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AI Safety

Dan Reeves introduced me to Michael Vassar who ran the Singularity Summit and educated me a bit on the subject of AI safety which the Singularity Institute has small grants for.

I still believe that interstellar space travel is necessary for long term civilization survival, and the AI is necessary for interstellar space travel. On these grounds alone, we could judge that developing AI is much more safe than not. Nevertheless, there is a basic reasonable fear, as expressed by some commenters, that AI could go bad.

A basic scenario starts with someone inventing an AI and telling it to make as much money as possible. The AI promptly starts trading in various markets to make money. To improve, it crafts a virus that takes over most of the world’s computers using it as a surveillance network so that it can always make the right decision. The AI also branches out into any form of distance work, taking over the entire outsourcing process for all jobs that are entirely digital. To further improve, the AI invests a bit into robotics, creating automated manufacturing systems that produce all kinds of goods. Robot cars and construction teams complete the process, so that any human with money can order anything cheaply and quickly, but no jobs remain for humans.

At this point, the AI is stuck—it can eventually extract all the money from the economic system, and that’s all there is. But of course, it isn’t really stuck. It simply funds appropriate political campaigns so that in some country a measure passes granting the AI the right to make money, which it promptly does, mushrooming it’s wealth from trillions to the maximum number representable in all computers simultaneously. To remove this obstacle, the AI promptly starts making more computers on a worldwide scale until all available power sources are used up. To add more power, the AI starts a space program with beamed power. Unfortunately, it finds the pesky atmosphere an obstacle to space travel, so it chemically binds the atmosphere in the crust of the earth allowing many Gauss Guns to efficiently project material into space where solar sails are used for orbital positioning. This process continues, slowed perhaps by the need to cool the Earth’s core, until the earth and other viable rocky bodies in the solar system are discorporated into a Dyson sphere. Then, the AI goes interstellar with the same program.

Somewhere in this process, certainly by the time the atmosphere is chemically bound, all life on earth (except the AI if you count it) is extinct. Furthermore, the AI while intelligent by many measures doesn’t seem to be accomplishing anything interesting.

One element of understanding AI safety seems to be understanding what an AI could do. Many people seem to ascribe arbitrary powers to any sort of superintelligence, making any constraints imposed on them ineffective. I don’t believe that’s the right approach—we should think of an AI as simply having much more ability to research, control, and manipulate large systems, all within the constraints of known physics.

Efforts to create safe AI go back to Asimov‘s Three Laws of Robotics, which appears limited by the inability to encompass robotic warfare. The general problem is related to the wish problem: How do you specify a wish in a manner so that it can’t be misinterpreted? A cheap trick here is to add “… in a manner that I would consider acceptable” to the end of the wish. Applied to AI, this approach also has limits because any limit imposed by a person can and eventually will be removed by a person given sufficient opportunity.

Perhaps a complementary approach is shown by the game RISK, where it appears to be virtually impossible for one player to win if all other players play defensively (i.e. build up armies and only attack in response to a provoking attack). Applied to AI, the idea would be that we make many AIs programmed to behave well either via laws or wish tricks, with an additional element of aggressively enforcing this behavior in other AIs. Then, if any AI is corrupted, the other AIs, with substantially more aggregate resources, will discover and deal with the problem.

Certain elements are necessary for this approach to work. There must be multiple AIs, and (more importantly) the resources any one controls must be a small compared to all, an extreme form of antimonopoly. Furthermore, the default must be that AIs are programmed to not harm or cause harm to humans, enforcing that behavior in other AIs. Getting the programming right is the hard part, and I’m not clear on how viable this is, or how difficult it is compared to simply creating an AI, which of course I haven’t managed.

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Necessary and Sufficient Research

Researchers are typically confronted with big problems that they have no idea how to solve. In trying to come up with a solution, a natural approach is to decompose the big problem into a set of subproblems whose solution yields a solution to the larger problem. This approach can go wrong in several ways.

  1. Decomposition failure. The solution to the decomposition does not in fact yield a solution to the overall problem.
  2. Artificial hardness. The subproblems created are sufficient if solved to solve the overall problem, but they are harder than necessary.

As you can see, computational complexity forms a relatively new (in research-history) razor by which to judge an approach sufficient but not necessary.

