I am Nate Soares, AMA!

Policy work / international coordination. Figuring out how to build an aligned AI is only part of the problem. You also need to ensure that an aligned AI is built, and that’s a lot harder to do during an international arms race. (A race to the finish would be pretty bad, I think.)

I’d like to see a lot more people figuring out how to ensure global stability & coordination as we enter a time period that may be fairly dangerous.

(1) Things Executive!Nate will do differently from Researcher!Nate? Or things Nate!MIRI will do differently from Luke!MIRI? For the former, I'll be thinking lots more about global coordination & engaging with interested academics etc, and lots less about specific math problems. For the latter, the biggest shift is probably going to be something like "more engagement with the academic mainstream," although it's a bit hard to say: Luke probably would have pushed in that direction too, after growing the research team a bit. (I have a lot of opportunities available to me that weren't available to Luke at this time last year.)

(2) The old SIAI definitely made some obvious mistakes; see e.g. Holden Karnofsky’s 2012 critique. Luke tried to transfer a number of the lessons learned to me, but it remains to be seen whether I actually learned them :-) The concrete list includes things like (a) constantly drive to systematize, automate, and outsource the busywork; (b) always attack the biggest constraint (by contrast, most people seem to have a default mode of "try and do everything that meets a certain importance level"); (c) put less emphasis on explicit models that you've built yourself an more emphasis on advice from others who have succeeded in doing something similar to what you're trying to do.

(3) MIRI played a pretty big role in getting long-term AI alignment issues onto the world stage. There are lots and lots of things I've learned from that particular success. Perhaps the biggest is "don't disregard intellectual capital."

(1) number of FAIs produced ;-)

Other important metrics include:

• number of agent foundations forum posts produced
• number of papers written
• number of papers published in conferences/journals
• number of papers published in high-prestige conferences/journals (a fuzzy metric)
• number of conferences attended
• number of collaborative papers written
• number of research associates
• number of people who have attended a workshop
• number of non-MIRI-employees who have produced a technical result
• amount of progress on core technical problems (a very fuzzy metric, which is why it’s important to also track the more concrete numbers above)
• size of research team

I also of course keep my eye on "number of dollars available."

Short version: FAI. (You said "hope", not "expect" :-p)

Longer version: Hard question, both because (a) I don't know how you want me to trade off between how nice the advance would be and how likely we are to get it, and (b) my expectations for the next five years are very volatile. In the year since Nick Bostrom released Superintelligence, there has been a huge wave of interest in the future of AI (due in no small part to the efforts of FLI and their wonderful Puerto Rico conference!), and my expectations of where I'll be in five years range all the way from "well that was a nice fad while it lasted" to "oh wow there are billions of dollars flowing into the field".

But I'll do my best to answer. The most obvious schelling point I'd like to hit in 5 years is "fully naturalized AIXI," that is, a solid theoretical understanding of how we would "brute force" an FAI if we had ungodly amounts of computing power. (AIXI is an equation that Marcus Hutter uses to define an optimal general intelligence under certain simplifying assumptions that don't hold in the real world: AIXI is sufficiently powerful that you could use it to destroy the world while demonstrating something that would surely look like "intelligence" from the outside, but it's not yet clear how you could use it to build a generally intelligent system that maximizes something in the world -- for example, even if you gave me unlimited computing power, I wouldn't yet know how to write the program that stably and reliably pursues the goal of turning as much of the universe as possible into into diamond.)

Formalizing "fully naturalized AIXI" would require a better understanding of decision theory (How do we want advanced systems to reason about counterfactuals? Preferences alone are not enough to determine what counts as a "good action," that notion also depends on how you evaluate the counterfactual consequences of taking various actions, we lack a theory of idealized counterfactual reasoning.), logical uncertainty (What does it even mean for a reasoner to reason reliably about something larger than the reasoner? Solomonoff induction basically works by having the reasoner be just friggin' bigger than the environment, and I'd be thrilled if we could get a working theoretical model of "good reasoning" in cases where the reasoner is smaller than the environment), and a whole host of other problems (many of them covered in our technical agenda).

5 years is a pretty wildly optimistic timeline for developing fully naturalized AIXI, though, and I'd be thrilled if we could make concrete progress in any one of the topic areas listed in the technical agenda.

should

I don't even know what that word means ;-)

(a) how many major insights remain between us and strong AI? (b) how many of those insights will come from thinking hard, and how many will come from examining the brain? (c) how many more AI winters will there be? (d) how far ahead will the frontrunner be? (e) will there be an arms race?, to name a few.

