I think this is similar to Security Mindset, so you might want to think about this post in relation to that.
I don't think so, or if it is, than to a version of "security mindset" by Eliezer Yudkowsky, not a version by Bruce Schneier.
Very roughly speaking, security mindset is about differences between probabilities 99,99% and 1-10^(-16). From a mathematical perspective the difference between 1-10^(-16) and 1 is still more similar to the difference between 1-10^(-4) and 1.
Notable feature anybody who seriously studies security learns quickly is, it is in practice impossible to proof the security of anything useful except OTP. The whole rest of security usually reduces to physics and economy.
Note: I am not saying that we don't need mathematicians. We absolutely should try to get to that level of precision.
At the same time, mathematical way of thinking is in some sense fragile: a proof is ether correct or not. A proof which is "almost correct" is not worth very much.
When Scott says "mathematician mindset can be useful for AI alignment", I take it that your interpretation is "we should try to make sure that when we build AGI, we can prove that our system is safe/robust/secure", whereas I think the intended interpretation is "we should try to make sure that when we build AGI, we have a deep formal understanding of how this kind of system works at all so that we're not flying blind". Similar to how we understand the mathematics of how rockets work in principle, and if we found a way to build a rocket without that understanding, it's very unlikely we'd be able to achieve much confidence in the system's behavior.
I think the end of this excerpt from a 2000 Bruce Schneier piece is assuming something like this, though I don't know that Schneier would agree with Eliezer and Scott fully:
Complexity is the worst enemy of security. [...]
The first reason is the number of security bugs. All software contains bugs. And as the complexity of the software goes up, the number of bugs goes up. And a percentage of these bugs will affect security.
The second reason is the modularity of complex systems. [...I]ncreased modularity means increased security flaws, because security often fails where two modules interact. [...]
The third reason is the increased testing requirements for complex systems. [...]
The fourth reason is that the more complex a system is, the harder it is to understand. There are all sorts of vulnerability points — human-computer interface, system interactions — that become much larger when you can't keep the entire system in your head.
The fifth (and final) reason is the difficulty of analysis. The more complex a system is, the harder it is to do this kind of analysis. Everything is more complicated: the specification, the design, the implementation, the use. And as we've seen again and again, everything is relevant to security analysis.
Cf. this thing I said a few months ago:
"Adding conceptual clarity" is a key motivation, but formal verification isn't a key motivation.
The point of things like logical induction isn't "we can use the logical induction criterion to verify that the system isn't making reasoning errors"; as I understand it, it's more "logical induction helps move us toward a better understanding of what good reasoning is, with a goal of ensuring developers aren't flying blind when they're actually building good reasoners".
Daniel Dewey's summary of the motivation behind HRAD is:
"2) If we fundamentally 'don't know what we're doing' because we don't have a satisfying description of how an AI system should reason and make decisions, then we will probably make lots of mistakes in the design of an advanced AI system.
"3) Even minor mistakes in an advanced AI system's design are likely to cause catastrophic misalignment."
To which Nate replied at the time:
"I think this is a decent summary of why we prioritize HRAD research. I would rephrase 3 as 'There are many intuitively small mistakes one can make early in the design process that cause resultant systems to be extremely difficult to align with operators’ intentions.' I’d compare these mistakes to the 'small' decision in the early 1970s to use null-terminated instead of length-prefixed strings in the C programming language, which continues to be a major source of software vulnerabilities decades later.
"I’d also clarify that I expect any large software product to exhibit plenty of actually-trivial flaws, and that I don’t expect that AGI code needs to be literally bug-free or literally proven-safe in order to be worth running."
The position of the AI community is something like the position researchers would be in if they wanted to build a space rocket, but hadn't developed calculus or orbital mechanics yet. Maybe with enough trial and error (and explosives) you'll eventually be able to get a payload off the planet that way, but if you want things to actually work correctly on the first go, you'll need to do some basic research to cover core gaps in what you know.
