Month: April 2005

It’s reviewing season right now, so I thought I would list (at a high level) the sorts of problems which I see in papers. Hopefully, this will help us all write better papers.

The following flaws are fatal to any paper:

1. Incorrect theorem or lemma statements A typo might be “ok”, if it can be understood. Any theorem or lemma which indicates an incorrect understanding of reality must be rejected. Not doing so would severely harm the integrity of the conference. A paper rejected for this reason must be fixed.
2. Lack of Understanding If a paper is understood by none of the (typically 3) reviewers then it must be rejected for the same reason. This is more controversial than it sounds because there are some people who maximize paper complexity in the hope of impressing the reviewer. The tactic sometimes succeeds with some reviewers (but not with me).

   As a reviewer, I sometimes get lost for stupid reasons. This is why an anonymized communication channel with the author can be very helpful.

3. Bad idea Rarely, a paper comes along with an obviously bad idea. These also must be rejected for the integrity of science

The following flaws have a strong negative impact on my opinion of the paper.

1. Kneecapping the Giants. “Kneecapping the giants” papers take a previously published idea, cripple it, and then come up with an improvement on the crippled version. This often looks great experimentally, but is unconvincing because it does not improve on the state of the art.
2. Only Toys. The paper emphasizes experimental evidence on datasets specially created to show the good performance of their algorithm. Unfortunately, because learning is worst-case-impossible, I have little trust that performing well on a toy dataset implies good performance on real-world datasets.

My actual standard for reviewing is quite low, and I’m happy to approve of incremental improvements. Unfortunately, even that standard is such that I suggest rejection on most reviewed papers.

In the quest to understand what good reviewing is, perhaps it’s worthwhile to think about what good research is. One way to think about good research is in terms of a producer/consumer model.

In the producer/consumer model of research, for any element of research there are producers (authors and coauthors of papers, for example) and consumers (people who use the papers to make new papers or code solving problems). An produced bit of research is judged as “good” if it is used by many consumers. There are two basic questions which immediately arise:

1. Is this a good model of research?
2. Are there alternatives?

The producer/consumer model has some difficulties which can be (partially) addressed.

1. Disconnect. A group of people doing research on some subject may become disconnected from the rest of the world. Each person uses the research of other people in the group so it appears good research is being done, but the group has no impact on the rest of the world. One way to detect this is by looking at the consumers² (the consumers of the consumers) and higher order powers. If the set doesn’t expand much with higher order powers, then there is a disconnect.
2. Latency. It is extraordinarily difficult to determine in advance whether a piece of research will have many consumers. A particular piece of work may be useful only after a very long period of time. This difficulty is particularly severe for theoretical research.
3. Self-fulfillment To some extent, interesting research by this definition is simply research presented to the largest possible audience. The odds that someone will build on the research are simply larger when it is presented to a larger audience. Some portion of this effect is “ok”—certainly attempting to educate other people is a good idea. But in judging the value of a piece of research, discounting by the vigor with which it is presented may be healthy for the system. (In effect, this as a bias against spamming.)

If we accept the difficulties of the producer consumer model, then good reviewing becomes a problem of predicting what research will have a large impact in terms of the numbers of consumers (and consumers^2, etc…) Citations can act (to some extent) as a proxy for consumption implying that it may be possible to (retroactively) score a reviewer’s judgement. There are many difficulties here. For example a citation of the form “[joe blow 93] is wrong and here’s why” isn’t an example of the sort of use we want to encourage. Another important effect is that a reviewer who rejects a paper biases the number of citations a paper later recieves. Another is that a rejected paper that has been resubmitted to another place may change so that it is simply a better paper. It isn’t obvious what a good method is for taking all of these effects into account.

Clearly, there are problems with this model for judging research (and at the second order, judgements of reviews of research). However, I am not aware of any other abstract model for “good research” which is even this good. If you know one, please comment.