That’s a good question: we don’t have a practical AGI to poke at, so why do we expect that we can do work today that’s likely to be relevant many years down the line?

I’ll answer in part with an analogy: Say you went back in time and dropped by to visit Kolmogorov back when he was trying to formalize probability theory, and you asked "working without concrete feedback, how are you planning to increase the chance that your probability theory will be relevant to people trying to reason probabilistically in the future?" It seems like the best response is for him to sort of cock his head and say "well, uh, I’m still trying to formalize what I mean by "chance" and "probability" and so on; once we’ve got those things ironed out, then we can chat."

Similarly, we’re still trying to formalize the theory of advanced agents: right now, if you handed me unlimited computing power, I wouldn’t know how to program it to reliably and "intelligently" pursue a known goal, even a very simple goal, such as "produce as much diamond as possible." There are parts of the problem of designing highly reliable advanced agents that we don’t understand even in principle yet. We don’t even know how to brute force the solution yet. We’re still trying to formalize the problems :-)

Also, note that working on theory doesn’t mean you can’t get feedback: we make various mathematical models that attempt to capture part of the problem, we investigate their behavior, we see which parts of the problems they do and don’t capture, and so on. (For example: Stuart Armstrong came up with a formal definition of a utility-indifferent agent; Benja responded by identifying a way Stuart's agent succumbs to blackmail. I think this counts as pretty concrete feedback: it doesn't get that much more concrete than "your idea provably doesn't work"!)

As for relevance, there are definitely paths where this sort of work wouldn’t end up being relevant (jumping straight to whole-brain emulation, jumping straight to nanotech, etc.) but I currently don’t think those scenarios are all that likely. Other cases where it turns out these problems are irrelevant include (a) we needed the theory, but didn’t complete it in time, (b) it turns out you can build a safe AGI even if you don’t understand why it’s working, not even in theory, and (c) someone else got to the theory first. I’m trying to avoid (a), (b) doesn’t seem likely enough to bet the universe on it, and I’d count (c) as a win :-)

(1) I don't want to put words in their mouths. I'm guessing that most of us have fairly broad priors over what may happen, though. The future's hard to predict.

(2) Depends what you mean by "Friendly AI research." Does AI boxing count? Does improving the transparency of ML algorithms count? Once the FLI grants start going through, there will be lots of people doing long-term AI safety research that may well be useful, so if you count that as FAI research, then the answer is "there will be soon." But if by "FAI research" you mean "working towards a theoretical understanding of highly reliable advanced agents," then the answer is "not to my knowledge, no."

Wow, cheers for answering over 30 questions here, Nate! What a heroic effort.

Thanks for your questions everybody. That is a LOT of reading to go through for anyone interested in this problem, and plenty of interesting thoughts to be absorbed.

If EAs want to support MIRI financially or with relevant technical skills, it's good that they now know more about what research they would be helping, and have an idea about the kind of person who will be leading it. Here is a link to how to get involved with MIRI as a researcher or donor: https://intelligence.org/get-involved/

Thanks very much Nate, and on behalf of the EA community, good luck in the new job!

There's a big spectrum, there. Some people think that no matter what the AI does that's fine because it's our progeny (even if it turns as much matter as it can into a giant computer so it can find better YouTube recommendations). Other people think that you can't actually build a superintelligent paperclip maximizer (because maximizing paperclips would be stupid, and we're assuming that it's intelligent). Other people think that yeah, you don't get good behavior by default, but AI is hundreds and hundreds of years off, so we don't need to start worrying now. Other people think that AI alignment is a pressing concern now but that improving our theoretical understanding of what we're trying to do isn't the missing puzzle piece. I interface with each of these different types of people in very different ways.

To actually answer your question, though, the default interface is "publish papers, attend conferences," with a healthy dose of "talk to people in person when they're in town" mixed in :-)

1) Huh, that hasn't been my experience. We have a number of potential donors who ring us up and ask who in AI alignment needs money the most at the moment. (In fact, last year, we directed a number of donors to FHI, who had much more of a funding gap than MIRI did at that time.)

2) If MIRI disappeared and everything else was held constant, then I'd be pretty concerned about the lack of people focused on the object level problems. (All talk more about why I think this is so important in a little bit, I'm pretty sure at least one other person asks that question more directly.) There'd still be a few people working on the object level problems (Stuart Russell, Stuart Armstrong), but I'd want lots more. In fact, that statement is also true in the actual world! We only have three people on the research team right now, remember, with a fourth joining in August.

