Good Topics for Future Research - And How You Find Them

It drives me nuts that there are so many great articles in the Chronicle of Higher Education - behind a paywall, where you can't see them unless you have a subscription. The December 19th issue had a great essay, In Search of New Frontiers: How Scholars Generate Ideas. If you have a subscription, that link will be useful for you. If not, try to rustle up a print copy somewhere on your campus.

The author, Robert L. Hampel, talked about how one selects a Good Topic for Future Research (GTFR). He came to question the advice he'd been giving to first year PhD students:

Fill a gap in the literature, identify a problem that has not been studied adequately, and add a brick to the wall of knowledge. That might be how I and others justified our research, but was it how we came upon the topic in the first place?

After talking with a dozen or so colleagues, he concluded that "filling a gap in the literature" was not really how anyone went about choosing a research problem. There were four main "lessons" he gained from his collegial conversations:

  • Future research arises from current research. Things are never really finished, and many projects don't work out as we'd planned. All that cleanliness in the literature is misleading!
  • Future research can be autobiographical. On this one, I'd like to quote the author at length:

    Research is often "me-search," a friend of mine likes to say. Ideas for research topics can stem from brief personal experiences from childhood or threads that run throughout their professional lives. For example, gender equity in science education has riveted a colleague since she majored in chemistry in college. Another colleague's passion is the give-and-take of arguments, "so I think that's why I'm studying fifth graders' persuasive writing." What "voice" means for minority scholars fascinates an African-American academic who feels that the traditional norms of scholarly discourse stifle her own creativity. For those colleagues, their lives are inspiration, but not evidence -- in other words, they are not autoethnographers.

    Sometimes a good project arises from family life. A child psychologist extended her work on infant communication when her 14-month-old son was pointing incessantly to the refrigerator. "I'd take one thing out after another, and he finally seemed to find what he wanted," she said. "So I got excited and found three families, studying how kids make their ideas known and how they correct your misconceptions when you're wrong about what they want."

  • Future research often arises from conversations. You know this one. Have lunch with your colleagues, visit them in their offices, hobnob at conferences. I don't care if you're shy and you don't like talking to people. Get out there and circulate!
  • Future research can derive from what others want and might pay for. This isn't just the obvious - grants and contracts. It can also be solicitations for a special volume (this is more likely in the humanities and social sciences than in the biological and physical science and engineering).

Apparently, just as no one gets taught how to teach (though this is changing some), no one gets taught how to generate research projects either. Hampel notes:

That lack of formal coaching may explain not only the variety of approaches that my colleagues take to identify ideas for future research but also the different mechanical ways that they keep track of them. One used a single folder; another had a separate folder for each idea. Two kept journals -- one was strictly about research, the other resembled a personal diary. Three used computer files ranging from the very simple to the elaborate, cross-referenced array with shorthand and symbols throughout. Another had index cards. The only common pattern held for the four people who used no system, preferring to carry the ideas in their heads, confident that they would never run short of topics.

How do you generate your ideas? And how do you keep track of them? Hampel also wonders what we are doing to document the ideas we haven't had time to work through, so that those who follow us can pick up where we have left off after we are gone. He doesn't want the fruits of our intellectual labor to just vanish when we do. What do you think of that idea - leaving a sort of legacy notebook of ideas? Right now, mine consists of a pile of clippings and cryptic notes to myself that I doubt anyone could make heads nor tails out of. I'm not saying the world will be in terrible shape just because I never got to blog that one insight about that one article or book I read...but maybe you have some really fab research ideas that could make the world a better place. Are you keeping track of them somewhere?

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Fascinating! Comrade PhysioProf generates directions for future research using a method not mentioned in that article: by creating new methodological of technological approaches. I have found that taking a new approach and applying it to an already answered question as an initial exercise in validation--you know what answer to expect so you know if the new approach is working--almost always leads to unexpected results and opens up large tracts of previously unimaginable fertile ground.

I keep a word document on my desktop labeled "ideas." I date entries and describe whatever is rattling in my head to the best of my ability. Later--sometimes months--I check back to find a particular idea and discover several good ones I've forgotten about.

Yes, CPP, yes. Boys and their toys. We know.
Your comment reminds me of a another scientist. Her advice to grad students was to make a list of all the unknown things about a particular subject, and all the tools one had for studying things ('tools' in a fairly broad senses like "we have an antibody that recognizes this protein), and then start linking them up appropriately. This works well in an established lab where you have a lot of tools, or when you are pretty good at knowing who has what in a field.

Thanks for blogging this, Zuska! It was very much something I've struggled with as a graduate student. Not so much having questions I'd like answered, as determining which of those questions might be "projectable".

I mostly keep a bound comp book in which I take notes from seminars/conferences and ocassionally journal articles (though more typically I print those out and write on the copy). There are almost always neat unanswered questions in there.
But I'm still looking for a good organization system for all this information!

