Lance Fortnow has published in CACM his viewpoint on the role of conferences in CS, another round in ever lasting internal debate on this issue. Among his recommendations is:
[…] holding conferences less frequently and accepting every reasonable paper for presentation without proceedings
While I am in favor of having large conferences where everyone meets and everyone talks as is common in other disciplines, I would like to see these as an additional format to the top CS conferences rather than a replacement. Of course, adding non-competitive non-proceedings conferences, without destroying the current competitive ones will not “solve the problem”, stated by the CRA tenure policy memo from 99, that “In those dimensions that count most, conferences are superior”.
From my point of view the unique role of top conferences in CS is that of influencing the agenda of the field. Science is a human endeavor, and as such is a social one. The raison d’etre of the whole academic system is to bring scientists together, having them influence each other. In fact, this is the only way for a field to advance: “standing on the shoulders of giants” or at least on the shoulders of each other. Now, the truth is that the most difficult insight at every single point in time is the understanding of what is important and how to look at things. A field manages to progress best if many researchers reach similar views on these questions, and then work, for a while, in the implied directions, boosting each other’s research. Of course, in many cases after a while it may become apparent that this research direction was “wrong” (i.e. not interesting, not solvable, or not bearing fruit), but this is the common risk in any research. When a whole community works in some direction together, they will tend not only to progress on it faster, but also to branch away into more profitable directions faster. If done right, they will also be able to abandon a wrong direction faster, and more often concentrate efforts in more promising directions.
All in all, I think that the CS conference system (at least in areas that I am familiar with) has been doing very well in concentrating the community effort, and more importantly in abandoning “old fields” and quickly moving into more promising ones. The “trends” we see evoked by the conference system have managed to develop whole areas extremely quickly: modern cryptography, quantum computation, online algorithms, streaming algorithms, and algorithmic game theory are examples of rapid creation of new fields. They have also manged to change directions quickly: the re-invention of CCC (formerly called Structures), the de-emphasis of new research in automata theory, the shift of focus away from the PRAM model in parallel computation, and the rise and fall of theoretical VLSI are such examples.
Now, I am sure that the reader will disagree with the “wisdom of the community” in at least some of the examples I listed above as well as in many other cases. Indeed it is important that there is ample room for other voices, both within each conference and in competing conferences. I do not think that one can seriously claim that the CS conference system is “shutting up” other voices. Certainly non-trendy areas get less attention and space than trendy ones, but they are allowed to compete for the mind-share and heart-share of the community, and may then become trendy. This competition is key. It may be artificially triggered by the limited size of the conference, but it really reflects a competition for the limited attention that humans have.
Now, one may evaluate differently the success of the CS conference system in setting the scientific agenda, and may certainly not like the idea of having a community agenda at all. But just consider the alternatives! One of the saddest and most common things in science is a brilliant graduate student that is working in the defunct area of his or her adviser. In most case, the area chosen for your PhD will determine what you work on for the rest of your career. What a loss! The CS conference system has given graduate students a better chance to find a research area with a promising future (better — not perfect). Many an adviser suggested: “read all abstracts of papers in the last STOC and find 2 or 3 papers that you want to read completely”. This is so much better than “read my own last 2 or 3 papers”. An enormous amount of research effort is wasted in all branches of science by researchers working in stupid and boring directions. This waste can not be totally eliminated of course, but I think that the CS conference system is very effective in reducing it relative to other scientific systems I know.
On the contrary.
The point is that conference competitiveness get too much effort on tiny and trendy “feasible” topics; and thus hinders more basic, deeper in some sense and slower endeavors.
Think of a brilliant graduate student working on trendy issues like “electronic commerce”, instead of concentrating on the more fundamental questions of TCS.
Indeed, what a lost!
(1) I don’t see why you think that competitition encourages “tiny feasible” topics rather than more important results. PCs must be pretty dumb to choose these “tiny feasible” results over “basic deeper” ones.
(2) A topic becomes “trendy” precisely because enough researchers think it is “fundamental” (or otherwise important). You may disagree of course…
typo: Should be “loss!”
Al Yankovich. A few points:
1- Theorists don’t work on “electronic commerce” per se. It is the unfortunate, legacy name of the main AGT conference, which may be contributing to your confusion.
2- This is the wrong blog on which to talk smack about “Electronic Commerce”.
3- Research in the AGT community, including some stuff you might call ec, is often technically deep, with many interesting connections to fundamental issues in algorithms and complexity. This is why it attracts the attention of the very best algorithmists and complexity theorists in the world (the author of this blog is one example). We could all spend our lives working on P vs NP, or we could do something more satisfyingly fruitful by finding a different lens through which to view computation. Who knows, some day some lens may give back by yielding insights into classical open questions in CS.
“All in all, I think that the CS conference system (at least in areas that I am familiar with) has been doing very well in concentrating the community effort, and more importantly in abandoning “old fields” and quickly moving into more promising ones.”
“Old fields”: What the “new fields” do promise? Is this not just “solve new problems with old methods?” I would like to see an example, where “new field” got rise to a “new method.” I don’t know any. If we cannot even prove that multiplying two number is indeed harder than to add them—do we can expect to say something reasonable in “new fields?”
Is this—“QUICKLY (too “quickly”) moving into more promising ones”—not our biggest problem?
Should we not call this “moving quickly to much EASIER questions?” This could make sense: “real” problems are often much easier to solve. These have not much to do with P vs. NP or the like.