In other words, if you were to find yourself in a world like this one except without a MIRI, then I would strongly suggest building something like a MIRI :-)

All right, I'll come back for one more question. Thanks, Wei. Tough question. Briefly,

(1) I can't see that many paths to victory. The only ones I can see go through either (a) aligned de-novo AGI (which needs to be at least powerful enough to safely prevent maligned systems from undergoing intelligence explosions) or (b) very large amounts of global coordination (which would be necessary to either take our time & go cautiously, or to leap all the way to WBE without someone creating a neuromorph first). Both paths look pretty hard to walk, but in short, (a) looks slightly more promising to me. (Though I strongly support any attempts to widen path (b)!)

(2) It seems to me that the default path leads almost entirely to UFAI: insofar as MIRI research makes it easier for others to create UFAI, most of that effect isn't replacing wins with losses, it's just making the losses happen sooner. By contrast, this sort of work seems necessary in order to keep path (a) open. I don't see many other options. (In other words, I think it's net positive because it creates some wins and moves some losses sooner, and that seems like a fair trade to me.)

To make that a bit more concrete, consider logical uncertainty: if we attain a good formal understanding of logically uncertain reasoning, that's quite likely to shorten AI timelines. But I think I'd rather have a 10-year time horizon and be dealing with practical systems built upon solid foundations that come from a decade's worth of formally understanding what good logically uncertain reasoning looks like, rather than a 20-year time horizon where we have to deal with systems built using 19 years of hacks and 1 year of patches bolted on at the end.

(In other words, the possibility of improving AI capabilities is the price you have to pay to keep path (a) open.)

A bunch of other factors also play into my considerations (including a heuristic which says "the best way to figure out which problems are the real problems is to start solving the things that appear to be the problems," and another heuristic which says "if you see a big fire, try to put it out, and don't spend too much time worrying about whether putting it out might actually start worse fires elsewhere", and a bunch of others), but those are the big considerations, I think.

Right now we’re talent-constrained, but we’re also fairly well-positioned to solve that problem over the next six months. Jessica Taylor is joining us in august. We have another researcher or two pretty far along in the pipeline, and we’re running four or five more research workshops this summer, and CFAR is running a summer fellows program in July. It’s quite plausible that we’ll hire a handful of new researchers before the end of 2015, in which case our runway would start looking pretty short, and it’s pretty likely that we’ll be funding constrained again by the end of the year.

A modified version of this question: Assuming MIRI's goal is saving the world (and not MIRI), at what funding level would MIRI recommend giving elsewhere, and where would it recommend giving?

1. (a) grow the research team, (b) engage more with mainstream academia. I'd also like to spend some time experimenting to figure out how to structure the research team so as to make it more effective (we have a lot of flexibility here that mainstream academic institutes don't have). Once we have the first team growing steadily and running smoothly, it's not entirely clear whether the next step will be (c.1) grow it faster or (c.2) spin up a second team inside MIRI taking a different approach to AI alignment. I'll punt that question to future-Nate.
2. So first of all, I'm not convinced that there's less of a role for supporters. If we had just ten people earning-to-give at the (amazing!) level of Ethan Dickinson, Jesse Liptrap, Mike Blume, or Alexei Andreev (note: Alexei recently stopped earning-to-give in order to found a startup), that would bring in as much money per year as the Thiel Foundation. (I think people often vastly overestimate how many people are earning-to-give to MIRI, and underestimate how useful it is: the small donors taken together make a pretty big difference!)

Furthermore, if we successfully execute on (a) above, then we're going to be burning through money quite a bit faster than before. An FLI grant (if we get one) will certainly help, but I expect it's going to be a little while before MIRI can support itself on large donations & grants alone.

As for how I plan to keep supporters engaged & donating, I don't expect it will be that much of a problem: I think that many of our donors are excited to see us publish peer-reviewed papers, attend conferences, and engage in the ongoing global conversation. It's hard for me to say for sure, but it seems quite likely that the last year has been much more exciting for MIRI donors than the previous few years, even though there was no Singularity Summit and most of our output was math.

Now that MIRI is focused on math research (a good move) and not on outreach

Any links on this?

That post mixes a bunch of different assertions together, let me try to distill a few of them out and answer them in turn:

One of Peter's first (implicit) points is that AI alignment is a speculative cause. I tend to disagree.

