On Ideas

MC3 asked:

“Far too many candidates are indistinguishable in that they don’t have original ideas at all; instead, they regurgitate what they’ve heard at conferences or in group meetings to be the next obvious steps.” I agree with this. But to be honest, I think the reason many people just regurgitate what they’ve heard at conferences and group meetings is because it’s really REALLY hard to come up with new, creative, and feasible ideas. So what about those of us–like me–who often find it extremely difficult, if not impossible, to come up with original ideas? Does that mean we’re just not meant to be in science?”

I can’t say whether someone has a future in science or not without knowing them well.

But I know that sometimes people have ideas, they just don’t know that those are viable ideas or they overestimate how much novelty is needed for something to be considered a viable idea.

Often the best ideas come from picking on a scab that was formed over a question that hadn’t been successfully settled in a research area. If you are honest about what you do or don’t understand, you will find that there are things that everyone glosses over but they are far from understood. If you pull on that thread of the unknown, you can uncover a whole set of interesting questions.

Are you curious in general? Are you a person who enjoys talking about science with colleagues, listening to talks, meeting visitors? In general, ideas can form almost subconsciously if you provide your brain with enough varied input to chew on.

Follow your interests. If you are really, truly into something and are in the position to pursue it, then do so. Follow your gut.

Follow your gut, but also learn from those with more experience. Learn how to estimate how long things will take, whether they are a good use of your time, how much manpower is needed, how to predict potential pitfalls and what to do when they happen.

A few years ago, one of my then senior graduate students read a proposal and said something like, “Oh, this looks totally doable. I thought you would have to propose something much more out there.” We started talking about what a proposal is, that it’s not a pie in the sky, but work that builds on what is known in a logical, well-justified way. That it’s not just the crazy idea, but that you need to convince people that spending money on you is a good idea.

So if you wonder whether you have sufficient ability to generate ideas, ask yourself:

When you work as a grad student or postdoc, are you systematic about your work? Do you try to clarify every detail in your understanding? When your advisor asks you if you checked something, do you often find that you already thought of the issue on your own and checked it? These are good signs.

Do you enjoy listening to your lab mates present their work? How much do you know about your lab mates’ work? Would you be able to give their talk at a conference? (That’s an excellent exercise that I’ve been meaning to implement as training in my group — have students present each other’s work.) Building a broad base to your expertise is good.

When you go to a conference and listen to talks, do you feel like you have questions? Do you notice things that are unclear, or missing, or suspicious, or perhaps unusually insightful? Do conferences make your mind catch fire in the best sense? I often find that I have a lot of ideas after a good meeting.

Can you identify a good project the size of a single manuscript in a society journal? How about in a prestigious journal? Now can you identify a project the size of a typical grant in your field? A project is like a novel, where each paper is like a chapter. The project has to have an overarching idea, a set of coherently sewn together smaller questions, each answered within a small number of papers.

The unit of scientific communication is a research paper. Understanding what makes a paper, how much is enough for a paper, how to weave a paper-worthy scientific story — these are all key ingredients in starting to believe in your ability to generate ideas.

And, of course, some people are happiest when doing technical work within the context of a large project outlined by someone else. Such people are usually very detail oriented.  Others wouldn’t want to have anyone else tell them what is to be done, may prefer big-idea thinking (and selling those ideas) to in-the-trenches technical work; these folks, if they are creative and good at marketing, they can go far; otherwise, it can be tough.

Blogosphere, what do you say? 

4 comments

  1. That you said this very well! “Picking the scab” is a nasty image but exactly what I’ve done in my career (20 years as a faculty member come December this year, so although I could have done better, I’m in some position to say it works!).

    If MC3 is fairly early career, then I’d encourage them to believe that ideas are something which will come, even if you don’t have them at an early stage, as long as you are open to them. That’s how it worked for me!

    I did a UK PhD, so was expected to submit at the end of three years. At the end of two years I had one very small idea, more of a niggling “there’s only one paper on this specific thing and it’s from the 1960s, yet everyone is so sure it’s true, I wonder if I could test it a little more”. At that point my PhD supervisor suggested I apply for a couple of funding schemes which would fund my own post-doc salary (these things take a year or more to come together), so I wrote up my small idea, my PhD supervisor pointed me towards a possible host PI for a scheme where the money was specifically for the holder to go abroad, and I put the application in along with a few others.