To say that calculus or orbital mechanics help you "formally verify" that the system's parts are going to work correctly is missing where the main benefit lies, which is in knowing what you're doing at all, not in being able to machine-verify everything you'd like to.
Scott can correct me if I'm misunderstanding his post (e.g., rounding it off too much to what's already in my head).
I think "what should be done" is generally different question that "what kind of mindsets there are" and I would prefer to disentangle them.
My claims about mindsets roughly are
As I understand it (correct me if I'm wrong), your main claim roughly is "we should have a deep understanding how these systems works at all".
I don't think there is much disagreement on that.
But please note that Scott's post in several places makes explicit distinction between the kind of understanding achieved in mathematics, and in science. The understanding we have how rockets work is pretty much on the physics side of this - e.g. we know we can disregard gravitational waves, radiation pressure, and violations of CP symmetry.
To me, this seems different from mathematics, where it would be somewhat strange to say something like "we basically understand what functions and derivatives are ... you can just disregard cases like the Weierstrass function".
(comment to mods: I would actually enjoy a setting allowing me to not see the karma system at all, the feedback it is giving me is "write things which people would upvote" vs. "write things which are most useful - were I'm unsure, see some flaws,...". )
I agree. When I think about the "mathematician mindset" I think largely about the overwhelming interest in the presence or absence, in some space of interest, of "pathological" entities like the Weierstrass function. The truth or falsehood of "for all / there exists" statements tend to turn on these pathologies or their absence.
How does this relate to optimization? Optimization can make pathological entities more relevant, if
(1) they happen to be optimal solutions, or
(2) an algorithm that ignores them will be, for that reason, insecure / exploitable.
But this is not a general argument about optimization, it's a contingent claim that is only true for some problems of interest, and in a way that depends on the details of those problems.
And one can make a separate argument that, when conditions like 1-2 do not hold, a focus on pathological cases is unhelpful: if a statement "fails in practice but works in theory" (say by holding except on a set of sufficiently small measure as to always be dominated by other contributions to a decision problem, or only for decisions that would be ruled out anyway for some other reason, or over the finite range relevant for some calculation but not in the long or short limit), optimization will exploit its "effective truth" whether or not you have noticed it. And statements about "effective truth" tend to be mathematically pretty uninteresting; try getting an audience of mathematicians to care about a derivation that rocket engineers can afford to ignore gravitational waves, for example.
I think the simple mathematical models here are very helpful in pointing to some intuitions about being confident systems will work even with major optimisation pressure applied, and why optimisation power makes things weird. I would like to see other researchers in alignment review this post, because I don't fully trust my taste on posts like these.
I don't like the intro to the post. I feel like the example Scott gives makes the opposite of the point he wants it to make. Either a number with the given property exists or not. If such a number doesn't exist, creating a superintelligence won't change that fact. Given talk I've heard around the near certainty of AI doom, betting the human race on the nonexistence of a number like this looks pretty attractive by comparison -- and it's plausible there are AI alignment bets we could make that are analogous to this bet.
One of the main explanations of the AI alignment problem I link people to.
What is the opportunity cost of the mathematical mindset? For example, if going through all formal proves and verifying them would require 100 years of research by 100 best minds, the cost is 10.000 genius-years (not speaking about non-zero probability that any proof-system may still have errors, as was shown by Yampolskiy).
Now, from the scientific mindset point of view, it is clear that we just don't have such long time, as other approaches to AI will create some forms of AGI before it.
If these geniuses would search for a quicker fix, they could win in AI race and stop it.
I talk here about how a mathematician mindset can be useful for AI alignment. But first, a puzzle:
Given m, what is the least number n≥2 such that for 2≤k≤m, the base k representation of n consists entirely of 0s and 1s?
If you want to think about it yourself, stop reading.
For m=2, n=2.
For m=3, n=3.
For m=4, n=4.
For m=5, n=82,000.
Indeed, 82,000 is 10100000001010000 in binary, 11011111001 in ternary, 110001100 in base 4, and 10111000 in base 5.
