Month: July 2005

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.

The AAAI conference is running a student blog which looks like a fun experiment.

One thing common to much research is that the researcher must be the first person ever to have some thought. How do you think of something that has never been thought of? There seems to be no methodical manner of doing this, but there are some tricks.

1. The easiest method is to just have some connection come to you. There is a trick here however: you should write it down and fill out the idea immediately because it can just as easily go away.
2. A harder method is to set aside a block of time and simply think about an idea. Distraction elimination is essential here because thinking about the unthought is hard work which your mind will avoid.
3. Another common method is in conversation. Sometimes the process of verbalizing implies new ideas come up and sometimes whoever you are talking to replies just the right way. This method is dangerous though—you must speak to someone who helps you think rather than someone who occupies your thoughts.
4. Try to rephrase the problem so the answer is simple. This is one aspect of giving up. Failing fast is better than failing slow.

There are also general ‘context development’ techniques which are not specifically helpful for your problem, but which are generally helpful for related problems.

1. Understand the multiple motivations for working on some topic, when they exist.
2. Question the “rightness” of every related thing. This is fundamental to finding good judgement in what you work on.
3. Let a little bit of chaos into your life. Once in awhile, attend a random conference, talk to people who you would not otherwise talk to, etc…

Suppose we had an infinitely powerful mathematician sitting in a room and proving theorems about learning. Could he solve machine learning?

The answer is “no”. This answer is both obvious and sometimes underappreciated.

There are several ways to conclude that some bias is necessary in order to succesfully learn. For example, suppose we are trying to solve classification. At prediction time, we observe some features X and want to make a prediction of either 0 or 1. Bias is what makes us prefer one answer over the other based on past experience. In order to learn we must:

1. Have a bias. Always predicting 0 is as likely as 1 is useless.
2. Have the “right” bias. Predicting 1 when the answer is 0 is also not helpful.

The implication of “have a bias” is that we can not design effective learning algorithms with “a uniform prior over all possibilities”. The implication of “have the ‘right’ bias” is that our mathematician fails since “right” is defined with respect to the solutions to problems encountered in the real world. The same effect occurs in various sciences such as physics—a mathematician can not solve physics because the “right” answer is defined by the world.

A similar question is “Can an entirely empirical approach solve machine learning?”. The answer to this is “yes”, as long as we accept the evolution of humans and that a “solution” to machine learning is human-level learning ability.

A related question is then “Is mathematics useful in solving machine learning?” I believe the answer is “yes”. Although mathematics can not tell us what the “right” bias is, it can:

1. Give us computational shortcuts relevant to machine learning.
2. Abstract empirical observations of what an empirically good bias is allowing transference to new domains.

There is a reasonable hope that solving mathematics related to learning implies we can reach a good machine learning system in time shorter than the evolution of a human.

All of these observations imply that the process of solving machine learning must be partially empirical. (What works on real problems?) Anyone hoping to do so must either engage in real-world experiments or listen carefully to people who engage in real-world experiments. A reasonable model here is physics which has benefited from a combined mathematical and empirical study.

The health of COLT (Conference on Learning Theory or Computational Learning Theory depending on who you ask) has been questioned over the last few years. Low points for the conference occurred when EuroCOLT merged with COLT in 2001, and the attendance at the 2002 Sydney COLT fell to a new low. This occurred in the general context of machine learning conferences rising in both number and size over the last decade.

Any discussion of why COLT has had difficulties is inherently controversial as is any story about well-intentioned people making the wrong decisions. Nevertheless, this may be worth discussing in the hope of avoiding problems in the future and general understanding. In any such discussion there is a strong tendency to identify with a conference/community in a patriotic manner that is detrimental to thinking. Keep in mind that conferences exist to further research.

My understanding (I wasn’t around) is that COLT started as a subcommunity of the computer science theory community. This implies several things:

1. There was a basic tension facing authors: Do you submit to COLT or to FOCS or STOC which are the “big” theory conferences?
2. The research programs in COLT were motivated by theoretical concerns (rather than, say, practical experience). This includes motivations like understanding the combinatorics of some models of learning and the relationship with crypto.

This worked well in the beginning when new research programs were being defined and new learning models were under investigation. What went wrong from there is less clear.

1. Perhaps the community shifted focus from thinking about new learning models to simply trying to find solutions in older models, and this went stale.
2. Perhaps some critical motivations were left out. Many of the learning models under investigation at COLT strike empirically motivated people as implausibly useful.
3. Perhaps the conference/community was not inviting enough to new forms of learning theory. Many pieces of learning theory have not appeared at COLT over the last 20 years.

These concerns have been addressed since the low point of COLT, but the long term health is still questionable: ICML has been accepting learning theory with plausible empirical motivations and a mathematical learning theory conference has appeared so there are several choices of venue available to authors.

The good news is that this year’s COLT appeared healthy. The topics covered by the program were diverse and often interesting. Several of the papers seem quite relevant to the practice of machine learning. Perhaps an even better measure is that there were many younger people in attendance.