a space for research, it is probably worth thinking about the need for a place in terms of what it provides the world. What subjects are currently under-represented in the world and need strong representation to guide us to a positive future? That will guide who you want to lead the organisation.
Constellation (which I think has some important FHI-like virtues, although makes different tradeoffs and misses on others)
What is Constellation missing or what should it do? (Especially if you haven't already told the Constellation team this.)
(Caveat: it's been a while since I've visited Constellation, so if things have changed recently I may be out of touch.)
I'm not sure that Constellation should be doing anything differently. I think there's a spectrum of how much your culture is like blue-skies thinking vs highly prioritized on the most important things. I think that FHI was more towards the first end of this spectrum, and Constellation is more towards the latter. I think that there are a lot of good things that come with being further in that direction, but I do think it means you're less likely to produce very novel ideas.
To illustrate via caricatures in a made-up example: say someone turned up in one of the offices and said "OK here's a model I've been developing of how aliens might build AGI". I think the vibe in Constellation would trend towards people are interested to chat about it for fifteen minutes at lunch (questions a mix of the treating-it-as-a-game and the pointed but-how-will-this-help-us), and then say they've got work they've got to get back to. I think the vibe in FHI would have trended more towards people treat it as a serious question (assuming there's something interesting to the model), and it generates an impromptu 3-hour conversation at a whiteboard with four people fleshing out details and variations, which ends with someone volunteering to send round a first draft of a paper. I also think Constellation is further in the direction of being bought into some common assumptions than FHI was; e.g. it would seem to me more culturally legit to start a conversation questioning whether AI risk was real at FHI than Constellation.
I kind of think there's something valuable about the Constellation culture on this one, and I don't want to just replace it with the FHI one. But I think there's something important and valuable about the FHI thing which I'd love to see existing in some more places.
(In the process of writing this comment it occurred to me that Constellation could perhaps decide to have some common spaces which try to be more FHI-like, while trying not to change the rest. Honestly I think this is a little hard without giving that subspace a strong distinct identity. It's possible they should do that; my immediate take now that I've thought to pose the question is that I'm confused about it.)
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2(I work out of Constellation and am closely connected to the org in a bunch of ways)
I think you're right that most people at Constellation aren't going to seriously and carefully engage with the aliens-building-AGI question, but I think describing it as a difference in culture is missing the biggest factor leading to the difference: most of the people who work at Constellation are employed to do something other than the classic FHI activity of "self-directed research on any topic", so obviously aren't as inclined to engage deeply with it.
I think there also is a cultural difference, but my guess is that it's smaller than the effect from difference in typical jobs.
I'll also note that if you want to show up anywhere in the world and get good takes from people on the "how aliens might build AGI" question, Constellation might currently be the best bet (especially if you're interested in decision-relevant questions about this).
1To anyone reading this who wants to work on or discuss FHI-flavored work: Consider applying to Constellation's programs (the deadline for some of them is today!), which include salaried positions for researchers.
I think that you're right that people's jobs are a significant thing driving the difference here (thanks), but I'd guess that the bigger impact of jobs is via jobs --> culture than via jobs --> individual decisions. This impression is based on a sense of "when visiting Constellation, I feel less pull to engage in the open-ended idea exploration vs at FHI", as well as "at FHI, I think people whose main job was something else would still not-infrequently spend some time engaging with the big open questions of the day".
I might be wrong about that ¯\_(ツ)_/¯
Your answer might also be "I, Oliver, will play this role". My gut take would be excited for you to be like one of three people in this role (with strong co-leads, who are maybe complementary in the sense that they're strong at some styles of thinking you don't know exactly how to replicate), and kind of weakly pessimistic about you doing it alone. (It certainly might be that that pessimism is misplaced.)
For what it’s worth, my guess is that your pessimism is misplaced. Oliver certainly isn’t as famous as Bostrom, so I doubt he’d be a similar “beacon.” But I’m not sure a beacon is needed—historically, plenty of successful research institutions (e.g. Bells Labs, IAS, the Royal Society in most eras) weren’t led by their star researchers, and the track record of those that were strikes me as pretty mixed.