Imagine it's 1942. The Manhattan project is well under way, Leo Szilard has shown that it's possible to get a neutron chain reaction, and physicists are hard at work figuring out how to make an atom bomb. You suggest that this might be a fine time to start working on nuclear containment, so that, once humans are done bombing the everloving breath out of each other, they can harness nuclear energy for fun and profit. In this scenario, would nuclear containment be a "speculative cause"?

There are currently thousands of person-hours and billions of dollars going towards increasing AI capabilities every year. To call AI alignment a "speculative cause" in an environment such as this one seems fairly silly to me. In what sense is it speculative to work on improving the safety of the tools that other people are currently building as fast as they can? Now, I suppose you could argue that either (a) AI will never work or (b) it will be safe by default, but both those arguments seem pretty flimsy to me.

You might argue that it's a bit weird for people to claim that the most effective place to put charitable dollars is towards some field of scientific study. Aren't charitable dollars supposed to go to starving children? Isn't the NSF supposed to handle scientific funding? And I'd like to agree, but society has kinda been dropping the ball on this one.

If we had strong reason to believe that humans could build strangelets, and society were pouring billions of dollars and thousands of human-years into making strangelets, and almost no money or effort was going towards strangelet containment, and it looked like humanity was likely to create a strangelet sometime in the next hundred years, then yeah, I'd say that "strangelet safety" would be an extremely worthy cause.

How worthy? Hard to say. I agree with Peter that it's hard to figure out how to trade off "safety of potentially-very-highly-impactful technology that is currently under furious development" against "children are dying of malaria", but the only way I know how to trade those things off is to do my best to run the numbers, and my back-of-the-envelope calculations currently say that AI alignment is further behind than the globe is poor.

Now that the EA movement is starting to look more seriously into high-impact interventions on the frontiers of science & mathematics, we're going to need to come up with more sophisticated ways to assess the impacts and tradeoffs. I agree it's hard, but I don't think throwing out everything that doesn't visibly pay off in the extremely short term is the answer.

Alternatively, you could argue that MIRI's approach is unlikely to work. That's one of Peter's explicit arguments: it's very hard to find interventions that reliably affect the future far in advance, especially when there aren't hard objective metrics. I have three disagreements with Peter on this point.

First, I think he picks the wrong reference class: yes, humans have a really hard time generating big social shifts on purpose. But that doesn't necessarily mean humans have a really hard time generating math -- in fact, humans have a surprisingly good track record when it comes to generating math!

Humans actually seem to be pretty good at putting theoretical foundations underneath various fields when they try, and various people have demonstrably succeeded at this task (Church & Turing did this for computing, Shannon did this for information theory, Kolmogorov did a fair bit of this for probability theory, etc.). This suggests to me that humans are much better at producing technical progress in an unexplored field than they are at generating social outcomes in a complex economic environment. (I'd be interested in any attempt to quantitatively evaluate this claim.)

Second, I agree in general that any one individual team isn't all that likely to solve the AI alignment problem on their own. But the correct response to that isn't "stop funding AI alignment teams" -- it's "fund more AI alignment teams"! If you're trying to ensure that nuclear power can be harnessed for the betterment of humankind, and you assign low odds to any particular research group solving the containment problem, then the answer isn't "don't fund any containment groups at all," the answer is "you'd better fund a few different containment groups, then!"

Third, I object to the whole "there's no feedback" claim. Did Kolmogorov have tight feedback when he was developing an early formalization of probability theory? It seems to me like the answer is "yes" -- figuring out what was & wasn't a mathematical model of the properties he was trying to capture served as a very tight feedback loop (mathematical theorems tend to be unambiguous), and indeed, it was sufficiently good feedback that Kolmogorov was successful in putting formal foundations underneath probability theory. We're trying to do something similar with various other confusing aspects of good reasoning (such as logical uncertainty), and you're welcome to raise concerns about whether we need to understand good reasoning under logical uncertainty in order to build an aligned AI, but saying that there's "no feedback loop" seems to just misunderstand the approach.

Great article. My thoughts:

The smallpox vaccine was the first ever vaccine... a highly unproven cause. This site says it saved over half a billion lives. If there was an EA movement when Edward Jenner was alive hundreds of years ago, would it have sensibly advised Jenner to work on a different project because the idea of vaccines was an unproven one?

Note that most of the top lifesavers on ScienceHeros.com did research work, which is an inherently unprovable cause, but managed to save many more lives than a person donating to Givewell's top charities can expect to save. Of course, scientific research can also backfire and cost lives. So one response to this might be to say: "scientific research is an unproven cause that's hard to know the sign of, so we should ignore scientific research in favor of proven causes". But to me this sounds like a head-in-the-sand approach. Scientific research is going to be by far the most significant bit affecting the future of life on Earth. I would rather see the EA movement try to develop tools to get better at predicting science impacts, or at least save money to nudge science when it's more clear what impacts it might have.

