Overcome the "Publication Block": Advice for a 5th Year PhD Student

[MayCaesar]

Hi all,

Hopefully this is the right section of the forum to post in!

I am a 5th year PhD student in physics at a prestigious university in the US. First 2 years I was taking classes and working in particle physics. On my 3rd year I transitioned to astrophysics. So in terms of the dedicated professional research, I am effectively on my 3rd year currently.

My work mostly has been going pretty well: I have had a lot of very interesting projects from which I learned a lot about the field. I read a lot of papers regularly and am currently working on 3 data science projects, that will likely be a part of my thesis. My advisor wants me to graduate in early 2020, which I think might be a little too early, but not undoable.

However, I've been struggling with converting my projects into publications. So far in this field only 2 papers were released with my name on it (and 1 more is on the submission stage), and I haven't had any first author publications yet.

Mainly, I do not know how to judge whether my results in a given project are publishable. My advisor (from my impression) prefers to let his students deal with the publication issues somewhat independently, and he only proof-reads the drafts and does not guide the process prior to it. As such, I always have trouble answering such questions as:
1) Are my results publishable? If not, how should I improve them to make them publishable?
2) What journal should I publish my work on? Should I target high-impact journals, or less prestigious ones?
3) How much detail should I put into my paper? What level of familiarity with the subject should I assume the typical reader, or the referee for that matter, to have?

With answering these questions, I simply do not know where to start. Question 1) is the main block that prevents me from even trying to write the Methods or the Discussion sections. I can compare my results to those in the papers that have already been published, but even then I am always uncertain: if my results are very similar to the ones in those papers, then is my work novel enough to be worth publishing?

TL;DR: How do I start publishing papers, and how do I decide at what project stage the results are worth publishing?

I would appreciate any advice, any personal experience, etc. both from the students' and the professors' points of view. I believe that this "publication block" is the main obstacle in my career development, the main factor holding me back from graduation with excellence and getting a great postdoc position afterwards.

Thanks a lot!

 

[Vanadium 50]

How many papers do you read in a week?

When you ask this specific question to your advisor, is his answer "I prefer to let my students deal with the publication issues somewhat independently"? Really?

 

[MayCaesar]

Typically, I read 2-3 papers a week very thoroughly, and perhaps 20-30 selectively (the abstract, the conclusion, the introduction, the plots and their description in the text, and the parts I am interested in). I also browse the interesting articles that our group's feed supplies (a few articles a day), although those I rarely read past the abstract and brief look through the figures. In my spare time, I often read the summaries of recent results on such websites as astrobytes, and delve into blogs on data science and statistics.

This is not quite the answer my advisor gives, although, to be fair, I have not asked him this exact question directly. From the indirect queries, it seems to me that he always wants to see some product before having a discussion. Simply coming to him and telling him that I want to write a paper on a given project does not quite work, and he wants to see some version of the paper already done. He is excellent at giving the advice on how to pursue various projects themselves, however.

It is also my impression that he values the quality of papers over quantity, so he is not very enthusiastic about his students publishing short papers summarising several specific results. He prefers the papers to be thorough, and every project should be taken pretty far before he becomes interested in publishing the results.
For instance, I have worked on a neural network project for many months, and the results of that project, in my opinion, are very interesting - however, the advisor believes that the results are not good enough, and we have not found a way to improve them until a certain database from another group becomes available and can be used in place of our, outdated database.

That said, in our group there are a few people who have already had one or more 1st-author papers published, albeit all of them have worked in the field longer than me. There is definitely something that I personally am not doing right, and I would like to figure out how I can find and tackle the issue.

 

[Vanadium 50]

2-3 papers a week x 3 years = 400 or so papers. That seems like a lot of templates to draw from, and likely far more useful than advice from the internet. Can you put into words why having this many examples still isn't working for you?

So, let's talk about the neural net project. Here you have asked your advisor. He think it's not ready. You think it is. Why do you think your judgment is better than his in this regard? (For now, let's disregard the meta-question of why you are working for him if his judgment is so bad) What is it that you understand and he does not?

 

[Choppy]

1) Are my results publishable? If not, how should I improve them to make them publishable?
2) What journal should I publish my work on? Should I target high-impact journals, or less prestigious ones?
3) How much detail should I put into my paper? What level of familiarity with the subject should I assume the typical reader, or the referee for that matter, to have?

These sounds like great specific questions to discuss with your supervisor. Rather than beating around the bush, see if you can book a meeting with him and ask these questions directly.

One thing that might help is to do sit down and plan out a roadmap for the projects that you've done and those you're still working on or planning to work on. In Canada this often happens around the time of the supervisory committee meeting - I would assume it's similar in the US. Sometimes I think students can get bogged down in the details of a project and lose sight of the main point of the work, so stepping back to make a 'big picture' assessment of the thesis work on a periodic basis (at least once a year) is a good thing.

If you're still having questions, another option is to try meeting with other members of your supervisory committee. It's not unreasonable to seek feedback on your work from other professors, and this should be encouraged. You can also do this with post-docs.

Something else to think about too (and this goes back to the roadmap idea) is that the model of "do a project and decide when my results are publishable" seems a little backward. Really, you should embark on a project because you have identified a specific question that hasn't been answered yet. Once you have an answer - that's when you publish. Sometimes you don't get the answer you expect. Sometimes you discover something new along the way. And in those cases you need a little experience in your corner to guide you on when to publish. But the basic problem of "when to publish" is "as soon as you have an answer to the question you set out to solve."

As for how much detail to put in: a lot of people struggle with this. Write it with the assumption that your readers are technically astute and familiar with general concepts in your field, but they may not be experts in the particular problem your work addresses. If the main problem you're working on has been around for a while, there should be some review articles you can cite. As an author it's your job to fill in specifics about what's new and give an overview of what may not be familiar to the readers. One trick you can use is to just assume that you're writing it for your supervisory committee.

 

[Vanadium 50]

"do a project and decide when my results are publishable" seems a little backward. Really, you should embark on a project because you have identified a specific question that hasn't been answered yet.

This is great advice.