I guess this a question about 'career pacing'. I am currently a first-year grad student studying for a PhD in Aerospace Engineering at a research university in the US. Even though I have only been studying this field for about 5 months, I am already starting to get quite a few ideas about interesting potential avenues for research. For example, possible numerical simulations or experiments that could be done.

I am thinking about pursuing an academic career post-PhD, so my question is: would it make sense for me to keep some of these ideas 'in reserve' for a possible post-doc or tenure track position? If I have one or more really 'great' ideas, when is the best time to pull those out of the bag? Now, during the PhD, or save them for later?

What I'm thinking is: if I pull out my best ideas now, it might be less clear whether they were really my ideas or my PI's; however, if I wait, then someone else might have similar ideas and beat me to it (i.e. publish or perish).

To look at it in another way: when is the optimal time during an academic career to fire off your 'biggest impact' ideas (if there is such a thing)? If I have more 'promising' ideas than I think I can work on during the PhD, would it make sense then to keep some in reserve?

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    I don't think you should. As you gain more experience and knowledge, your ideas tend to get more interesting. As an example, in the recent past, I have written many ideas down and never seem to go back to them. I always pursue my latest ideas. – Prof. Santa Claus Jan 17 at 20:24
  • The point in paragraph 3 is valid, but maybe your current PI would be OK with you publishing as sole author. If that is the case, you would get the full credit for your ideas. – lighthouse keeper Jan 17 at 20:27
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    Other people's mileage may vary, but something it took me years to learn: never hold back on an idea. The ideas you have later will be better anyway. If you try to go back to an old one you might get it finished, but working on it won't be nearly as much fun as working on the new idea that you're excited about now. If you have a good idea and you have time, then work on it now - you're not going to regret that later. – Nathaniel Jan 19 at 14:29
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    Whatever you do, don't worry about running out of ideas. They don't stop for a very, very long time. If anything, they get better as you get more experience, and they get more refined as you grow your professional network! – corsiKa Jan 20 at 22:06

I don't see a point in holding back ideas on purpose, at least not for a longer time.

If you are doing well in research, you will generally have more interesting ideas than you have time to pursue. And you will keep having new ideas all the time. So there won't be a time when you will have ample of time, but be in desperate need of a great project.

So you should work now on the best ideas you have now: First, people will judge you by your best work and best ideas. If you work on more exciting ideas now, you will be more likely to secure good postdoc positions later. And if you have a fair advisor, they will clearly credit you with those ideas (e.g. in recommendation letters). So you win by working on your best ideas now. Second, your best ideas now might be outdated in a few years time, or your interests might shift, or you might have even better and more timely ideas at that time, so there is not much point in saving those ideas. Third, someone else might have the same idea and publish a result on it in the meantime, making your ideas not new any more. And finally, even if you don't have the time to work out all ideas fully yourself, it can make sense to share them with colleagues: Maybe they get excited by the ideas and collaborate with you on them, increasing your scientific output.

Finally, what if you will not have good ideas any more in the future? Well, then very likely your chances to secure a permanent position in research are slim, and having kept your old ideas will not save you.

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    This is really helpful advice, thanks. "Working now on the best ideas I have now" makes a lot of sense. – Time4Tea Jan 18 at 1:32
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    +1 Even if you have brilliant ideas now, they most likely will be obvious to anyone in your field by the time you get your doctorate. – Karl Jan 18 at 11:07
  • I agree on following the good ideas now. However, my experience with good ideas is that the more interesting ones did not get outdated, rather, when I am asking around whether anyone has heard of a solution/tried approach X etc., the answer tends to be, no, but that sounds interesting; let me know when you have the solution :-) – cbeleites unhappy with SX Jan 18 at 17:09
  • @cbeleites But aren't those rather the ideas which have always been there, yet no one knows how to actually resolve them? – user151413 Jan 18 at 22:36
  • @user151413: from the feedback I got, no. Some of them turned out to be related to known problems which had totally different names in other subfields, but some of them are apparently new questions. One may say that some have become "askable" only recently, though - sometimes because other developments have paved the way. – cbeleites unhappy with SX Jan 18 at 23:50

When I was a graduate student, I thought I had lots of good ideas; most of them I realized after working on them for 6-12 months were not so good or led nowhere (i.e. they weren’t good at all).

In a competitive field, there is no point in holding back. In 5 years from now the simulation you wanted to do at the start of your PhD will no longer be cutting edge or - if it’s really a good idea - someone else will have scooped you to publication.

Moreover, good ideas actually snowball. A really good idea gets noticed and opens collaborations that bring other good ideas. If the idea is yours, then these collaborators will recognize this as a fact through your comfort and competence with the and will attribute you proper credit.

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    I think the first paragraph is of major relevance. It would be the rare grad student indeed who can accurately assess the quality of their ideas four months into a PhD; learning that skill is after all one of the main goals of a PhD. – Kevin Arlin Jan 19 at 18:16

I'm not sure I'd look at it quite like that. Your dissertation has a problem to solve an/or questions to answer, so you do what's necessary to resolve that. That is the main line.

There is no reason to make your dissertation longer or more complex than it needs to be.

But, along the way you will have ideas for other related (and maybe not so related) things that you might pursue. Rather than trying to find a way to squeeze them into the dissertation, creating a hodgepodge, keep a notebook of those ideas.