Noam makes a good case that there are _some_ benefits to the conference system. A question left unasked is “are the benefits worth the drawbacks?”. This is not a rhetorical question, and it needs to be addressed by both sides.
I don’t see why you think that competitition encourages “tiny feasible” topics rather than more important results.
It does so in the case where the basic deeper result does not fit neatly in ten pages. The tiny feasible result will rate better than the incomplete deeper result under the current review process.
So people attack tiny units, some of which are of very little relevance, while leaving behind more important problems that might take two-three years before a top-tier result comes out.
Is this—”QUICKLY (too “quickly”) moving into more promising ones”—not our biggest problem?
Now taking a stance on the other side, I don’t think the field moves “too quickly”. If you look back at the historical record, if anything we were a bit slow to abandon areas that were not yet ripe for attack. Yes, this is moving to “EASIER” problems, and no, there is nothing wrong with that.
Andrew Wiles has talked about how for many years he wouldn’t work on FLT per se, since it was out of reach. When the proper machinery was discovered (Frey’s conjecture) he immediately embarked on the project. This is proper allocation of resources, not scientific cowardice.
I disagree that having stoc/focs conferences encourages students with “advisors in defunct areas” to broaden their research horizons. I also think it is very sad to meet such a smart student working on a problem that just does not seem to be interesting. However, if we had conferences in which everyone could present, which would make everyone feel more welcome, these students would be more likely to actually meet someone who might help them determine if it is right to stay with the defunct adviser or to try to go somewhere else and work on another topic. If the advisor is working in a defunct area not represented in stoc/focs, they are very unlikely to say to the student to go read the stoc/focs proceedings.
“Old fields”: What the “new fields” do promise? Is this not just “solve new problems with old methods?” I would like to see an example, where “new field” got rise to a “new method.” I don’t know any. If we cannot even prove that multiplying two number is indeed harder than to add them—do we can expect to say something reasonable in “new fields?”
Indeed. We should all be working on proving lower bounds for multiplication.
Less sarcastically, we have in fact said several reasonable things in new fields. We have sometimes used old methods in new places, but we have also developed several new methods. We have also given back to math when we borrowed tools from it, and some of the new methods have found other surprising applications. Of the list above: “modern cryptography, quantum computation, online algorithms, streaming algorithms, and algorithmic game theory”: one can mention lattice-based crypto, Shor’s algorithm, tree embeddings, compressed sensing, PPAD as just a few examples of new methods. I think you are subconsciously comparing the best of your-favorite-area to the worst of “new field”.
On a related note, I think one thing our community values and does well is to make connections between seeming different questions. This happens so often because we go to the same small conferences and see each others’ talks, techniques, problems. This is another benefit of the current conference system that is often overlooked.
“On a related note, I think one thing our community values and does well is to make connections between seeming different questions.”
Actually, can you give some good examples rather than just patting ourselves on the back? There are also some examples of us NOT seeing the connections between fields. For example, the paper below claimed to solve a longstanding open problem in algorithms, but didn’t know it, so they thought their solution was correct:
“Vickrey Pricing and Shortest Paths: What is an Edge Worth?”
Thus, they may well have made some superficial connections, but that is about it.
MAKE_BLOG(research_area){
IF (research_area = CS){
WHILE(1){
POST(“should we stop publishing in FOCS/STOC?”);
}
}
ELSE {
POST(NULL);
DO(research);
}
}
“Indeed. We should all be working on proving lower bounds for multiplication.”
Why not? With such a huge potential we would be done in a week or so 🙂 But more seriously: there is nothing wrong in moving to or discovering new fields quickly — this have a potential to discover a new point of view to “old” problems. Bad, perhaps, is only leaving these “old” fields much too quickly. Mathematicians counted these “moving phases” in centuries. We count them in years …
Actually, I don’t see that “Noam’s vs. Lance’s” view at the role of conferences is so much different. Noam says that “From my point of view the unique role of top conferences in CS is that of INFLUENCING THE AGENDA of the field.” And this is true! Lance says “By deemphasizing their PUBLICATION ROLE, conferences can once again play their most important role: Bringing the community together.” And this again true! These two opinions do not contradict but rather complement each other: influence the agenda and, at the same time, try to keep the community together. Let conferences just be what they should be by definition: “A meeting for consultation or discussion an exchange of views.” Not a place for “collecting boons” for ones carrier. N.B. I understand pretty well that this is only a doubtful wish …
[…] Fortnow’s column to appear in CACM arguing for a reform of the competitive conference system, Noam Nisan’s “opposing” view and many comments on both blogs. Central to the debate seems to be the concern on one side that CS […]
[…] Knowledge Building Summer Institute Noam Nisan quotes Lance Fortnow as […]
[…] initial availability of low hanging fruit in this uncharted territory this culture seems to have served the field well, despite its many shortcomings. At this point AGT seems to have become rather faddish (in the […]
[…] So, what’s my bottom line: I like the notion of a “non-archival” competitive conference that does not expect exclusivity from submitted papers. I certainly see no reason to “respect” such conference publications less than “archival” ones — respect should just be a function of quality. Maybe having high-quality highly-competitive “non-archival” conferences can get the best of both worlds in the CS journal-conference debate? (See also my view.) […]
[…] young graduate student among the hundreds of non-important ones out there. The main reason why I prefer conferences to journals in CS is that the former seem to be doing a much better job (although still far from perfect) of this […]
[…] course, this shift is part of larger trends that were discussed on this blog, as well as in many other places. Whether we want to call them journals, conferences, or […]