Oliver spends most of his time building infrastructure for researchers, and I think he’s become quite good at it. For example, you are reading this comment on (what strikes me as) rather obviously the best-designed forum on the internet; I think the review books LessWrong made are probably the second-best designed books I’ve seen, after those from Stripe Press; and the Lighthaven campus is an exceedingly nice place to work.
Personally, I think Oliver would probably be my literal top choice to head an institution like this.
I completely agree that Oliver is a great fit for leading on research infrastructure (and the default thing I was imagining was that he would run the institute; although it's possible it would be even better if he could arrange to be number two with a strong professional lead, giving him more freedom to focus attention on new initiatives within the institute, that isn't where I'd start). But I was specifically talking about the "research lead" role. By default I'd guess people in this role would report to the head of the institute, but also have a lot of intellectual freedom. (It might not even be a formal role; I think sometimes "star researchers" might do a lot of this work without it being formalized, but it still seems super important for someone to be doing.) I don't feel like Oliver's track record blows me away on any of the three subdimensions I named there, and your examples of successes at research infrastructure don't speak to it. This is compatible with him being stronger than I guess, because he hasn't tried in earnest at the things I'm pointing to. (I'm including some adjustment for this, but perhaps I'm undershooting. On the other hand I'd also expect him to level up at it faster if he's working on it in conjunction with people with strong track records.)
I think it's obvious that you want some beacon function (to make it an attractive option for people with strong outside options). That won't be entirely by having excellent people which will mean that internal research conversations are really good, but it seems to me like that was a significant part of what made FHI work (NB this wasn't just Nick, but people like Toby or Anders or Eric); I think it could be make-or-break for any new endeavour in a way that might be somewhat path-dependent in how it turns out; it seems right and proper to give it attention at this stage.
Huh, I feel confused. I suppose we just have different impressions. Like, I would say that Oliver is exceedingly good at cutting through the bullshit. E.g., I consider his reasoning around shutting down the Lightcone offices to be of this type, in that it felt like a very straightforward document of important considerations, some of which I imagine were socially and/or politically costly to make. One way to say that is that I think Oliver is very high integrity, and I think this helps with bullshit detection: it's easier to see how things don't cut to the core unless you deeply care about the core yourself. In any case, I think this skill carries over to object-level research, e.g., he often seems, to me, to ask cutting-to-the core type questions there, too. I also think he's great at argument: legible reasoning, identifying the important cruxes in conversations, etc., all of which makes it easier to tell the bullshit from the not.
I do not think of Oliver as being afraid to be disagreeable, and ime he gets to the heart of things quite quickly, so much so that I found him quite startling to interact with when we first met. And although I have some disagreements over Oliver's past walled-garden taste, from my perspective it's getting better, and I am increasingly excited about him being at the helm of a project such as this. Not sure what to say about his beacon-ness, but I do think that many people respect Oliver, Lightcone, and rationality culture more generally; I wouldn't be that surprised if there were an initial group of independent researcher types who were down and excited for this project as is.
I don't really disagree with anything you're saying here, and am left with confusion about what your confusion is about (like it seemed like you were offering it as examples of disagreement?).
Aw man, this is so exciting! There’s something really important to me about rationalist virtues having a home in the world. I’m not sure if what I’m imagining is what you’re proposing, exactly, but I think most anything in this vicinity would feel like a huge world upgrade to me.
Apparently I have a lot of thoughts about this. Here are some of them, not sure how applicable they are to this project in particular. I think you can consider this to be my hopes for what such a thing might be like, which I suspect shares some overlap.
It has felt to me for a few years now like something important is dying. I think it stems from the seeming inevitability of what’s before us—the speed of AI progress, our own death, the death of perhaps everything—that looms, shadow-like. And it’s scary to me, and sad, because “inevitability” is a close cousin of “defeat,” and I fear the two inch closer all the time.