(1) That's not quite how I'd characterize the current technical agenda. Rather, I'd say that in order to build an AI aligned with human interests, you need to do three things: (a) understand how to build an AI that's aligned with anything (could you build an AI that reliably builds as much diamond as possible?), (b) understand how to build an AI that assists you in correcting things-you-perceive-as-flaws (this doesn't come for free, but it's pretty important, because humans are bad at getting software right on the first try), and (c) figure out how to build a machine that can safely learn human values & intentions from training data.

We're currently splitting our time between all these problems. It's not that we haven't focused on the value learning problem yet, rather, it's that the value learning problem is only a fraction of the whole problem. We'll keep working on all the parts, and I'm not sure which parts will yield first. I can't give you a timeline on how long various parts will take; scientific progress is very hard to predict.

(2) I wouldn't currently say that "formal logic is the arena in which MIRI's technical work takes place" -- if anything, “math in general” is the arena, and that will probably remain the case until we have a much better understanding of the problems we're trying to solve (and how to solve simplified versions of them), at which point computer programming will become much more essential. Again, it's hard to say how long it will take to get there, because scientific progress is hard to predict.

Formal logic is one of many tools useful in mathematics (alongside probability theory, statistics, linear algebra, etc.) that shows up fairly frequently in our work, but I don’t think of our work as "focused on formal logic." I don't think we'll "move away from formal logic" at a particular time; rather, we'll just use whichever mathematical tools look useful for the problems at hand. That will change as the problems change :-)

It seems a bit like the question behind the question might be "I'd like to help, but I don't know formal logic, when will that stop being a barrier". In which case it's worth saying that I'm attending a MIRI decision theory workshop at the moment, and I don't really know formal logic, but it isn't proving too much of a barrier; I can think about the assertion "Suppose PA proves that A implies B" without really understanding exactly what PA is.

We don't have a working definition of "what has intrinsic value." My basic view on these hairy problems ("but what should I value?") is that we really don't want to be coding in the answer by hand. I'm more optimistic about building something that has a few layers of indirection, e.g., something that figures out how to act as intended, rather than trying to transmit your object-level intentions by hand.

In the paper you linked, I think Max is raising about a slightly different issue. He's talking about what we would call the ontology identification problem. Roughly, imagine building an AI system that you want to produce lots of diamond. Maybe it starts out with an atomic model of the universe, and you (looking at its model) give it a utility function that scores one point per second for every carbon atom covalently bound to four other carbon atoms (and then time-discounts or something). Later, the system develops a nuclear model of the universe. You do want it to somehow deduce that carbon atoms in the old model map onto six-proton atoms in the new model, and maybe query the user about how to value carbon isotopes in its diamond lattice. You don't want it to conclude that none of these six-proton nuclei pattern-match to "true carbon", and then turn the universe upside down looking for some hidden cache of "true carbon."

We have a few different papers that mention this problem, albeit shallowly: Ontological Crises in Artificial Agents' Value Systems, The Value Learning Problem, Formalizing Two Problems of Realistic World-Models. There's a lot more work to be done here, and it's definitely on our radar, though also note that work on this problem is at least a little blocked on attaining a better understanding of how to build multi-level maps of the world.

(1) Eventually. Predicting the future is hard. My 90% confidence interval conditioned on no global catastrophes is maybe 5 to 80 years. That is to say, I don't know.

(2) I fairly strongly expect a fast takeoff. (Interesting aside: I was recently at a dinner full of AI scientists, some of them very skeptical about the whole long-term safety problem, who unanimously professed that they expect a fast takeoff -- I'm not sure yet how to square this with the fact that Bostrom's survey showed fast takeoff was a minority position).

It seems hard (but not impossible) to build something that's better than humans at designing AI systems & has access to its own software and new hardware, which does not self improve rapidly. Scenarios where this doesn't occur include (a) scenarios where the top AI systems are strongly hardware limited; (b) scenarios where all operators of all AI systems successfully remove all incentives to self-improve; or (c) the first AI system is strong enough to prevent all intelligence explosions, but is also constructed such that it does not itself self-improve. The first two scenarios seem unlikely from here, the third is more plausible (if the frontrunners explicitly try to achieve it) but still seems like a difficult target to hit.

