Machine Learning (Theory)

This is the 6 month point in the “run a research blog” experiment, so it seems like a good point to take stock and assess.

One fundamental question is: “Is it worth it?” The idea of running a research blog will never become widely popular and useful unless it actually aids research. On the negative side, composing ideas for a post and maintaining a blog takes a significant amount of time. On the positive side, the process might yield better research because there is an opportunity for better, faster feedback implying better, faster thinking.

My answer at the moment is a provisional “yes”. Running the blog has been incidentally helpful in several ways:

1. It is sometimes educational. example
2. More often, the process of composing thoughts well enough to post simply aids thinking. This has resulted in a couple solutions to problems of interest (and perhaps more over time). If you really want to solve a problem, letting the world know is helpful. This isn’t necessarily because the world will help you solve it, but it’s helpful nevertheless.
3. In addition, posts by others have helped frame thinking about “What are important problems people care about?”, and why. In the end, working on the right problem is invaluable.

I wanted to expand on this post and some of the previous problems/research directions about where learning theory might make large strides.

1. Why theory? The essential reason for theory is “intuition extension”. A very good applied learning person can master some particular application domain yielding the best computer algorithms for solving that problem. A very good theory can take the intuitions discovered by this and other applied learning people and extend them to new domains in a relatively automatic fashion. To do this, we take these basic intuitions and try to find a mathematical model that:
   1. Explains the basic intuitions.
   2. Makes new testable predictions about how to learn.
   3. Succeeds in so learning.

   This is “intuition extension”: taking what we have learned somewhere else and applying it in new domains. It is fundamentally useful to everyone because it increases the level of automation in solving problems.

2. Where next for learning theory? I like the analogy with physics. Back before we-the-humans knew much, people would experiment occasionally and learn to design new things by slow evolution. At some point the physics model arose: you try to build mathematical models of what is happening and then make predictions based on the models. This was wildly succesful for physics. For machine learning, it has only been moderately succesful. We have some formalisms which are of some use in addressing novel learning problems, but the overall process of doing machine learning is not very close to “automatic”. The good news is that over the last 20 years a much richer set of positive examples of succesful applied machine learning has developed. Thus, there are many good intuitions from which we can hope to generalize. In the physics analogy, the year is (perhaps) 1900. Here are a few specific issues:
   1. What is the “right” mathematical model of learning? (in analogy, What is the “right” mathematical model of physical phenomena?”) The models we currently use have their compelling points but typically fail to capture all of the relevant details. This is a very hard question to address, but it should be actively considered and any progress may be very helpful. Examples of this include:
      1. What is the “right” model of active learning? We know almost nothing except there is great potential.
      2. What is the “right” model of Reinforcement learning? Again, we know very little in comparison to what we want to know—a fully automatic general RL solver.

      The notion of “right” here is partially theoretical (can we get derive efficient algorithms?) and partially empirical (do they actually work?).

   2. How do we refine the empirical observations and intuitions of applied learning?
      1. How should we think about “prior”? The Bayesian answer seems unconvincing. At a minimum, information used to create a Bayesian prior often does not come in the form of a Bayesian prior, and so some translation system must be developed.
      2. How can we develop big learning systems that solve big problems? Some form of structure seems necessary, but the right form is still unclear. What theory governs the design of such systems?
   3. How do we take existing theoretical insights and translate them into practical algorithms?
      1. The method of linear projection into spaces has been studied theoretically. Is it useful empirically?
      2. The online learning setting seems theoretically compelling and, at least sometimes, empirically validated. What concerns remain to be addressed to make this a useful technology?

We should keep in mind that there is a real chance the limits of machine learning are lower bounded by human learning. Getting from here to there of course will require a bit of work, some of which might be greatly aided by mathematical consideration.

Some of the “sister conference” presentations at AAAI have been great. Roughly speaking, the conference organizers asked other conference organizers to come give a summary of their conference. Many different AI-related conferences accepted. The presenters typically discuss some of the background and goals of the conference then mention the results from a few papers they liked. This is great because it provides a mechanism to get a digested overview of the work of several thousand researchers—something which is simply available nowhere else.

Based on these presentations, it looks like there is a significant component of (and opportunity for) applied machine learning in AIIDE, IUI, and ACL.

There was also some discussion of having a super-colocation event similar to FCRC, but centered on AI & Learning. This seems like a fine idea. The field is fractured across so many different conferences that the mixing of a supercolocation seems likely helpful for research.