It’s a fatalism that creeps in slow, but settles thick. And it lurks, I think, in the emotional tenor of doom that resides beneath nominally probabilistic estimates of our survival. Lurks as well, although much more plainly, within AI labs: AGI is coming whether we want it to or not, pausing is impossible, the invisible hand holds the reins, or as Claude recently explained to me, “the cat is already out of the bag.” And I think this is sometimes intentional—we are supposed to think about labs in terms of the overwhelming incentives, more than we are supposed to think about them as composed of agents with real choice, because that dispossesses them of responsibility, and dispossesses us of the ability to change them.
There is a similar kind of fatalism that often attaches to the idea of the efficient marketplace—that what is desired has already been done, that if one sits back and lets the machine unfold it will arrive at all the correct conclusions itself. There is no room, in that story, for genuinely novel ideas or progress, all forward movement is the result of incremental accretions on existing structures. This sentiment looms in academia as well—that there is nothing fundamental or new left to uncover, that all low hanging fruit has been plucked. Academic aims rarely push for all that could be—progress is instead judged relatively, the slow inching away from what already is.
And I worry this mentality is increasingly entrenching itself within AI safety, too. That we are moving away from the sort of ambitious science that I think we need to achieve the world that glows—the sort that aims at absolute progress—and instead moving closer to an incremental machine. After all, MIRI tried and failed to develop agent foundations so maybe we can say, “case closed?” Maybe “solving alignment” was never the right frame in the first place. Maybe it always was that we needed to do the slow inching away from the known, the work that just so happens not to challenge existing social structures. There seems to me, in other words, to be a consensus closing in: new theoretical insights are unlikely to emerge, let alone to have any real impact on engineering. And unlikelier, still, to happen in time.
I find all of this fatalism terribly confused. Not only because it has, I think, caused people to increasingly depart from the theoretical work which I believe is necessary to reach the world that glows, but because it robs us of our agency. The closer one inches towards inevitability, the further one inches away from the human spirit having any causal effect in the world. What we believe is irrelevant, what is good and right is irrelevant; the grooves have been worn, the structures erected—all that’s left is for the world to follow course. We cannot simply ask people to do what’s right, because they apparently can’t. We cannot succeed at stopping what is wrong, because the incentives are too strong to be opposed. All we can do, it seems, is to meld with the structure itself, making minor adjustments on the margin.
And there’s a feeling I get, sometimes, when I look at all of this, as if a tidal wave were about to engulf me. The machine has a life of its own; the world is moved by forces outside of my control. And it scares me, and I feel small. But then I remember that it’s wrong.
There was a real death, I think, that happened when MIRI leadership gave up on solving alignment, but we haven’t yet held the funeral. I think people carry that—the shadow of the fear, unnamed but tangible: that we might be racing towards our inevitable death, that there might not be much hope, that the grooves have been worn, the structures erected, and all that’s left is to give ourselves away as we watch it all unravel. It’s not a particularly inspiring vision, and in my opinion, not a particularly correct one. The future is built out of our choices; they matter, they are real. Not because it would be nice to believe it, but because it is macroscopically true. If one glances at history, it’s obvious that ideas are powerful, that people are powerful. The incentives do not dictate everything, the status quo is never the status quo for very long. The future is still ours to decide. And it’s our responsibility to do so with integrity.
I have a sense that this spirit has been slipping, with MIRI leadership largely admitting defeat, with CFAR mostly leaving the scene, with AI labs looming increasingly large within the culture and the discourse. I don’t want it to. I want someone to hold the torch of rationality and all its virtues, to stay anchored on what is true and good amidst a landscape of rapidly changing power dynamics, to fight for what’s right with integrity, to hold a positive vision for humanity. I want a space for deep inquiry and intellectual rigor, for aiming at absolute progress, for trying to solve the god damn problem. I think Lightcone has a good shot at doing a fantastic job of bringing something like this to life, and I’m very exited to see what comes of this!
