Recently, 星空浩淼 brought up the subject of publishing papers in
international journals. I would like to say something about
it. However, before I start, I would like to stress that these
comments are derived only from my personal experience in my own
field. It does not specifically refer to any particular paper
either. Although the publication review process is unavoidably
subjective and not complete fair, I will focus here only on the issue
of the quality of papers. This is the only thing that an author can really
control.

By the way, such comments also apply to many non-Chinese papers as
well.

From my own experience, many papers from China fail to get accepted at
important journals, and/or fail to attract significant attention, due
to at least one of the following reasons:

1) The subject is not interesting. An subject can be uninteresting for
many reasons. Here are some of them:

1a. The work is a trivial extension to or a straightforward application of a
well-known idea. No new phenomenon is presented. No new insight is
gained from such an application. It is something like ``By the way,
this is to tell you that we also understand this idea and know how to
use it. ''

1b. The work is an attempt to follow some trendy idea. However, it applies
it to almost the most uninteresting case, where the idea is very
unlikely to be prominent, or important. It seems that the application
is usually picked because it is simple, or because it is what the author
knows how to implement.

1c. It attempts to reformulate some very old, well understood idea,
where there is no big confusion and contradiction in the conventional
way of understanding it. The new formulation does not solve new
problems which cannot be solved by the old understanding. Sometimes,
it also shows a lack of understanding of the conventional wisdom.

1d. It is some far fetched idea with very little possibility of being
useful. The author does not know how it will be useful either.

1e. No thinking, at least from what is written in the paper, goes into
why the study is interesting. What is new? The introduction reads like
``We did this since so and so published a paper on ... We want to do
something about it as well''.

2) The physics is wrong, or at least vague and unclear. This problem
could also have several possible representations.

2a. The physics is just wrong. It involves serious
misunderstanding of some basic concepts.

2b. The author misunderstands what other people have already done. As
a result, claims of novelty or superiority are falsely made in the
paper.

2c. The discussion of the subject is naive and very incomplete. It shows
signs of lack of reading and studying the existing literature.

3) The quality of the research is poor.

3a. There is no in-depth study of problems which the paper is set out
to address. The research contains plugging in numbers into a couple
of formulas and produce a couple of preliminary plots. That's it. No detailed
consideration is carried out. It is OK to have
a so so paper, as long as it could get published. It is similar to a
first quick survey by an inexperienced graduate student.

3b. The work does not even try to address the most obvious
questions. It does not discuss the most standard issues related to a
subject.

3c. No effort goes into searching for the best possible solution.

4) The presentation of the paper is poor.

4a. The English is bad. We all suffer from this problem. However, some of
the papers are written in amazingly bad English.

4b. There is no discussion of physics, only formulas and
numbers. There is no discussion of why it is new, why it is important,
why it is not trivial. When presenting some surprising result, there
is no discussion of how it can be understood. It reads like ``Hey, we
programed these formulas into the computer. Here is what comes out of
it. ''

4c. There is no discussion of the implication of the results. There is no
attempt to present a first rated, well-argued paper.


Not all of these aspects are independent of each other. In fact, they
are usually closely connected.

I sincerely hope that the quality of the paper (and research) will
become the number one focus of every Chinese physicist. It only takes
some of us to write crappy papers to tarnish the reputation of paper from
China. Write good papers. Think about what is important. Think about
what is new. Think about how we can write the paper better than
anybody else.

Blindly following gets us nowhere. Cheap and lazy work earn us only
disgrace. Blind pride makes us stupid.

We can be on top of the world. However, we have to try much harder.

总的是好文，但我也有不同的看法
1c 重构一方面使得自己对这个问题理解得更清楚。另一方面也可能使别人更加深对这个问题的理解。惯常的智慧并不都是值得效仿的。就拿通常量子场论讨论时空对称性蕴含守恒律来说，我本人很坦诚地说，我看不懂那帮人在说什么。很多别人对我说，他们懂了。但我很清楚他们没有真正的搞懂，充其量也就是似乎懂了，但他们喜欢冠以美名，物理的洞察与直觉。我后来花了很大的功夫弄得让我自己满意了。当然这只是很小的学习的一个心得。我以为学物理是自己和上帝对话。自己觉得过关才算过关。惯常的智慧只是参考而已。但另一方面，大家都知道经典力学的重构，拉式，哈式。量子力学的重构，费曼路径积分。还有现行研究中对同一个结果的不同的推导都是有价值的。有些东西，当时可能没有觉得有价值，但若干年以后，可能发现它价值打得很。当然我这个是从一个理论物理学家的角度说一个问题的。如果一个实验物理学家或者唯象物理学家，这些美感也好，形式也好，也许不是很注意。注意的可能是你对我当下的这个问题能否给点提示，没有的话，你就滚蛋。