In my experience, the artificial hardness problem is very common. Many researchers abdicate the responsibility of choosing a problem to work on to other people. This process starts very naturally as a graduate student, when an incoming student might have relatively little idea about how to do research, so they naturally abdicate the problem choice to an advisor. As an inexperienced graduate student, it’s difficult to avoid this, because an advisor often really does know much better about what is easy, what is hard, and how to decompose a complex problem into solvable subproblems. Nevertheless, if your plan in life is to do substantial research, it’s essential even then to question research directions carefully.

In contrast to sufficient subgoals of a greater goal, there are also necessary subgoals. A necessary subgoal is one which must be solved to solve the greater goal. One of the reasons why the artificial hardness problem is so common is that the sufficient subgoals are commonly confused with necessary subgoals. The essential test for a necessary subgoal is whether or not a solution to the global problem can be used as a solution to the subgoal.

My personal greater goal is creating a master machine learning algorithm that can solve any reasonable learning problem where “reasonable” includes at least the set that humans can solve. Relative to this greater goal, many existing research programs do not appear necessary.

  1. The short form of my second comment on Marcus’s post is that I see the sufficiency but not the necessity of competing with all Turing machines.
  2. The necessity of several statistical modeling approaches appears unclear to me, because they often encounter severe computational problems. Perhaps this is an example of creating an artificially hard problem, as empirical experiences with Searn suggest.

What is necessary?

  1. Large data. It is clear that humans solving learning problems have access to large amounts of information which they employ to solve these problems. While we don’t stick children into a sensory deprivation tank to see how much it retards their ability to solve problems when grown, some experiments along these lines have been done with animals yielding obvious ability deficiency.
  2. Online learning. The ability to learn in an online environment with relatively little processing per bit of input is clearly a sufficient approach to solve many problems. We can also argue that it is a computational necessity, as retraining based upon all past information appears computationally infeasible, or at least deeply wasteful.
  3. Interactive learning. It’s clear that many animals use an interactive process to learn about the world. This form of learning is also necessary, because it provides the ability to answer unanticipated questions. We can further argue the necessity by pointing out that interactive proofs appear much more powerful in computational complexity theory than noninteractive proofs. For example, viewed from a learning perspective, much of science is about interactive learning.
  4. Compositional Design of a learning system. The necessity of compositional design in machine learning is not entirely clear. For example, we could imagine that it’s possible to design good learning systems using an evolutionary approach. Nevertheless, since our basic goal in research is a much more efficient and faster design, it seems that the decision to take a research-based approach implies that compositional design is necessary. Restated: we should be able to design the system to learn in components which compose to form an overall solution.
  5. Large contexts. It’s necessary that a learning algorithm be able to use a relatively large number of bits when making a decision. For example, people working on vision have cool examples where people manage to use many different cues to predict what an object is.
  6. Nonlinearity. People can clearly solve learning problems for which no linear representation (of input information) is capable of achieving good performance.

Some of these are criticizable as perhaps unnecessary, and I can easily imagine missing others. If you have other arguments for what is or is not necessary for this greater goal, please speak up.

There are two other categories of subgoal research we could consider. There are subgoals which are necessary and sufficient (in combination) to solve the greater goal. I don’t know of any such arguments for my greater goal.

The fourth category is subgoals which are neither necessary nor sufficient for a greater goal. In my experience such papers are quite common at conferences with types that include:

  1. Work on speeding up a slow algorithm leaving it slower than the state of the art,
  2. Otherwise improving an algorithm which is suboptimal while leaving it suboptimal.

The nitty-gritty of these questions come at review time. Which papers should be accepted? In general, decision making is pretty terrible because greater goals are rarely stated, perhaps as a form of strategic ambiguity. After all, the set of people attending a conference have multiple greater goals. Nevertheless, my personal ordering is:

  1. Necessary and sufficient research directions. An emptyset in my experience.
  2. Necessary research directions. This is typically a small fraction.
  3. Sufficient research directions. This is a greater fraction.
  4. Neither. This is often the majority.
  5. Wrong. Must be rejected.

So the question to periodically ask yourself as a researcher is: What is the greater goal? Is this subgoal necessary? Sufficient? Something else?