71Man, I can’t believe there are no straightforwardly excited comments so far!
Personally, I think an institution like this is sorely needed, and I’d be thrilled if Lightcone built one. There are remarkably few people in the world who are trying to think carefully about the future, and fewer still who are trying to solve alignment; institutions like this seem like one of the most obvious ways to help them.
Sorry, but I don't think this should be branded as "FHI of the West".
I don't think you personally or Lightcone share that much of an intellectual taste with FHI or Nick Bostrom - Lightcone seems firmly in the intellectual tradition of Berkeley, shaped by orgs like MIRI and CFAR. This tradition was often close to FHI thoughts, but also quite often at tension with it. My hot take is you particularly miss part of the generators of the taste which made FHI different from Berkeley. I sort of dislike the "FHI" brand being used in this way.
edit: To be clear I'm strongly in favour of creating more places for FHI-style thinking, just object to the branding / "let's create new FHI" frame. Owen expressed some of the reasons better and more in depth
Totally agree, it definitely should not be branded this way if it launches.
I am thinking of "FHI of the West" here basically just as the kind of line directors use in Hollywood to get the theme of a movie across. Like "Jaws in Space" being famously the one line summary of the movie "Alien".
It also started internally as a joke based on an old story of the University of Ann Arbor branding itself as "the Harvard of the West", which was perceived to be a somewhat clear exaggeration at the time (and resulted in Kennedy giving a speech where he described Harvard jokingly as "The Michigan of the East" which popularized it). Describing something as "Harvard of the West" in a joking way seems to have popped up across the Internet in a bunch of different contexts. I'll add that context to the OP, though like, it is a quite obscure reference.
If anything like this launches to a broader audience I expect no direct reference to FHI to remain. It just seems like a decent way to get some of the core pointers across.
1Two notes:
- I think the title is a somewhat obscure pun referencing the old saying that Stanford was the "Harvard of the West". If one is not familiar with that saying, I guess some of the nuance is lost in the choice of term. (I personally had never heard that saying before recently, and I'm not even quite sure I'm referencing the right "X of the West" pun)
- habryka did have a call with Nick Bostrom a few weeks back, to discuss his idea for an "FHI of the West", and I'm quite confident he referred to it with that phrase on the call, too. Far as I'm aware Nick didn't particularly react to it with more than a bit humor.
I also think the name is off, but for a different reason. When I hear "the west" with no other context, I assume it means this, which doesn't make sense here, because the UK and FHI are very solidly part of The West. (I have not heard the "Harvard of the west" phrase and I'm guessing it's pretty darn obscure, especially to the international audience of LW.)
I would imagine I would also react to it with smile in the context of an informal call. When used as brand / "fill interest form here" I just think it's not a good name, even if I am sympathetic to proposals to create more places to do big picture thinking about future.
Noting that a nicer name that's just waiting to be had, in this context, is "Future of the Lightcone Institute" :)
2Such an unambitious, narrowly-scoped topic area?? There may be infinitely many parallel universes in which we can acausally improve life … you’re giving up of the value at stake before even starting :)
[Even more off-topic]
I like thinking about "lightcone" as "all that we can 'effect', using 'effect' loosely to mean anything that we care about influencing given our decision theory (so e.g., potentially including acausal things)".
Another way to put this is that the normal notion of lightcone is a limit on what we can causally effect under the known laws of physics, but there is a natural generalization to the whatever-we-decide-matters lightcone which can include acausal stuff.
2Sent the form.
What do you think about combining teaching and research? Similar to the Humboldt idea of the university, but it wouldn't have to be as official or large-scale.
When I was studying math in Moscow long ago, I was attending MSU by day, and in the evenings sometimes went to the "Independent University", which wasn't really a university. Just a volunteer-run and donation-funded place with some known mathematicians teaching free classes on advanced topics for anyone willing to attend. I think they liked having students to talk about their work. Then much later, when we ran the AI Alignment Prize here on LW, I also noticed that the prize by itself wasn't too important; the interactions between newcomers and old-timers were a big part of what drove the thing.