此外，写好文章，一是起源于自己的格调与品位以及对自身的要求，另一方面也有来自科研环境与氛围的影响。而这后者如何改变，这是影响中国科研水准的最大问题。因此我倒希望大家就此发表建设性的方案或者看法。

谢谢sage兄的好文章，这对想出好文章的人有帮助，我复制粘贴地收藏了:-)

我比较不服的一个情况是，别人同一时期还不如自己的文章不断地发表了，而自己的文章却被编辑剥夺送审的权力。

美国有个人H. G. Winful，跟PR系列杂志的编辑是哥们，很有权势（这是德国和意大利科学家们说的)，他是计算机专业的，没有学过量子力学，更不懂量子场论，却在某个量子理论才能解释的研究领域兴风作浪，在PR系列杂志上很有“权威”，跟他意见相左的文章很难发表，而他本人的文章，某些水平低得难以置信、违背基本物理常识，却被编辑强行同意发表。可怕的是，这个人在世界很多最权威杂志上都有论文发表（包括Nature，PRL，Reports of Physics等等，怀疑支持他的审稿人是PR系列的编辑）。尽管如此，他的东西在圈内几乎没有一个人接受，引用的时候多是带有负面引用，带上problematic一词。

就拿通常量子场论讨论时空对称性蕴含守恒律来说，我本人很坦诚地说，我看不懂那帮人在说什么。很多别人对我说，他们懂了。但我很清楚他们没有真正的搞懂，
-------------------------------------------
这个...HPC兄可能有些极端吧。真的有这么难以理解的吗？

量子场论我当年没来得及学得更深入，主要原因是我当时找不到进一步的教材（不象现在书店里面能买到）。例如，超对称理论我是空白的。虽然我数学从小到大都很不错，但重整化理论中的数学推导令我厌烦，没有耐心去追踪每个推算细节，这使得我在这方面缺乏演算训练，好在我好像一般都用不着。因此对量子场论我只具备一些基本基础，一些现代场论（例如拓扑场论什么的），我很惭愧，完全是个外行。

呵呵 我这个人知识面不宽，但是对自己深究的东西有着天生的自信，甚至达自负。后来Weinberg的书要好一些，我能感觉到老温比前人进步了。但是还没有达到我想像的痛快淋漓。这大约起源于老温不懂几何的缘故。

我以前接受的专业训练是：A的思想+B的方法+C的模型+D的分析+.... 开山祖师在一次内部会议上，无意中说出了师门秘诀，听闻几位前辈，发挥到极致，教授，杰青，博导，如抟嚷之物。可惜本人资质愚鲁，始终不能领悟和融会贯通，靠着师兄的指点，勉强达到毕业的最低条件，算是最不成才的一位。
工作以来，几位同事也是灌水高手，一到年底，科研奖励特多，仔细琢磨他们的工作程序，关键之处是特专业，就做特定方向的，把程序钻研的很透，换换模型，改改参数，据某甲自夸，单凭文章，十个教授也能评上。
不过专业课老师的几句话我至今不忘：“你的文章好，但我的比你更好。”“什么是国际领先，人家跟着你屁股后面坐，你就是国际一流。”

HPC说的对

大家都知道经典力学的重构，拉式，哈式。量子力学的重构，费曼路径积分。这些全是非常精彩有意思的. 甚至一个著名的问题,重新做一下也是很有意思的,比如yau他们证明了正质量猜想,过了一年,witten用旋量重新证明了正质量猜想.
witten虽然做了重复的工作,但大家由这个事情觉得,witten是个人物.

再比如,牛顿发现棱镜能够色散光线,这是一个历史事件.后来傅里叶发现,这个世界就是色散的.现在凌意做量子引力,也搞色散.这就是从同一事件中不断找到新的灵感.

北落师门非常的幽默啊.老感觉你姓名的第一个字母是q----当然我这是猜想了.

sage,我写了一篇短论文，是否可以帮忙审阅？如果你乐意，请告知我你的email。我的邮箱是taizhouer@gmail.com 。占用你的时间，当然没有报酬，就算是你捐赠给希望工程。我涂鸦也是好玩。

如果你不愿意，请在帖里告知我。

楼上，sage兄看到的话应该会直接给你回复，但是不会在这个帖子里回复。