标题: Writing good papers
作者: sage

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.