It also seems worthwhile to give some sense of the scope and reviewing criteria for ICML for authors considering submitting papers. At ICML, the (very large) program committee does the reviewing which informs final decisions by area chairs on most papers. Program chairs setup the process, deal with exceptions or disagreements, and provide advice for the reviewing process. Providing advice is tricky (and easily misleading) because a conference is a community, and in the end the aggregate interests of the community determine the conference. Nevertheless, as a program chair this year it seems worthwhile to state the overall philosophy I have and what I plan to encourage (and occasionally discourage).
At the highest level, I believe ICML exists to further research into machine learning, which I generally think of as turning observations into useful predictions. Research is greatly varied in general, but in all cases it involves answering an interesting question for which the answer was not previously known. Interesting questions are generally natural: they can be stated easily and other people plausibly encounter them. Interesting questions are generally also ones for which there are multiple plausible wrong answers. The definition of “interesting” is otherwise hard to pin down, because it is does and must change over time.
ICML is a broad conference which incorporates the interests of many different groups of people with different tastes in the research they prefer. It’s broad enough that most people don’t appreciate all the papers. That’s ok as long as there is some higher level appreciation for which directions of research benefit the community. Some common flavors are:
- ML for X In general, Machine Learning is a core field of study with many applications. Often, it’s a good idea to publish within a conference focused on that area, but particularly when no such conference exists, ICML is a solid choice for a place to publish. One example of this kind of thing is Machine Learning for Sustainability, where the CCC will be giving a few travel grants. Here the core question is typically “How?” Exhibiting new things that you can do with ML provides good reference points for what is possible, provides a sense of what works, and compelling new ideas about what to work on can be valuable to the community.
There are several ways that papers of this sort can bounce. Perhaps X is insufficiently interesting, the results are unconvincing, or the method of solution is considered too straight-forward. I consider the first and second criteria sound, but am inclined toward leniency on the third, since there is often quite a bit of work in figuring out how to frame the problem so that the solution happens to be easy.
- New Algorithms Often, authors find that existing learning algorithms for solving some problem are lacking in some way, so they propose new better algorithms. This is plausibly the most common category of paper at ICML, so there is quite a bit of variety. The most straight-forward version proposes a new algorithm for a well-studied problem. For these papers it’s important to have an empirical comparison to existing baselines.
It’s easy for an empirical comparison to go wrong. Some authors use synthetic datasets which do not seem significant to me, because good results on such datasets may not transfer to real-world problems well as the real world tends to be quite a bit more complex than the synthetic processes which are natural to program. Instead, it’s important to show good results on real datasets. One problem with relying on real datasets is dataset selection—choosing the dataset for which your algorithm seems to perform best. You can avoid this by choosing datasets in some clearly unbiased manner and by evaluating on many standard datasets. Another way to fail is with a poor choice of baseline. This is tricky, because three reviewers might consider three different baselines the most natural one. Asking around a bit when developing the paper might help here, but in the end this can be a tough judgement call: Is the paper convincing enough that people interested in solving the problem should use this algorithm?
Another class of new algorithms papers is new algorithms for new areas of machine learning, blending into the previous category. Here, there typically are relatively few (perhaps just one) dataset available and there may be no (or only implausibly bad) baselines. For papers like this, one way I’ve seen difficulties is when authors are very invested in a particular approach to solving the problem. If you have defined the problem too narrowly, broadening the definition of the problem can help you see appropriate baselines. Another difficulty I’ve observed is reviewers used to the well-studied problems reject an interesting paper because (essentially) they assume that the authors left out a good baseline which does not exist. To prevent the first, authors who ask around might get some valuable early feedback. For the second, it’s a difficulty we are aware of and will consider asking reviewers to judge on the merits of ML for X.
- Algorithmic studies A relatively rare but potentially valuable form of paper is an algorithmic study. Here, the authors do not propose a new algorithm, but instead do a comprehensive empirical comparison of different algorithms. The standards here are quite high—the empirical comparison needs to be first-class to convince people, so the empirical comparison comments under new algorithms apply strongly.
- New Theory Good theory can enlighten us about what is (or might be) possible. It can also help us build robust learning algorithms, where we design learning algorithms so that they provably solve some large class of problems. I am personally most interested in theory that helps us design new learning algorithms, but broadly interested in what is possible. I’m most interested in the question answered, while the means (and language) should only be as complex as necessary so the theory can be understood as widely as possible.
In many areas of CS theory, double blind reviewing is rare, so theory-oriented people may be unfamiliar with it. An important consequence is that complete proofs must be included either in the paper or supplemental material so that proof checking is fully feasible.
Another way that I’ve seen theory papers run into trouble is when it is a post-hoc justification for an algorithm. In essence, authors who choose to analyze an existing algorithm are sometimes forced to make many unnatural assumptions for the theory to be correct. There generally isn’t an easy fix if you arrive at this point.
- n of the above It is common for ICML papers to be multicategory. At the extreme, you might have a new algorithm which solves a new X well, empirically and theoretically. Reviewers can fall into a trap where they are most interested in 1 of the 4 questions answered above, and find 1/4 of the paper devoted to their question relatively weak compared to the paper that devotes all the pages to the same question.
We are aware of this, and will encourage it to be taken into account.
- The exception The set of papers I expect to see at ICML is more diverse than the above—there are often exceptions of one sort or another. For these exceptions, it often becomes a judgment call: Does this paper significantly further research into machine learning? Papers with little potential audience probably don’t while fun/interesting/useful things that we didn’t think of do.
Further comments or questions are welcome.