(3) I think we're pretty likely to eventually get a singleton: in order to get a multi-polar outcome, you need to have a lot of systems that are roughly at the same level of ability for a long time. That seems difficult but not impossible. (For example, this is much more likely to happen if the early AGI designs are open-sourced and early AGI algorithms are incredibly inefficient such that progress is very slow and all the major players progress in lockstep.)

Remember that history is full of cases where a better way of doing things ends up taking over the world -- humans over the other animals, agriculture dominating hunting & gathering, the Brits, industrialization, etc. (Agriculture and arguably industrialization emerged separately in different places, but in both cases the associated memes still conquered the world.) One plausible outcome is that we get a series of almost-singletons that can't quite wipe out other weaker entities and therefore eventually go into decline (which is also a common pattern throughout history), but I expect superintelligent systems to be much better at "finishing the job" and securing very long-term power than, say, the Romans were. Thus, I expect a singleton outcome in the long run.

The run-up to that may look pretty strange, though.

(1) Not great. (2) Not great.

(To be clear, right now, MIRI is not attempting to build an AGI. Rather, we're working towards a better theoretical understanding of the problem.)

1) The things we have no idea how to do aren't the implicit assumptions in the technical agenda, they're the explicit subject headings: decision theory, logical uncertainty, Vingean reflection, corrigibility, etc :-)

We've tried to make it very clear in various papers that we're dealing with very limited toy models that capture only a small part of the problem (see, e.g., basically all of section 6 in the corrigibility paper).

Right now, we basically have a bunch of big gaps in our knowledge, and we're trying to make mathematical models that capture at least part of the actual problem -- simplifying assumptions are the norm, not the exception. All I can easily say that common simplifying assumptions include: you have lots of computing power, there is lots of time between actions, you know the action set, you're trying to maximize a given utility function, etc. Assumptions tend to be listed in the paper where the model is described.

2) The FLI folks aren't doing any research; rather, they're administering a grant program. Most FHI folks are focused more on high-level strategic questions (What might the path to AI look like? What methods might be used to mitigate xrisk? etc.) rather than object-level AI alignment research. And remember that they look at a bunch of other X-risks as well, and that they're also thinking about policy interventions and so on. Thus, the comparison can't easily be made. (Eric Drexler's been doing some thinking about the object-level FAI questions recently, but I'll let his latest tech report fill you in on the details there. Stuart Armstrong is doing AI alignment work in the same vein as ours. Owain Evans might also be doing object-level AI alignment work, but he's new there, and I haven't spoken to him recently enough to know.)

Insofar as FHI folks would say we're making assumptions, I doubt they'd be pointing to assumptions like "UDT knows the policy set" or "assume we have lots of computing power" (which are obviously simplifying assumptions on toy models), but rather assumptions like "doing research on logical uncertainty now will actually improve our odds of having a working theory of logical uncertainty before it's needed."

(3) I think most of the FHI folks & FLI folks would agree that it's important to have someone hacking away at the technical problems, but just to make the arguments more explicit, I think that there are a number of problems that it's hard to even see unless you have your "try to solve FAI" goggles on. Consider: people have been working on some of these problems for decades (logical uncertainty) or even centuries (decision theory) without solving the AI-alignment-relevant parts.

We're still very much trying to work out the initial theory of highly reliable advanced agents. This involves taking various vague philosophical problems ("what even is logical uncertainty?") and turning them into concrete mathematical models (akin to the concrete model of probability theory attained by Kolmogorov & co).

We're still in the preformal stage, and if we can get this theory to the formal stage, I expect we may be able to get a lot more eyes on the problem, because the ever-crawling feelers of academia seem to be much better at exploring formalized problems than they are at formalizing preformal problems.

Then of course there's the heuristic of "it's fine to shout 'model uncertainty!' and hover on the sidelines, but it wasn't the armchair philosophers who did away with the epicycles, it was Kepler, who was up to his elbows in epicycle data." One of the big ways that you identify the things that need working on is by trying to solve the problem yourself. By asking how to actually build an aligned superintelligence, MIRI has generated a whole host of open technical problems, and I predict that that host will be a very valuable asset now that more and more people are turning their gaze towards AI alignment.

We're actually going to be hiring a full-time office manager soon: someone who can just Make Stuff Happen and free up a lot of our day-to-day workload. Keep your eyes peeled, we'll be advertising the opening soon.

Additionally, we're hurting for researchers who can write fast & well, and before too long we'll be looking for a person who can stay up to speed on the technical research but spend most of their time doing outreach and stewarding other researchers who are interested in doing AI alignment research. Both of these jobs would require a bit less technical ability than is required to make new breakthroughs in the field.

