My research field is a "hot" one. It is in modeling of additive manufacturing process. Majority of the research being carried out is experimental and some research is theoretical/computational. My research is entirely computational. Publications in my research topic don't go to top journals like nature or science but to applied journals like journal of thermal spray and technology, surface and coatings technology, additive manufacturing or computational materials science.

I read computational papers published by other groups from good universities (in the US and other places) and I often find them quite straightforward (that is, not much novelty in their work). In my research work, I always try to implement something extra (be it a different modeling technique, a different analysis method) to develop a distinctive new knowledge rather than a small incremental knowledge. Nevertheless, my work ultimately gets published in these journals only.

In such scenario, how do I know if I am doing a good work? My experimental collaborators are happy with my work and so is my postdoc advisor. But, how do I know that I am not generating noise? My past entirely computational papers have got just 3 unique citations each in 1-1.5 years. But my collaborative work (with experimentalists) has over 15 citations in same amount of time.

  • "Nevertheless, my work ultimately gets published in these journals only." Do you actually submit to other journals? Regularly? If you do, are the reasons for rejection consistent between reviewers? Jan 3, 2021 at 8:53
  • I submitted to other journals (journal of solids and structures, journal of mechanical sciences) just one time. It got desk rejected for not being rigorous enough for these journals. Very few papers from my field make it to these journals.
    – querydr
    Jan 3, 2021 at 9:14

5 Answers 5


I think your question has no answer since "good research" is too broad and ill-defined a term. What do you mean by "good research"? Research that gets cited a lot? Research that gets you your next job? Research to be proud of? Research that moves your field ahead?

The answer to your question will depend on YOUR definition of "good research". And since this is really hard to do, I would suggest to reframe the question to something like: Is my research helping me to accomplish my goals xyz?


I agree with the other answer that "good research" is not in any way objectively well defined, and that ultimately you will have to develop your own standards. If you get published in the best journals where this kind of work is usually published, obviously its standard is good enough for their standards. If you wonder whether you could publish in higher impact more general journals, you can try out to submit there and see what the reviewers/editors make of it. Before I had some top journal publications in my field, I had a number of things rejected there, and the feedback gave me a feel for what is required.

Obviously you can also ask senior colleagues you trust about what they think of the quality of your work, how can it be improved etc., but of course these people don't always have time to read your stuff properly (better they already know some). Ultimately one can never know whether they say all they think, but it could give you an indication.

One final comment about a thing you wrote: "In my research work, I always try to implement something extra (be it a different modeling technique, a different analysis method) to develop a distinctive new knowledge rather than a small incremental knowledge." This of course is good for your learning and experience, however it doesn't necessarily make an applied paper better if the specific application could also be handled with less innovative methods. Doing something nonstandard and new in applied work isn't an aim in itself, it needs to make the application better. Things done only in order to look original in the first place will not benefit an applied paper. If you develop genuinely new models or methodology, or if you are the first to use them in your field, you should consider writing a more general methodological paper about it that colleagues may want to cite because they can take your idea for their own application.


There are many scales on which you can judge whether your work is "good". On many of them, it seems that the answer from an outsider would be yes.

You are getting published. You are getting citations. You have collaborators (so you are worth working with). Etc.

One that is important in many ways, but easy to dismiss is whether you are happy in your work. Whether you think you are learning anything through it. Even people that don't publish but learn something can have a satisfying professional life. Their work is "good" if only in a personal way. The statement that you like to "add something" suggests that you are happy with the work and enjoy it.

You don't mention whether students like to work with you, at any level from undergraduate to doctoral studies. That can be a measure, as it may indicate that students feel your ideas are worth pursuing.

Do you have new ideas? Even ones that don't work out? Science doesn't plod along. It is fresh and "interesting" ideas that drive it forward. Ideas about "what might be true" but isn't yet known.

But the difference in citation count between your personal and collaborative papers is probably not a good measure since they are different sorts of papers. Some sorts of things get more citations than others.

Another important measure is how your career is advancing. Are your colleagues happy with you? Are you on the road to promotion? To higher pay?


You say that your work is strictly computational, and not theoretical/computational, and I submit that such work is too limited by the lack of a theoretical basis to get in the top journals. A career in academia requires frequent publication in high quality journals. You must get into the theoretical aspects of your field, maybe in a collaboration with a theoretician. But don’t let that person do all the theory. You should learn from them to do it yourself.


Are there computational papers in your field that get published in what you consider top journals ? If yes, then read them and see what is it that they do differently/better than you. At least that's how I would approach it.

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