So maybe if you're starting an organization now, it could be worth thinking about this kind of generational mixing, research/teaching/seminars/whatnot. Though there isn't much of a set curriculum on AI alignment now, and teaching AI capability is maybe not the best idea :-)
Then much later, when we ran the AI Alignment Prize here on LW, I also noticed that the prize by itself wasn't too important; the interactions between newcomers and old-timers were a big part of what drove the thing.
Could you provide more detail?
I mean, one of the participants wrote: "getting comments that engage with what I write and offer a different, interesting perspective can almost be more rewarding than money". Others asked us for feedback on their non-winning entries. It feels to me that interaction between more and less experienced folks can be really desirable and useful for both, as long as it's organized to stay within a certain "lane".
To what extent would the organization be factoring in transformative AI timelines? It seems to me like the kinds of questions one would prioritize in a "normal period" look very different than the kinds of questions that one would prioritize if they place non-trivial probability on "AI may kill everyone in <10 years" or "AI may become better than humans on nearly all cognitive tasks in <10 years."
I ask partly because I personally would be more excited of a version of this that wasn't ignoring AGI timelines, but I think a version of this that's not ignoring AGI timelines would probably be quite different from the intellectual spirit/tradition of FHI.
More generally, perhaps it would be good for you to describe some ways in which you expect this to be different than FHI. I think the calling it the FHI of the West, the explicit statement that it would have the intellectual tradition of FHI, and the announcement right when FHI dissolves might make it seem like "I want to copy FHI" as opposed to "OK obviously I don't want to copy it entirely I just want to draw on some of its excellent intellectual/cultural components." If your vision is the latter, I'd find it helpful to see a list of things that you expect to be similar/different.)
To what extent would the organization be factoring in transformative AI timelines? It seems to me like the kinds of questions one would prioritize in a "normal period" look very different than the kinds of questions that one would prioritize if they place non-trivial probability on "AI may kill everyone in <10 years" or "AI may become better than humans on nearly all cognitive tasks in <10 years."
My guess is a lot, because the future of humanity sure depends on the details of how AI goes. But I do think I would want the primary optimization criterion of such an organization to be truth-seeking and to have quite strong norms and guardrails against anything that would trade off communicating truths against making a short-term impact and gaining power.
As an example of one thing I would do very differently from FHI (and a thing that I talked with Bostrom about somewhat recently where we seemed to agree) was that with the world moving faster and more things happening, you really want to focus on faster OODA loops in your truth-seeking institutions.
This suggests that instead of publishing books, or going through month-long academic review processes, you want to move more towards things like blogposts and comments, and maybe in the limit even on things like live panels where you analyze things right as they happen.
I do think there are lots of failure modes around becoming too news-focused (and e.g. on LW we do a lot of things to not become too news-focused), so I think this is a dangerous balance, but its one of the things I think I would do pretty differently, and which depends on transformative AI timelines.
To comment a bit more on the power stuff: I think a thing that I am quite worried about is that as more stuff happens more quickly with AI people will feel a strong temptation to trade in some of the epistemic trust they have built with others, into resources that they can deploy directly under their control, because as more things happen, its harder to feel in control and by just getting more resources directly under your control (as opposed to trying to improve the decisions of others by discovering and communicating important truths) you can regain some of that feeling of control. That is one dynamic I would really like to avoid with any organization like this, where I would like it to continue to have a stance towards the world that is about improving sanity, and not about getting resources for itself and its allies.
1I ask partly because I personally would be more excited of a version of this that wasn't ignoring AGI timelines, but I think a version of this that's not ignoring AGI timelines would probably be quite different from the intellectual spirit/tradition of FHI.
This frame feels a bit off to me. Partly because I don’t think FHI was ignoring timelines, and because I think their work has proved quite useful already—mostly by substantially improving our concepts for reasoning about existential risk.