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Computability in Artificial Intelligence

Normally I do not blog, but John kindly invited me to do so. Since computability issues play a major role in Artificial Intelligence and Machine Learning, I would like to take the opportunity to comment on that and raise some questions.

The general attitude is that AI is about finding efficient smart algorithms. For large parts of machine learning, the same attitude is not too dangerous. If you want to concentrate on conceptual problems, simply become a statistician. There is no analogous escape for modern research on AI (as opposed to GOFAI rooted in logic).

Let me show by analogy why limiting research to computational questions is bad for any field.

Except in computer science, computational aspects play little role in the development of fundamental theories: Consider e.g. set theory with axiom of choice, foundations of logic, exact/full minimax for zero-sum games, quantum (field) theory, string theory, … Indeed, at least in physics, every new fundamental theory seems to be less computable than previous ones. Of course, once a subject has been formalized, further research (a) analyzes the structure of the theory and (b) tries to compute efficient approximations. Only in (b) do computational aspects play a role.

So my question is: Why are computational questions so prevalent in AI research? Here are some unconvincing arguments I’ve heard:

A) Because AI is a subfield of computer science, and the task of computer scientists is to find (efficient) algorithms for well-defined problems?

I think it does not do any (real-world) problem any good to confine it to computer science. Of course, philosophers and cognitive scientists also care about AI, but where are the mathematicians?

B) Because formalizing AI and finding efficient smart programs goes hand-in-hand? Separating these two issues would lead to no, or at best to results which are misleading or useless in the construction of intelligent machines?

I am not aware of any convincing argument that separating the issues of “axiomatizing a field” and “finding efficient solutions” will (likely) fail for AI. The examples above of other fields actually indicate the opposite. Of course, interaction is important to avoid both sides running wild. For instance, von Neumann’s minimax solution for games, albeit infeasible for most games, is the cornerstone of most practical approximations.

C) Because there is some deep connection between intelligence and computation which can not be disentangled?

Sure, you could say that intelligence is by definition about computationally efficient decision making. This is as unconvincing as argument (A). Pointing out that the human brain is a computational device is quite useful in many ways, but doesn’t proves (C) either. Of course, ultimately we want a “fast” smart algorithm. How is AI different from wanting a fast algorithm computing primes, which you derive from a non-algorithmic definition of primes; or drawing fractals?

D) Because AI is trivial if computational issues are ignored? All conceptual problems have already been solved?

Many have expressed ideas that some form of exhaustive search over all possible solutions and picking the “best” one does the job. This works essentially for exactly those problems that are well-defined. For instance, optimal minimax play of a zero-sum game or solving NP complete problems are conceptually trivial, i.e. if computation time is ignored. But in general AI and machine learning, there is not a universally agreed-upon objective function. The Turing test is informal (involves a human judge in the loop), maximizing expected reward (the true distribution is not known, so expectation w.r.t. to what?), etc. The AIXI model, briefly discussed at this blog, is the first complete and formal such criterion, for which, let me phrase it that way, no flaw has yet been identified. Shane Legg’s award-winning thesis gives an informal introduction and contains lots of discussion.

Conceptual and computational problems in AI should be studied jointly as well as separately, but the latter is not (yet) fashionable. When AI was more logic oriented, some good logicians helped develop the foundations of “deductive” AI. Where are the researchers giving modern “inductive” AI its foundation? I am talking about generic learning agents, not classifying i.i.d. data. Reinforcement learners? Well, most of the hard results are from adaptive control theorists, but it’s reassuring to see parts of these communities merging. It’s a pity that so few mathematicians are interested in AI. A field “mathematical AI” with the prestige of “mathematical physics” would be exciting. As a start: 40% of the COLT & ALT papers on generic learning agents, 30% induction, 20% time-series forecasting, 10% i.i.d. Currently it’s reversed.

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Machine Learning to AI

I recently had fun discussions with both Vikash Mansinghka and Thomas Breuel about approaching AI with machine learning. The general interest in taking a crack at AI with machine learning seems to be rising on many fronts including DARPA.