There is one final thing. I have a postit above my desk which says "WANT experiment X" to remind me of an idea I had last June. My advisor has somehow (finally) magically come up with this idea so now we can actually buy the antibodies I need to do it...

Regardless of the particular method used to generate new ideas, the key is that one needs to figure out ways of exposing oneself to the completely unexpected and unpredictable. Studying the literature to look for "unanswered questions" is guaranteed to only lead you down roads that are already visible. Genuinely new ideas are, by definition, not visible from where a field currently stands. Developing novel tools, techniques, methods is one way of heading down roads whose existence one couldn't have predicted ahead of time. There are, of course, others.

Your comment reminds me of a another scientist. Her advice to grad students was to make a list of all the unknown things about a particular subject, and all the tools one had for studying things ('tools' in a fairly broad senses like "we have an antibody that recognizes this protein), and then start linking them up appropriately.

Oh, and just to be clear. What I am proposing is the exact opposite of considering "all the tools one had". I am proposing inventing new tools.

This is such a useful post. I finished my PhD two years ago and have had trouble thinking of _anything_ to write about for the past year. I can't get a full time job (though sessional teaching abounds) and I have very little contact with other academics. I can't afford to go to conferences (though I have managed to scam my way into a few small bursaries for conferences in the past) and I'm beginning to feel very depressed about the whole 'being an academic' thing. Though my PhD was passed without corrections and I also have an MA by research and a BA with first class honours, the fact that I don't have a book (or a very long list of published articles and a big fat grant for a new project) means that finding full time work is really not in my future.
If I could only start a new project that was both interesting and 'marketable' (as in 'will score me grant money, secure my reputation as doing 'new and valuable research')...
But I can't, because I am out of ideas.

Your post was so nice to read - it reminded me that finding ideas for new projects is not something that happens in a moment of glorious, isolated artist-like inspiration. It is a product of process and environment and discourse.

.... now I have to get me some of those things. :D

My strategy was to read, read, read. Two strategies: read one's area deep into old history; read other unconnected fields.

I got some great ideas from reading every paper in the history of my field up till 1995 (after that the molecular explosion made me filter to some extent). I got ideas from papers published in 1960s, 1940s, 1920s, 1890s....

I did my best work when I made connections between 3 fields that nobody thought were connected (and thus people are unfamiliar with each other's literature). Apart from circadian stuff, I also got well versed in the literature on crustacean aggression, avian ecology and evolution, behavioral neuroendocrinology, poultry science, insect behavioral ecology, philosophy of science, evolutionary theory... In addition to reading I also went to 2-3 seminars every week - in various departments, from Zoology, Entomology and Genetics, to Psychology, Poultry Science and History. Got some great ideas that way.

I have found that taking a new approach and applying it to an already answered question as an initial exercise in validation--you know what answer to expect so you know if the new approach is working--almost always leads to unexpected results and opens up large tracts of previously unimaginable fertile ground.

huh. very fascinating. I do stuff very unlike PP and with very different characteristics vis a vis "tool generation". and yet I find a similar effect of what one thinks at the outset are validation experiments. I don't know that I would ever (in a million years) recommend this as an explicit strategy. Now I wonder why this is so. I must think on this more...

A cool example of this is the first experiment to demonstrate that electrons have spin. The experimenters thought they were measuring the interaction of angular momentum of an entire atom with an electromgnetic field, and thus strongly expected that the incoming beam of atoms would segregate into more than one beam after interaction with the field, with the predicted number of beams being three.

It turned out that the beam did segregate--thus supporting their expectation--but into only two. It turned out that they were measuring the interaction not of atomic angular momentum with the field, but rather electron spin.

At this point in time, there was no theoretical prediction that electron spin even existed, so it would have been impossible to intentionally design an experiment to detect electron spin.

DM- cause it takes the Chutzpuh of a CPP to take a brand spankin new method that no one has ever used before, compare it to the three previous states-of-the-science, determine that there is a discrepancy in the measurements, and immediately conclude that OMG EVERYBODY WAS DOIN IT RONG THIS WHOLE TIME!!!ELEVENTY!?

Interesting question. For me it was choosing to do a postdoc in a much more specialized field than my PhD. By doing this, I learned a whole set of new techniques and ideas that have made me question the simplistic and outdated approaches in my former, but much loved, field which has subsequently opened up several new research ideas. So I guess you could say that I agree with PP in that trying something new can help generate supercool ideas - even if the new stuff has been borrowed from another field or simply applied in a new way.

A very successful colleague once told me: "Ideas are cheap."

By that, he meant that ideas are easy, carrying them through to fruition is hard. I agree, and increasingly see the wisdom in his words.

