Stanford-CV华人教授李飞飞写给她学生的一封信
2016-06-08 01:19阅读：
李飞飞是斯坦福大学计算机视觉领域的牛人。
De-mystifying Good Research and Good Papers
By Fei-Fei Li, 2009.03.01
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 that I'd
share these thoughts with you. I probably have said all these at
various points during our group and individual meetings. But as I
continue my AC reviews these days (that's 70 papers and 200 reviews
-- between me and my AC partner), these following points just keep
coming up. Not enough people conduct first class research. And not
enough people write good papers.
- Every research project and every paper should be conducted and
written with one singular purpose: *to genuinely advance the field
of computer vision*. So when you conceptualize and carry out your
work, you need to be constantly aski
ng yourself this question in the most critical way you could –
“Would my work define or reshape xxx (problem, field, technique) in
the future?” This means publishing papers is NOT about 'this has
not been published or written before, let me do it', nor is it
about “let me find an arcane little problem that can get me an easy
poster”. It's about 'if I do this, I could offer a better solution
to this important problem,' or “if I do this, I could add a
genuinely new and important piece of knowledge to the field.” You
should always conduct research with the goal that it could be
directly used by many people (or industry). In other words, your
research topic should have many ‘customers’, and your solution
would be the one they want to use.
- 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 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. So
why is this paper rejected? Because it doesn't teach us anything,
and no one will likely be using it 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 a good
reflection of real-world image data. It uses a BoW representation
without object level understanding. All reviewers (from very
different angles) asked the same question 'what do we learn from
your method?' And the only sensible answer I could come up with is
that Caltech101 is no longer a good dataset.
- Einstein used to say: everything should be made as simple as
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 science research, is about problems, not equations.
No one appreciates a complicated graphical model with super fancy
inference techniques that essentially achieves the same result as a
simple SVM -- unless it offers deeper understanding of your data
that no other simpler methods could offer. A method in which you
have to manually tune many parameters is not considered principled
or coherent.
- This might sound corny, but it is true. You're PhD
students in one of the best universities in the world. This means
you embody the highest level of intellectualism of humanity today.
This means you are NOT a technician and 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 is finished, but many for many years to come.
- Set a high goal for yourself – the truth is, you can
achieve 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 2009 that people will remember in computer
vision? If not, why not? The truth is only 10 /-epsilon gets
remembered every year. Most of the papers are just meaningless
publication games. A long string of mediocre papers on your resume
can 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 can get you a faculty job in a top
university. This is the truth that most graduate students don't
know, or don't have a chance to know.
- Review process is highly random. But there is one golden rule
that withstands the test of time and randomness -- badly written
papers get bad reviews. Period. It doesn't matter if the idea is
good, result is good, citations are good. Not at all. Writing is
critical -- and this is ironic because engineers are the worst
trained writers among all disciplines in a university. You need to
discipline yourself: leave time for writing, think deeply about
writing, and write it over and over again till it's as polished as
you can think of.
- Last but not the least, please remember this rule:
important problem (inspiring idea) solid and novel theory
convincing and analytical experiments good writing = seminal
research excellent paper. If any of these ingredients is weak, your
paper, hence reviewer scores, would suffer.