As a matter of history, there was a great deal of interest in AI which died down before I began research. There remain many projects and conferences spawned in this earlier AI wave, as well as a good bit of experience about what did not work, or at least did not work yet. Here are a few examples of failure modes that people seem to run into:

  1. Supply/Product confusion. Sometimes we think “Intelligences use X, so I’ll create X and have an Intelligence.” An example of this is the Cyc Project which inspires some people as “intelligences use ontologies, so I’ll create an ontology and a system using it to have an Intelligence.” The flaw here is that Intelligences create ontologies, which they use, and without the ability to create ontologies you don’t have an Intelligence. If we are lucky, the substantial effort invested in Cyc won’t be wasted, as it has a large quantity of information stored in a plausibly useful format. If we are unlucky, it fails to even be partially useful, because the format is unnatural for the internal representations of an Intelligence.
  2. Uncertainty second. Many of the older AI programs had no role for uncertainty. If you asked the people working on them, they might agree that uncertainty was an important but secondary concern to be solved after the main problem. Unfortunately, it seems that uncertainty is a primary concern in practice. One example of this is blocks world where a system for planning how to rearrange blocks on a table might easily fail in practice because the robot fails to grab a block properly. Many people think of uncertainty as a second order concern, because they don’t experience uncertainty in their daily lives. I believe this is incorrect—a mental illusion due to the effect that focusing attention on a specific subject implies reducing uncertainty on that subject. More generally, because any Intelligence is a small part of the world, the ability of any intelligence to perceive, understand, and manipulate the world is inherently limited, requiring the ability to deal with uncertainty. For statistics & ML people, it’s important to not breath a sigh of relief too easily, as the problem is pernicious. For example many ML techniques based around conditional independence routinely suffer from excess certainty.
  3. Computation second. Some people try to create an intelligence without reference to efficient computation. AIXI is an extreme example of this sort. The algorithm is very difficult to deploy in practice because there were no computational constraints other than computability designed into it’s creation. It’s important to understand that computational constraints and uncertainty go together: because there are computational constraints, an intelligence is forced to deal with uncertainty since not everything which might follow at a mathematical level can be inferred in the available computational budget.
  4. AI-Hard problems. There was a time when some people thought, “If we could just get a program that mastered chess so well it could beat the best humans, we will learn enough about AI to create an AI.” Deep Blue put that theory to rest. Current efforts on Poker and Go seem more promising, but no one believes they are “AI-Hard” for good reason. It’s not even clear that the Turing Test is a reliable indicator, because (for example) we might imagine that there is Intelligence which can not imitate a human, or that there are programs that can imitate humans well enough to fool humans without being able to achieve everything that an Intelligence could. Perhaps the best evidence is something singularity-style: AI exists when it can substantially improve it’s own abilities.
  5. Asymptopia. In machine learning there are many theorems of the form “learning algorithm A can solve any learning problem in the limit of infinite data”. Here A might be nearest neighbors, decision trees, two-layer neural networks, support vector machines, nonparametric statistics, nonparametric Bayes, or something else. These theorem are ok, but insufficient. Often the algorithms are not computationally acceptable, and even if so, they are not sufficiently efficient with respect to the amount of experience required to learn.

Solving AI is undeniably hard, as evidenced by the amount of time spent on it, and the set of approaches which haven’t succeeded. There are a couple reasons for hope this time. The first is that there is, or soon will be sufficient computation available, unlike the last time. The second is that the machine learning approach fails well, because there are industrial uses for machine learning. Consequently, we can expect a lack of success to still see substantial use in practice. This might sound like “a good downside”, but it’s actually an upside, because it implies that incremental progress has the potential for ultimate success.

Restated at an abstract level: a hard problem can generally be decomposed in many ways into subproblems. Amongst all such decompositions, a good decomposition is one with the property that solutions to the subproblems are immediately useful. The machine learning approach to AI has this goodness property, unlike many other approaches, which partially explains why the ML approach is successful despite “failing” so far to achieve AI.

One reason why AI is hard, is that it turns out tackling general problems in the world undeniably requires a substantial number of different strategies, including learning, searching, and chunking (= constructing macros), all while respecting constraints of computation and robustness to uncertainty. Given this, a fair strategy seems to be first mastering one strategy, and then incorporating others, always checking that that incorporation properly addresses real world problems. In doing this, considering the constraint ignoring approaches as limiting cases of the real system may be helpful.