If you're curious, ideas pop up all the time. I find it hard to read about something and not wonder 'How does it do that?' or 'But what about if...?' or 'What if it's this instead?' The hard part is getting the motivation or (even harder) the time to see if anyone else already has the answer. Most scientists have had the experience of lying awake all night incessantly wondering about some thing. With reading and talking to people, I find most of the time someone has already answered my naive question. In which case I can sleep again. Sometimes no one has an answer, and I am left with my question. After a while some of those questions don't seem so intriguing any more. But some keep gnawing away. In some (a very few) of these cases, I conclude that I am actually well qualified to answer my own questions, and try to do so.

Or, more accurately, I convince a grad student and/or postdoc to answer it, and work on getting funding to get it done. Being PI is great for curious people happy to delegate.


yeh. this does not go down so well with grant review committees in many cases. which is why if this is your reflexive bent* to a lot of topics, you may want to think this out a bit...

*not sayin nuttin'

1. Laziness. Really, honestly, I am lazy. Many of my ideas come from, "This is a pain in the ass! Three DAYS to do this shit? And I'm supposed to do it HOW many times? The hell with that!" and finding some way to do it in much less time. This encounters the same problem as DM mentioned with new methods though.

2. Ah, the joys of industry. I can afford to run things high throughput style and generate a zillion tons of data, then sift through it with fancy-shmancy statistics. I get a lot more fish on my fishing expeditions than I can ever hope to fillet, though.

3. Read everything, especially stuff not in your field. Other fields think differently about problems, which teaches you to think differently too. The downside to this is that people in your regular field don't usually know what you're nattering on about. Works well for industry, where they care more about results and economics than about Dr. Superstar's pet hypothesis/gold standard method/egomania, but does not go over well in academia where interdisciplinary work is smirked at.

I agree with Corturnix and Lora about reading everything. Especially stuff that is not in the precise field you are working in. But when people don't know what you are talking about (but pretend they do) it is very frustrating. That has happened to me more than once.

Focus more on people's data than on their conclusions (which usually follow from their hypothesis, not necessarily from their data). If their data fits another hypothesis better, that might be the correct one. In many fields researchers get caught up in some wrong ideas and it can be difficult for the correct ideas to get through the conceptual barriers that get put up, especially if it is senior people who have the wrong ideas and have invested their careers and reputations on them, and then yes OMG EVERYBODY WAS DOIN IT RONG THIS WHOLE TIME!!!ELEVENTY!?

But if everyone was doing it wrong, then the right answer is considered extraordinary and so requires extraordinary evidence which can be extraordinary difficult to get without extraordinary funding which requires extraordinary evidence.

Data from 20, 50 or even 100 years ago is just as good as data today. It is only ever as good as the scientists producing it.

Never blame a misunderstanding on the concept being counterintuitive. If your intuition doesn't match reality, it is your intuition that is faulty and must change. This is the main reason people persist in wrong ideas, because they are intuitive and they are unwilling to change their intuition even when it is wrong.

Once you find an intuitive concept that is wrong, often many fruitful avenues for research open up when that wrong idea is discarded.

Once I appreciated that the idea of homeostasis was wrong, the data in the literature became much easier to understand with fewer and simpler hypotheses; generating more avenues for research than I can possibly pursue.

Thank you for this discussion! I just started a tenure-track position and I am trying to establish my own research program. I don't want to continue on with my PhD research (not directly, at least) and while I have a few ideas that I am excited about, the thought of finding new questions to explore for the next couple of decades is daunting! I am finding that talking to others in the department is very useful - I have two collaborations in the works already and they are opening up avenues I wouldn't have discovered on my own.

Sometimes I worry about not being able to blog more frequently...then when I get back to my blog I see that just by my having shut up and gotten out of the way, people then have a wonderful discussion! I am glad this post and discussion has been of some use to so many of you. You would think that talking about how to generate new research ideas would be something we'd do at least once in awhile as part of training grad students, but apparently not. So, all you PI's out there, take note! Start havin' some conversations with your students and postdocs!

Holy crap, Heather. How the heck did you manage to get a tenure track position without a research plan already in place? You must have impressed the hell out of them with your CV and in the interview.

The collaborations sound good but don't ignore the stuff that excites you. This isn't a factory job where you can just punch a clock every day and be successful. You gotta have passion.

I do field-based research with undergrads, and I get my best research ideas by going out into the field with students and listening to the questions that they ask. Field trips with other professionals are great, too - brainstorming sessions while on long hikes in beautiful places can be inspiring.

My two cents: Research something you love, something that keeps on thrilling you, no matter who or how many people care about it when you start. You've got to care about your work more than anyone else, and pretty much any area contains questions that deserve to be answered - and may lead to new questions beyond your wildest dreams.
Nothing is more powerful than true love to get you through the hard times.

It turned out that the beam did segregate--thus supporting their expectation--but into only two. It turned out that they were measuring the interaction not of atomic angular momentum with the field, but rather electron spin.

I got some great ideas from reading every paper in the history of my field up till 1995 (after that the molecular explosion made me filter to some extent).

we do extract ideas from realities but the findings dont have universal application. how a researcher assures fruitfull and utilitarian research area?