Stanford Prof. Li Feifei写给她学生的一封信

Please remember this: 

1000+ computer vision papers get published every year! 

Only 5-10 are worth reading and remembering! 

Since many of you are writing your papers now, I thought thatI'd share these thoughts with you. I probably have said all these at variouspoints during our group and individual meetings. But as I continue my ACreviews these days (that's 70 papers and 200+ reviews
-- between me and my ACpartner), these following points just keep coming up. Not enough people conductfirst class research. And not enough people write good papers. 

- Every research project and every paper should be conductedand written with one singular purpose: *to genuinely advance the field ofcomputer vision*. So when you conceptualize and carry out your work, you needto be constantly asking yourself this question
in the most critical way youcould – “Would my work define or reshape xxx (problem, field, technique) in thefuture?” This means publishing papers is NOT about "this has not beenpublished or written before, let me do it", nor is it about “let me findan arcane
little problem that can get me an easy poster”. It's about
"if I do this, I could offer a better solutionto this important problem," or“if I do this, I could add a genuinely new and important piece of knowledge tothe field.” You should always conduct research with the goal that it could bedirectly used by many
people (or industry). In other words, your research topicshould have many ‘customers’, and your solution would be the one they want touse. 

- A good research project is not about the past (i.e.obtaining a higher performance than the previous N papers).
It's about the future (i.e. inspiring N futurepapers 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 farthe highest performance I've seen for Caltech101. So why is this paperrejected? Because it doesn't teach us anything, and
no one will likely be usingit for anything. It uses a known technique (at least for many people already)with super tweaked parameters custom-made for the dataset that is no longer agood reflection of real-world image data. It uses a BoW representation withoutobject
level understanding. All reviewers (from very different angles) askedthe same question "what do we learnfrom your method?" And the onlysensible answer I could come up with is that Caltech101 is no longer a gooddataset.

- Einstein used to say: everything should be made as simpleas possible, but not simpler. Your method/algorithm should be the most simple,coherent and principled one you could think of for solving this problem.Computer vision research, like many other areas
of engineering and scienceresearch, is about problems, not equations. No one appreciates a complicatedgraphical model with super fancy inference techniques that essentially achievesthe same result as a simple SVM -- unless it offers deeper understanding ofyour
data that no other simpler methods could offer. A method in which you haveto manually tune many parameters is not considered principled or coherent. 

- This might sound corny, but it is true. You're PhD studentsin one of the best universities in the world. This means you embody the highestlevel of intellectualism of humanity today. This means you are NOT a technicianand you are NOT a coding monkey. When
you write your paper, you communicate and. That's what a paper is about. This is how you should approach your writing.You need to feel proud of your paper not just for the day or week it isfinished, but many for many years to come. 

- Set a high goal for yourself – the truth is, you canachieve it as long as you put your heart in it! When you think of your paper,ask yourself this question: Is this going to be among the 10 papers of 2009that people will remember in computer vision? If not,
why not? The truth is only10+/-epsilon gets remembered every year. Most of the papers are justmeaningless publication games. A long string of mediocre papers on your resumecan at best get you a Google software engineer job (if at all – 2009.03 update:no, Google
doesn’t hire PhD for this anymore). A couple of seminal papers canget you a faculty job in a top university. This is the truth that most graduatestudents don't know, or don't have a chance to know. 

- Review process is highly random. But there is one goldenrule that withstands the test of time and randomness -- badly written papersget bad reviews. Period. It doesn't matter if the idea is good, result is good,and citations are good. Not at all. Writing
is critical -- and this is ironicbecause engineers are the worst trained writers among all disciplines in auniversity. You need to discipline yourself: leave time for writing, thinkdeeply about writing, and write it over and over again till it's as polished
asyou can think of. 

- Last but not the least, please remember this rule:important problem (inspiring idea) + solid and novel theory + convincing andanalytical experiments +
ab63
good writing = seminal research + excellent paper. Ifany of these ingredients is weak, your paper, hence
reviewer scores, wouldsuffer.