But also, the portfolio of alignment research with maximal expected value need not necessarily perform well in the most likely particular world. One might imagine, for example—and indeed this is my own bet—that the most valuable actions we can take will only actually save us in the subset of worlds in which we have enough time to develop a proper science of alignment.
The LessWrong Review runs every year to select the posts that have most stood the test of time. This post is not yet eligible for review, but will be at the end of 2025. The top fifty or so posts are featured prominently on the site throughout the year.
Hopefully, the review is better than karma at judging enduring value. If we have accurate prediction markets on the review results, maybe we can have better incentives on LessWrong today. Will this post make the top fifty?
I strongly agree with Owen's suggestions about figuring out a plan grounded in current circumstances, rather than reproducing what was.
Here's some potentially useful directions to explore.
Just to be clear, I'm not claiming that it should adopt all of these. Indeed, an attempt to adopt all of these would likely be incoherent and attempting to pursue too many different directions at the same time.
These are just possibilities, some subset of which is hopefully useful:
- Rationality as more of a focus area: Given that Lightcone runs Less Wrong, an obvious path to explore is whether rationality could be further developed by providing people either a fellowship or a permanent position to work on developing the art:
- Being able to offer such paid positions might allow you to draw contributions from people with rare backgrounds. For example, you might decide it would be useful to better understand anthropology as a way of better understanding other cultures and practices and so you could directly hire an anthropologist to help with that.
- It would also help with projects that would be valuable, but which would be a slog and require specific expertise. For example, it would be great to have someone update the sequences in light of more recent psychological research.
- Greater focus on entrepreneurship:
- You've already indicated your potential interest in taking it this direction by adding it as one of the options on your form.
- This likely makes sense given that Lightcone is located in the Bay Area, the city with the most entrepreneurs and venture capitalists in the world.
- Insofar as a large part of the impact of FHI was the projects it inspired elsewhere, it may make sense to more directly attempt this kind of incubation.
- Response to the rise of AI:
- One of the biggest shifts in the world since FHI was started has been the dramatic improvements in AI
- One response to this would be to focus more on the risks and impacts from AI. However, there are already a number of institutions focusing on this, so this might simply end up being a worse version of them:
- You may also think that you might be able to find a unique angle, for example, given how Eliezer was motivated to create rationality in order to help people understand his arguments on AI safety, it might be valuable for there to be a research program which intertwines those two elements.
- Or you might identify areas, such as AI consciousness, that are still massively neglected
- Another response would be to try to figure out how to leverage AI:
- Would it make sense to train an AI agent on Less Wrong content?
- As an example, how could AI be used to develop wisdom?
- Another response would be to decide that better orgs are positioned to pursue these projects.
- Is there anything in the legacy of MIRI, CFAR of FHI that is particularly ripe for further development?:
- For example, would it make sense for someone to try to publish an explanation of some of the ideas produced by MIRI on decision theory in a mainstream philosophical journal?
- Perhaps some techniques invented by CFAR could be tested with a rigorous academic study?
- Potential new sources of ideas:
- There seems to have been a two-way flow of ideas between LW/EA and FHI.
- While there may still be more ideas within these communities that are deserving of further exploration, it may also make sense to consider whether there any new communities that could provide a novel source of ideas?:
- A few possibilities immediately come to mind: post-rationality, progress studies, sensemaking, meditation, longevity, predictions.
- Less requirement for legibility than FHI:
- While FHI leaned towards the speculative end of academia, there was still a requirement for projects to still be at least somewhat academically legibility. What is enabled by no longer having that kind of requirement?
- Opportunities for alpha from philosophical rigour:
- This was one of the strengths of FHI - bringing philosophical rigour to new areas. It may be worth exploring how this could be preserved/carried forward?
- One of the strengths of academic philosophy - compared to the more casual writing that is popular on Less Wrong - is its focus on rigour and drawing out distinctions. If this institute were able to recruit people with strong philosophical backgrounds, are there any areas that would be particularly ripe for applying this style of thinking?