    I got the funding, and went overseas for two years with my own salary but my PI’s lab paid my research expenses (my field is not very expensive). By the end of the first six months out “on my own” (and interacting with a new field area, new set of ideas, new system, which was all very stimulating), I had three or four sub-questions, and a serious methodological problem (essentially a key piece of kit was broken and wouldn’t be fixed for a year), so I tried using a different method, nothing NEW, but no-one had used it to look at my specific problem, to look at one of the sub-questions. By the time I began applying for faculty positions in year two, I had a couple of nice clear questions and an unusual if not original method (which lent itself to being done on the cheap/by undergrads – bonus!), and my PI was wonderful in helping me come up with an overall sentence for the topics.

    I spent the next two years back in the UK, applying for faculty jobs and doing several short stints of work somewhere between consultancy and post-doctoral research on other people’s projects, and each one of those sparked questions. It was like I’d turned on a tap! Suddenly there were questions everywhere.

    Once I got my faculty job, learning some discipline was hard (especially as I’m NOT at an R1 and DON’T have anything like the resources peers at top institutions, or even decent research institutions have) but the requirement for ingenuity with limited resources let me come up with a niche which is largely mine (not that other people really WANT the niche, but they like what I do well enough that I publish well, get asked to train other people’s grad students and run workshops at conferences, and sometimes even get grants, and the few graduate students/post-docs I’ve had of my own have all gone on to good careers that they wanted, some within the academy, some outside it).

    I nearly didn’t try to go on after the PhD because I assumed a fully-fledged academic had to have lots of ideas, and I didn’t. The other PhD students who DID have ideas, lots of them, and weren’t quiet about it? Nearly all male (surprise surprise) and most of them did not go on to research careers. If you have curiosity, there is hope for the ideas to come.

  2. Very interesting post, and this part particularly resonated with me:

    “A few years ago, one of my then senior graduate students read a proposal and said something like, ‘Oh, this looks totally doable. I thought you would have to propose something much more out there.’ We started talking about what a proposal is, that it’s not a pie in the sky, but work that builds on what is known in a logical, well-justified way. That it’s not just the crazy idea, but that you need to convince people that spending money on you is a good idea.”

    When I first got to see a (successful) proposal written by my advisor as an early/mid-stage PhD student, I had a similar reaction (internally!). I definitely wasn’t well calibrated to what a typical proposal (successful or otherwise) looked like, and as you said, I hadn’t thought much about the feasibility aspect as compared to the novelty.

    With regards to faculty applications and proposing new ideas, one thing that has been helpful to me is that when candidates interview at my PhD institution, they give a seminar that is open for anyone to come watch. There is also a closed “chalk talk” later, where I believe the candidates explain their proposed future work in more detail, but most spend at least a few minutes on future work in the open talk. So that has been helpful to see, in contrast to my undergrad institution where all of the faculty interview was closed to students.

    Finally, I think that one’s capacity to come up with new, viable, interesting ideas is to some degree an inherent or fixed trait, but there’s also a lot of potential for growth at least early on, i.e. throughout the PhD. At the beginning, I worried that I simply didn’t have the ability to come up with enough (or any!) good research ideas to apply for faculty positions. As a senior grad student, I’m now much better calibrated to my field and have so much more background knowledge, so I find that new ideas come to me much more easily.

  3. My PhD supervisor always said that we should look at the literature from 15-20 years ago to see what would be interesting to tackle now. I find that is still as true as when I was a student. Many times, revisiting a problem with modern techniques can help tease up misunderstood/unclear aspects and also help send your research in a new direction while starting with something feasible.

  4. ProdigalAcademic wrote ” we should look at the literature from 15-20 years ago to see what would be interesting to tackle now.” That works in some fields, but not in all. The problems that were filling the literature in bioinformatics 15–20 years are now mostly irrelevant, as the experimental technology that produces the data to analyze has been almost completely replaced by new experiments that present radically different challenges.

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