What about when m=6?
So, a mathematician might tell you that this is an open problem. It is not known if there is any n≥2 which consists of 0s and 1s in bases 2 through 6.
A scientist, on the other hand, might just tell you that clearly no such number exists. There are 2k−1 numbers that consist of k 0s and 1s in base 6. Each of these has roughly log5(6)⋅k digits in base 5, and assuming things are roughly evenly distributed, each of these digits is a 0 or a 1 with "probability" 2/5. The "probability" that there is any number of length k that has the property is thus less than 2k⋅(2/5)k=(4/5)k. This means that as you increase k, the "probability" that you find a number with the property drops off exponentially, and this is not even considering bases 3 and 4. Also, we have checked all numbers up to 2000 digits. No number with this property exists.
Who is right?
Well, they are both right. If you want to have fun playing games with proofs, you can consider it an open problem and try to prove it. If you want to get the right answer, just listen to the scientist. If you have to choose between destroying the world with a 1% probability and destroying the world if a number greater than 2 which consists of 0s and 1s in bases 2 through 6 exists, go with the latter.
It is tempting to say that we might be in a situation similar to this. We need to figure out how to make safe AI, and we maybe don't have that much time. Maybe we need to run experiments, and figure out what is true about what we should do and not waste our time with math. Then why are the folks at MIRI doing all this pure math stuff, and why does CHAI talk about "proofs" of desired AI properties? It would seem that if the end of the world is at stake, we need scientists, not mathematicians.
I would agree with the above sentiment if we were averting an astroid, or a plague, or global warming, but I think it fails to apply to AI alignment. This is because optimization amplifies things.
As a simple example of optimization, let Xi for i<1,000,000 be i.i.d. random numbers which are normally distributed with mean 0 and standard deviation 1. If I choose an Xi at random, the probability that Xi is greater than 4 is like 0.006%. However, if I optimize, and choose the greatest Xi, the probability that it is greater that 4 is very close to 100%. This is the kind of thing that optimization does. It searches through a bunch of options, and takes extreme ones. This has the effect of making things that would be very small probabilities much larger.
Optimization also leads to very steep phase shifts, because it can send something on one side of a threshold to one extreme, and send things on the other side of a threshold to another extreme. Let Xi for i<1,000,000 be i.i.d. random numbers that are uniform in the unit interval. If you look at the first 10 numbers and take the one that is furthest away from .499, the distribution over numbers will be bimodal peaks near 0 and 1. If you take the one that is furthest away from .501, you will get a very similar distribution. Now instead consider what happens if you look at all 1,000,000 numbers and take the one that is furthest from .499. You will get a distribution that is almost certainly 1. On the other hand, the one that is furthest from .501 will be almost certainly 0. As you slightly change the optimization target, the result of a weak optimization might not change much, but the result of a strong one can change things drastically.
As a very rough approximation, a scientist is good at telling the difference between probability 0.01% and probability 99.99%, while the mathematician is good at telling the difference between 99.99% and 100%. Similarly, the scientist is good at telling if a≃b, while the mathematician is good at telling if a=b when you already know that a≃b.
If you only want to get an approximately correct answer almost surely, the absence of strong optimization pressure makes the mathematician skills much less useful. However strong optimization pressure amplifies and creates discontinuities, which creates the necessity for a mathematician level of precision even to achieve approximate correctness in practice.
Notes:
1) I am not just saying that adversarial optimization makes small probabilities of failure large. I am saying that in general any optimization at all messes with small probabilities and errors drastically.
2) I am not saying that we don't need scientists. I am saying that we don't just need scientists, and I am saying that scientists should pay some attention to the mathematician mindset. There is a lot to be gained from getting your hands dirty in experiments.
3) I am not saying that we should only be satisfied if we achieve certainty that an AI system will be safe. That's an impossibly high standard. I am saying that we should aim for a deep formal understanding of what is going on, more like the "fully reduced" understanding we have of steam engines or rockets.