Luke talks about the pros and cons of various terms here. Then, long story short, we asked Stuart Russell for some thoughts and settled on "AI alignment" (his suggestion, IIRC).

Hard to get there. Highly likely that we get to neuromorphic AI along the way. (Low-fidelity images or low-speed partial simulations are likely very useful for learning more about intelligence, and I currently expect that the caches of knowledge unlocked on the way to WBE probably get you to AI before the imaging/hardware supports WBE.)

Great question! I suggest checking out either our research guide or our technical agenda. The first is geared towards students who are wondering what to study in order to eventually gain the skills to be an AI alignment researcher, the latter is geared more towards professionals who already have the skills and are wondering what the current open problems are.

In your case, I'd guess maybe (1) get some solid foundations via either set theory or type theory, (2) get solid foundations on AI, perhaps via AI: A Modern Approach, (3) brush up on probability theory, formal logic, and causal graphical models, and then (4) dive into the technical agenda and figure out which open problems pique your interest.

I wouldn't reject it as a possibility. MIRI wants AGI to have good consequences for human freedom, happiness, etc., but any big increase in power raises the risk that the power will be abused. Ideally we'd want the AI to resist being misused, but there's a tradeoff between 'making the AI more resistant to misuse by its users (when the AI is right and the user is wrong)' and 'making the AI more amenable to correction by its users (when the AI is wrong and the user is right).'

I wouldn't say it's inevitable either, though. It doesn't appear to me that past technological growth has tended to increase how totalitarian the average state is.

Than a slow takeoff? Yes :-)

Great question! The short version is, writing more & publishing more (and generally engaging with the academic mainstream more) are very high on my priority list.

Mainstream publications have historically been fairly difficult for us, as until last year, AI alignment research was seen as fairly kooky. (We've had a number of papers rejected from various journals due to the "weird AI motivation.") Going forward, it looks like that will be less of an issue.

That said, writing capability is a huge bottleneck right now. Our researchers are currently trying to (a) run workshops, (b) engage with & evaluate promising potential researchers, (c) attend conferences, (d) produce new research, (e) write it up, and (f) get it published. That's a lot of things for a three-person research team to juggle! Priority number 1 is to grow the research team (because otherwise nothing will ever be unblocked), and we're aiming to hire a few new researchers before the year is through. After that, increasing our writing output is likely the next highest priority.

Expect our writing output this year to be similar to last year's (i.e., a small handful of peer reviewed papers and a larger handful of technical reports that might make it onto the arXiv), and then hopefully we'll have more & higher quality publications starting in 2016 (the publishing pipeline isn't particularly fast).

I mostly agree with Daniel's paper :-)

The most reliable strategy to date is "ask me" :-)

I'll take a stab at this question too.

There are two different schools of thought about what the goal of AI as a field is. One is that the goal is to build a machine that can do everything humans can -- possibly including experiencing emotions and other conscious states. On this view, a "full AI" would plausibly be a person, deserving of moral rights like any other.

The more common view within contemporary AI is that the goal of AI is to build machines that can effectively achieve a variety of practical goals in a variety of environments. Think Nate's Deep Blue example, but generalized: instead of steering arrangements of chess pieces on a board toward some goal state, a "full" AI steers arbitrary arrangements of objects in space toward some goal state. Such an AI might not be conscious or have real preferences; it might have "goals" only in the limited sense that Deep Blue has "goals." This is the kind of AI MIRI has in mind, and the kind we're trying to plan for: a system that can draw inferences from sensor inputs and execute effective plans, but not necessarily one that has more moral weight than Google's search engine algorithms do.

If it turns out that you do need to make AI algorithms conscious in order to make them effective at scientific and engineering tasks, that does make our task a lot harder, because, yes, we'll have to take into account the AI's moral status when we're designing it, and not just the impact its actions have on other beings. For now, though, consciousness and intelligent behavior look like different targets, and there are obvious economic reasons why mainstream AI is likely to prioritize "high-quality decision making" over "emulating human consciousness."

A better analogy to MIRI's goal than "we build Hitler and then put him in chains" is "we build a reasonably well-behaved child and teach the child non-Hitler-ish values." But both of those ways of thinking are still excessively anthropomorphized. A real-world AI, of the "high-quality decision-making" sort, may not resemble a human child any more closely than the earliest airplanes resembled a baby bird.

