李飞飞是斯坦福大学计算机视觉领域的牛人。
By Fei-Fei Li, 2009.03.01
Please remember this:
1000+
Only 5-10 are worth reading andremembering!
Since many of you are writing your papers now, I thought that I'dshare these thoughts with you. I probably have said all these atvarious points during our group and individual meetings. But as Icontinue my AC reviews these days (that's 70 papers and 200+reviews -- between me and my AC partner), these following pointsjust keep coming up. Not enough people conduct first classresearch. And not enough people write goodpapers.
- Every research project and every paper should be conducted andwritten with one singular purpose: *to genuinely advance the fieldof computer vision*. So when you conceptualize and carry out yourwork, you need to be constantly asking yourself this question inthe most critical way you could – “Would my work define or reshapexxx (problem, field, technique) in the future?” This meanspublishing papers is NOT about "this has not been published orwritten before, let me do it", nor is it about “let me find anarcane little problem that can get me an easy poster”. It's about"if I do this, I could offer a better solution to this importantproblem," or “if I do this, I could add a genuinely new andimportant piece of knowledge to the field.” You should alwaysconduct research with the goal that it could be directly used bymany people (or industry). In other words, your research topicshould have many ‘customers’, and your solution would be the onethey want to use.
- A good research project is not about the past (i.e. obtaining ahigher performance than the previous N papers). It's about thefuture (i.e. inspiring N future papers to follow and cite you,N->inf).
- A CVPR'09 submission with a Caltech101 performance of 95%received 444 (3 weakly rejects) this year, and will be rejected.This is by far the highest performance I've seen for Caltech101. Sowhy is this paper rejected? Because it doesn't teach us anything,and no one will likely be using it for anything. It uses a knowntechnique (at least for many people already) with super tweakedparameters custom-made for the dataset that is no longer a goodreflection of real-world image data. It uses a BoW representationwithout object level understanding. All reviewers (from verydifferent angles) asked the same question "what do we learn fromyour method?" And the only sensible answer I could come up with isthat Caltech101 is no longer a gooddataset.
- Einstein used to say: everything should be made as simple aspossible, but not simpler. Your method/algorithm should be the mostsimple, coherent and principled one you could think of for solvingthis problem. Computer vision research, like many other areas ofengineering and science research, is about problems, not equations.No one appreciates a complicated graphical model with super fancyinference techniques that essentially achieves the same result as asimple SVM -- unless it offers deeper understanding of your datathat no other simpler methods could offer. A method in which youhave to manually tune many parameters is not considered principledor coherent.
- Review process is highly random. But there is one golden rulethat withstands the test of time and randomness -- badly writtenpapers get bad reviews. Period. It doesn't matter if the idea isgood, result is good, citations are good. Not at all. Writing iscritical -- and this is ironic because engineers are the worsttrained writers among all disciplines in a university. You need todiscipline yourself: leave time for writing, think deeply aboutwriting, and write it over and over again till it's as polished asyou can think of.
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