Conference paper rejected without any fault in algorithm

Question

I am working on a hard problem in computer science. The problem is NP-complete. Untill now, the fastest algorithm for this problem runs in $O(3^n)$ time and I came up with an algorithm with a time complexity of $O(2.82)^n$. Yet the paper, in which I described my approach, was rejected in three A* conferences. I am wondering why.

1. First conference: They asked why I did not compare my algorithm with algorithm X. They appreciated my algorithm and have not found any fault with it.

2. Second conference: Now I compared my algorithm with algorithm X. They asked me why I did not compare it with some parallel algorithm Y. Again they appreciated my algorithm and have not found any fault with it.

3. Third conference: This time I compared my algorithm with algorithm Y. They did not find any fault with my algorithm and said that it still is exponential and that for large input number it will take much time. The paper was rejected. But isn't 2.83^n a clear improvement over O(3^n)?

I'm at a loss. What should I do next to publish my result in a good conference?

Answer 1

Since you are describing an algorithm paper, I assume you are submitting to algorithms conferences, and the "A*" description refers to the CORE ratings of CS conferences originally developed by the Australian Research Council. The only A* conferences in algorithms are FOCS, STOC, and SODA. I've served on the program committees for all three.

These three conferences are extremely competitive, and standards for acceptance are extremely high. It is not enough for your algorithm to be correct. It is not even enough for your algorithm to offer a significant improvement on the state of the art for your specific problem. At STOC and FOCS in particular, papers are judged on their likely impact on theoretical computer science research beyond the scope of the specific result. For algorithms papers, that means either that you're describing a significant advance on a problem of central interest to the field, and/or that you are introducing new techniques that are likely to generalize to many other problems, and/or that the PC finds your result both surprising and technically impressive.

I would not expect these conferences to accept a paper that only describes a faster exponential-time algorithm for an NP-hard problem. We've seen lots of those before; yet another one is not that surprising. Unless you are proposing a strong general technique, or the specific problem you address has resisted significant progress for a long time, I would recommend aiming for a lower-tier algorithms conference: ESA, ISAAC, COCOON, WADS, LATIN, ....

All the advice in the other answers still applies when submitting to those penultimate-tier conferences, of course. It's still not enough for your algorithm to be correct. You still need to clearly explain your precise contribution and its importance to the research community. You still need to give a thorough comparison of your algorithm to the state of the art. You still need to convince the PC that they should trust you and care about your results.

Answer 2

From reading your question, I'm guessing you failed to articulate the significance of your contribution and problem. One aspect that you need to understand is the interest of the community. Take the matrix multiplication problem as an example: when a recent paper (2014) claimed a 'small' improvement in the bound by a few decimal places, it was big news. Why? Does your problem fall in this category? If not, then it will be hard to get into top conferences. Another problem is that your slight improvement may be 'obvious' to the community, and hence, it is not interesting.

In summary, rewrite the significance of your problem and discuss why the 'small' improvement is very significant. Why should the community care? Was the method used innovative? Does it have wide ranging application on other NP-complete problems? If you can't make a case, then it is time to look for lower-tier conferences.

Answer 3

Since I do not know details about the problem you're working on, the reasons come to mind can be various. But based on your question and comments, I think the reviewer tells you that your improvement is not significant.

If they require you to test your algorithm with bigger inputs, that means they are looking for a reason to pick your algorithm over the other one. Sometimes, even your algorithm has slightly less complexity in terms of running time, the first described algorithm might be a standart and neat one.

Another reason might be that the algorithm you're competing with is just a naive algorithm to give solution to the problem. Maybe authors of that paper prove some other result.

Not every correct algorithm is to be published, and not every improvement is significant. For instance, merge sort was developed in 1945 with worst-case time complexity Nlog(N), and shellsort was developed in 1959 with the same worst-case time complexity. But one cannot argue that shellsort is insignificant.

All in all, to answer

Please share your advice what to do next to publish my result in good conference.

Try to write what do you improve and why would it be important for scientists to know about your improvement very clearly. If you're not convinced it is a considerable improvement, then there is a good chance that audience of conference will not either.