For more information about this, I can recommend Stuart Russell's talk on the future of AI: https://www.youtube.com/watch?v=GYQrNfSmQ0M

(1) I suspect it's possible to create an artificial system that exhibits what many people would call "intelligent behavior," and which poses an existential threat, but which is not sentient or conscious. (In the same way that Deep Blue wasn't sentient: it seems to me like optimization power may well be separable from sentience/consciousness.) That's no guarantee, of course, and if we do create a sentient artificial mind, then it will have moral weight in its own right, and that will make our job quite a bit more difficult.

(2) The goal is not to build a sentient mind something that wants to destroy humanity but can't. (That's both morally reprehensible and doomed to failure! :-p) Rather, the goal is to successfully transmit the complicated values of humanity into a powerful optimizer.

Have you read Bostrom's The Superintelligent Will? Short version is, it looks possible to build powerful optimizers that pursue goals we might think are valueless (such as an artificial system that, via very clever long-term plans, produces extremely large amounts of diamond, or computes lots and lots of digits of pi). We'd rather not build that sort of system (especially if it's powerful enough to strip the Earth of resources and turn them into diamonds / computing power): most people would rather build something that shares some of our notion of "value," such as respect for truth and beauty and wonder and so on.

It looks like this isn't something you get for free. (In fact, it looks very hard to get: it seems likely that most minds would by default have incentives to manipulate & decieve in order to acquire resources.) We'd rather not build minds that try to turn everything they can into a giant computer for computing digits of pi, so the question is how to design the sort of mind that has things like respect for truth and beauty and wonder?

In hollywood movies, you can just build something that looks cute and fluffy and then it will magically acquire a spark of human-esque curiosity and regard for other sentient life, but in the real world, you've got to figure out how to program in those capabilities yourself (or program something that will reliably acquire them), and that's hard :-)

First, I think that civilization had better be really dang mature before it considers handing over the reins to something like CEV. (Luke has written a bit about civilizational maturity in the past.)

Second, I think that the CEV paper (which is currently 11 years old) is fairly out of date, and I don't necessarily endorse the particulars of it. I do hope, though, that if humanity (or posthumanity) ever builds a singleton, that they build it with a goal of something like taking into account the extrapolated preferences of all sentients and fulfilling some superposition of those in a non-atrocious way. (I don't claim to know how to fill in the gaps there.)

Or at least laying out the inferential steps you see most lacking within EA groups you meet? Or less-wrongians

Looks like a few of Nate's other answers partly address your question: "Right now we're talent-constrained..." and "grow the research team..."

You could call it a kind of moral relativism if you want, though it's not a term I would use. I tend to disagree with many self-proclaimed moral relativists: for example, I think it's quite possible for one to be wrong about what they value, and I am not generally willing to concede that Alice thinks murder is OK just because Alice says Alice thinks murder is OK.

Another place I depart from most moral relativists I've met is by mixing in a healthy dose of "you don't get to just make things up." Analogy: we do get to make up the rules of arithmetic, but once we do, we don't get to decide whether 7+2=9. This despite the fact that a "7" is a human concept rather than a physical object (if you grind up the universe and pass it through the finest sieve, you will find no particle of 7). Similarly, if you grind up the universe you'll find no particle of Justice, and value-laden concepts are human concoctions, but that doesn't necessarily mean they bend to our will.

My stance can roughly be summarized as "there are facts about what you value, but they aren't facts about the stars or the void, they're facts about you." (The devil's in the details, of course.)

Kinda. The current approach is more like "Pretend you're trying to solve a much easier version of the problem, e.g. where you have a ton of computing power and you're trying to maximize diamond instead of hard-to-describe values. What parts of the problem would you still not know how to solve? Try to figure out how to solve those first."

(1) If we manage to (a) generate a theory of advanced agents under many simplifying assumptions, and then (b) generate a theory of bounded rational agents under far fewer simplifying assumptions, and then (c) figure out how to make highly reliable practical generally intelligent systems, all before anyone else gets remotely close to AGI, then we might consider teching up towards designing AI systems ourselves. I currently find this scenario unlikely.

(2) We're currently far enough away from knowing what the actual architectures will look like that I don't think it's useful to try to build AI components intended for use in an actual AGI at this juncture.

(3) I think that making theorem provers easier to use is an important task and a worthy goal. I'm not optimistic about attempts to merge natural language with Martin-Lof type theory. If you're interested in improving theorem-proving tools in ways that might make it easier to design safe reflective systems in the future, I'd point you more towards trying to implement (e.g.) Marcello's Waterfall in a dependently typed language (which may well involve occasionally patching the language, at this stage).