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
• 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.)

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!  

Man, 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

Noting that a nicer name that's just waiting to be had, in this context, is "Future of the Lightcone Institute" :) 

Sent 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 :-)

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.)

Do you have any specific examples of what this new/rebooted organization would be doing?

The LessWrong Review [? · GW] 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.