Make it a formal notebook, with a new idea starting on a new page, such as a physical notebook. If you use an electronic version, keep it backed up as you may not return to some of the ideas for years.

You can keep this notebook up throughout your professional life, adding to it as ideas come to you. It is also worthwhile perusing the notebook periodically to see if you have things to add to earlier thoughts. At some point some specific thread may ripen into a paper.

With regard to your concern about who's idea something is, there is no reason you can't continue a collaboration with your PI after you graduate. Collaboration at a distance is much more possible now.

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    And when the notebook is full, that's when you get tenure! :) (On a more serious note, what speaks against pursueing projects which don't make it into the dissertation?) – user151413 Jan 17 at 21:02
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    @user151413, actually when all the notebook ideas get checked off is when you get tenure. – Buffy Jan 17 at 21:05
  • Thanks. I really like your suggestion of starting a 'research ideas' notebook. I will definitely do that. – Time4Tea Jan 18 at 1:36

The answer may depend on the field you happen to be working in. As an example, in health sciences, 5 months is an extremely short amount of time. It takes years until you have any data that's worth publishing and as a junior scientist, it is rare to publish ideas or concepts alone (ie. writing a review article, letter to the editor etc.). Those articles are usually written by senior scientists in the field who are invited by the journals to do so.

The focus of a junior scientist (at least in health sciences) is expected to be the production and publishing good data. Once you have the data, the priority is to get it peer reviewed and published asap, and when you do so, you do not want to be withholding any data for later. You do not want to make a hodgepodge as Dr. Buffy said, but in order to get a high impact paper, you want your paper to be rich in content.

A paper that is rich in content gets a lot of citations, not only for the main message that it is conveying, but for the methods employed, individual pieces of data and the occasional reference to new ideas, concepts and possible future research directions (and... you are intending to withhold this?:D). A journal's aim is to maximize its impact factor, so a rich manuscript is the most valuable for them. When you try and divide your content into sub-papers, your main manuscript loses some of its desirability for the high impact journals and the sub-papers will usually be extremely difficult to publish anywhere. Some may never even make it to any journal at all, and the process will drain a lot of time and energy from you.

You also need to take into account the human factor: by the time you successfully published 1 paper, you will be near the end of the road as a PhD student, burnt-out, emotionally drained and depleted. The ideas that once looked great will appear so far away and it is not unusual for individuals to prefer spending time with family (or just some high quality sleep) over pursuing those. I found myself handing some great projects of my own to newcomers of the lab which I never regretted. Most eventually got published and I was the severalth author, but at least they made the finish line. I guess my point is, if you discuss your great ideas with the team now instead of keeping them to yourself:

  1. You may at least get some credit for the intellectual aspect of the work.
  2. The ideas may have a better chance at eventually being realized and your name being associated with it.
  3. You will get criticism, which is great. Some ideas may not be as great as you imagined they were, and may have some room for improvement.

One can't do everything on their own and 21st century science is nothing but teamwork.


In some fields, comming up with new ideas is not hard. But then, you still have to carry the research to test these ideas, and some of them may turn out to be bad ideas or to give results that are not great, even if you though it was some good ideas. What I personally do is to keep track of all the ideas that I have over time. For example, when I read a paper and think about some new possibility, I will take some notes to remember it. Then, when I need to start some new project or give a project to a new graduate students, I will browse through my list of previous ideas to select the best one or to use this as startup point to search for more ideas. Generally, it is better to always work on the best idea first , because you want to publish good research.

But what is the "best" idea? Well, you can think about it from different perspectives such as the potential impact in your field, the time required to do the research (some idea may be easier than others), the risk of failure, the risk that someone else publish it before you or not, etc. So I recommend to list your ideas and think about which one you should give the most priority first based on the different perspectives and your own goals. For example, if your goal is to publish a paper quickly because you urgently need to graduate, you may focus on some easier idea than working on the harder ideas. But if your goal is to get a paper in the top journals, then you should focus on the harder ideas that may have a bigger impact first.

Thus, to summarize, I think you should focus on your "best" idea first, where best is defined based on your goals and the different criteria to evaluate an idea (time, risk, potential, impact, .. You dont need to hold back ideas but I recommend to keep a list of your ideas so you dont forget them. It may be useful later.


Keep in mind: given you are similarly bright-minded as your peers (including current PostDocs and Professors) and you are accessing the same material they are, it is likely that someone else is already working on those ideas.

So ... do not hold back them! On one hand, they can be the starting point of a path to your future career steps and those ideas can be your way out of a possible non-optimal development of your PhD: what if you feel strongly your ideas are correct, you can prove that, but your current advisor is strongly against those ideas? he may be right, but you better found out on your own if he is right or wrong... and you will need support from people in your field already investigating those ideas.

On the other hand, if you are just thinking about new possible numerical simulations or experiments that could be done, only to improve (not changing) current knowledge or getting more precise data, just piggy-back who is doing that already, experiments are something like 10% idea and 90% implementation, so proposing a new thing is worthwhile only if you can commit

  • your time or
  • some undergraduates' time working for you

Keep up your curiosity!


No matter how many ideas you have, they will only award you one PhD. The definition in most disciplines is an original contribution of knowledge (that is, your knowledge and not anyone else's). Hence, if you are sure of your facts you could certainly hold back ideas over and above "enough" if you have a good reason to do so. Many people, however, complete a PhD for personal reasons and in that case doing one's best would be the key driver.

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