- Pursuing this direction might be a mistake if you would struggle to recruit the right people. It may turn out that the placement of FHI within Oxford was vital for drawing the philosophical talent of the calibre that they drew.
11I agree in the abstract with the idea of looking for niches, and I think that several of these ideas have something to them. Nevertheless when I read the list of suggestions my overall feeling is that it's going in a slightly wrong direction, or missing the point, or something. I thought I'd have a go at articulating why, although I don't think I've got this to the point where I'd firmly stand behind it:
It seems to me like some of the central FHI virtues were:
- Offering a space to top thinkers where the offer was pretty much "please come here and think about things that seem important in a collaborative truth-seeking environment"
- I think that the freedom of direction, rather than focusing on an agenda or path to impact, was important for:
- attracting talent
- finding good underexplored ideas (b/c of course at the start of the thinking people don't know what's important)
- Caveats:
- This relies on your researchers having some good taste in what's important (so this needs to be part of what you select people on)
- FHI also had some success launching research groups where people were hired to more focused things
- I think this was not the heart of the FHI magic, though, but more like a particular type of entrepreneurship picking up and running with things from the core
- I think that the freedom of direction, rather than focusing on an agenda or path to impact, was important for:
- Willingness to hang around at whiteboards for hours talking and exploring things that seemed interesting
- With an attitude of "OK but can we just model this?" and diving straight into it
- Someone once described FHI as "professional amateurs", which I think is apt
- The approach is a bit like the attitude ascribed to physicists in this xkcd, but applied more to problems-that-nobody-has-good-answers-for than things-with-lots-of-existing-study (and with more willingness to dive into understanding existing fields when they're importantly relevant for the problem at hand)
- Someone once described FHI as "professional amateurs", which I think is apt
- Importantly mostly without directly asking "ok but where is this going? what can we do about it?"
- Prioritization at a local level is somewhat ruthless, but is focused on "how do we better understand important dynamics?" and not "what has external impact in the world?"
- With an attitude of "OK but can we just model this?" and diving straight into it
- Sometimes orienting to "which of our ideas does the world need to know about? what are the best ways to disseminate these?" and writing about those in high-quality ways
- I'd draw some contrast with MIRI here, who I think were also good at getting people to think of interesting things, but less good at finding articulations that translated to broadly-accessible ideas
Reading your list, a bunch of it seems to be about decisions about what to work on or what locally to pursue. My feeling is that those are the types of questions which are largely best left open to future researchers to figure out, and that the appropriate focus right now is more like trying to work out how to create the environment which can lead to some of this stuff.
Overall, the take in the previous paragraph is slightly too strong. I think it is in fact good to think through these things to get a feeling for possible future directions. And I also think that some of the good paths towards building a group like this start out by picking a topic or two to convene people on and get them thinking about. But if places want to pick up the torch, I think it's really important to attend to the ways in which it was special that aren't necessarily well-represented in the current x-risk ecosystem.
Just thought I'd add a second follow-up comment.
You'd have a much better idea of what made FHI successful than I would. At the same time, I would bet that in order to make this new project successful - and be its own thing - it'd likely have to break at least one assumption behind what made old FHI work well.
1Reading your list, a bunch of it seems to be about decisions about what to work on or what locally to pursue.
I think my list appears more this way then I intended because I gave some examples of projects I would be excited by if they happened. I wasn't intending to stake out a strong position as to whether these projects should projects chosen by the institute vs. some examples of projects that it might be reasonable for a researcher to choose within that particular area.
Makes sense! My inference was because the discussion at this stage is a high-level one about ways to set things up, but it does seem good to have space to discuss object-level projects that people might get into.
I knew that this was going to happen in some form or another for a year or two, having heard through the grapevine and private conversations of FHI's university-imposed hiring freeze and fundraising block, and so I have been thinking about how to best fill the hole in the world that FHI left behind.