Generating Novel Scientific Concepts
December 30, 2008
Zuska found an interesting article in the Chronicle of Higher Education discussing how scholars generate new ideas, and a nice conversation about it is going on at her place. I have some ideas of my own that have been expressed to some extent in the course of that conversation, but I thought I would collect them and organize them here.
The Chronicle article lists the following four key sources of inspiration for generating novel ideas for future research:
(1) Future research arises from current research.
(2) Future research can be autobiographical.
(3) Future research often arises from conversations.
(4) Future research can derive from what others want and might pay for.
These sources are certainly reasonable, but subject to a fatal flaw. They are each guaranteed to only lead to future research directions that are already visible from where one currently stands. Different approaches are required to generate truly novel–that is, unexpected and unpredictable–ideas.
A route to the truly novel that Comrade PhysioProf frequently relies upon in his laboratory is to invent new methodological of technological approaches. As part of the generation of a novel technique, one needs of course to validate the technique. And 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.
A cool historical example of this principle in practice is the first experiment to demonstrate that electrons have spin. The experimenters thought they were measuring the interaction of quantized angular momentum of an entire atom with an electromgnetic field–which is theoretically predicted to be either -1, 0, or +1–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 partially 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.
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. Inventing 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. Please share with us your own strategies for generating truly novel scientific ideas.
DrugMonkey 
December 30, 2008 at 4:33 pm
I think the literature within one’s own field is generally useful for gaining insight into where the field stood 1-2 years ago. In my field, the data that are presented in the literature stem from experiments that have already been discussed in meetings and seminars, etc, and folks are often moving on by the time the paper is published.
That being said, the literature is still extremely valuable to be. In addition to the journals within my field that I read, I also try to read some publications from fields that are more disparate. Exploring these other areas has often reshaped the way I think about a problem or presented me with tools I might not previously have considered. My latest ideas stems from browsing articles in GI physiology, a field that is quite removed from mine at meetings and seminars. You can’t read everything, but sometimes even this blind squirrel finds her nut.
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December 30, 2008 at 5:02 pm
I don’t have a systematic approach to getting ideas. I can tell you where my latest favorite idea came from: Wishful thinking.
I saw a talk about a new experimental technique at a conference. I’m a theoretical physicist, and I wondered if a computational trick I’d developed might be useful for analyzing some of this data (and whether better data analysis might mean you could get the same information from a faster experiment that collects fewer data points). So I put a student on it. I was 50-50 on whether the trick would turn out to be useful. But I wanted to find out, so it was a good project for an undergraduate who wanted to spend the summer on research.
Meanwhile, I asked myself this question: “Well, suppose the trick works better than expected? What’s the maximum performance we could get from this?” So I started doing the math, and I calculated the optimum performance assuming an ideal algorithm, and how the performance of a non-ideal algorithm would depend on certain figures of merit, and what this would mean for the speed of the experiment. And in doing this, I realized that I’d worked out what the fundamental limit is for an important new technique. Even better, I realized that I’d developed a theory that could predict which types of algorithms would be more useful for the data analysis. So not only did I have a limit, I actually had a prediction for how to get close to that limit.
The particular algorithm I started off with turns out to be kind of crappy, but the student working on it learned lots of techniques that we can use for other algorithms, and now we have a theory predicting which way to go, and setting down the limits (so we have a real benchmark for distinguishing near-optimal algorithms from crappy ones).
Coming up with calculations to improve a technique might sound kind of minor, but the experiments being done are overcoming a limit that physicists used to think was fundamental. And now we have a mathematical theory telling what the new limit is on these techniques.
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December 30, 2008 at 5:06 pm
BTW, in another thread somebody was saying that all the blogging here is too focused on the negative side of scientific careers. Here’s a thread where we get to talk about how we come up with cool ideas. So, great space for positive stuff!
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December 30, 2008 at 5:16 pm
PS, this is both an excellent post, my dearest PP, and an excellent testament to the role blogging can play in professional development. You are the true king of careerism blogging.
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December 30, 2008 at 5:42 pm
This is an awesome topic but I’m feeling lazy this afternoon so I’ll just cross-post most of the comment I already made over at Zuska’s …
For me I found that new scientific concepts came about by choosing to do a postdoc in a different 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 and Isis 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.
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December 30, 2008 at 5:44 pm
Hello — long-time lurker and appreciator of PP’s writing and career advice. There is another method (maybe related to PP’s method), and that’s tracking down seemingly trivial things just to “make sure”. Not accepting easy explanations for gel smears or weird-but-reproducible phenotypes. Like all those bits of RNA that used to get ignored as a smear at the bottom of the gel, til we realized, yes RNAs that small can do something big. It helps sometimes if you’re willing to throw dogma on its head to explain what everyone else shrugs off. One example of this latter case might be prions, where what could have been an endless game of “find the elusive virus” turned into a paradigm shift (and a Nobel Prize). Come to think of it, those RNA bits led to some accolades as well 🙂
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December 30, 2008 at 5:52 pm
My understanding is that the aquaporin transmembrane proteins were identified as plasma membrane water channels via a scenario like MBench describes. Red blood cell membrane preparations separated on PAGE gels always contained–in addition to the bands that people knew about and were interested in–a big fucking band that was a mystery. So Peter Agre’s lab cloned the fucking cDNA encoding that protein and discovered that it was a water channel. Bingo: Nobel Prize!
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December 30, 2008 at 6:00 pm
For those of us in the applied biomedical sciences (such as myself — pain research) and excellent source of new ideas is seeing the most difficult patients. This is not always easy and it is emotionally taxing. Partnerships with medics interested in basic science is a great way to get going on this. There are many doctors and nurses out there that would love to get back into learning about basic science but just don’t have time for it with busy clinical schedules. Informal chatting about basic science ideas centered around some clinical visits is a great way to see the forest through the trees.
From the basic science perspective, I always try to throw in a “what if” experiment for any given trial. We generally collect enough sample to last us a long time for any given project, why not try some shit out while we’re at it. And sequence those “other” bands! The cost is negligible nowadays, why not!
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December 30, 2008 at 6:04 pm
And one more thing. I taught myself to use bioinformatics tools (like all those links you don’t know what they mean on the genomics library websites) a few years back. I also spent some cash for a gene annotation tool that runs natively on my computer and that is capable of scanning for patterns, etc.. Many good ideas have come from running protein sequences of interest through these programs to see what other motifs, TM regions or phospho-sites are there, at least theoretically. With the software I can then file those ideas away neatly and searchably. It takes some extra time but has led to many new ideas so its far from a waste.
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December 30, 2008 at 6:12 pm
Data-mining is another method of generating new ideas. Nowadays, as juniorprof mentions, there are semi-automated and even automated ways of generating hypotheses based on new data inputted into existing networks or algorithms. Automated gene annotation, microarray analysis, proteomics, prediction of DNA binding or interaction motifs, prediction of miRNA clusters, all of these are categories where non-specialists can use data-mining tools to generate new hypotheses to test, often things they never would have considered just staring at or sorting the data based on existing priorities.
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December 30, 2008 at 6:34 pm
I have been fortunate to observe two Nobel prize-winning stories in their infancy.
First, I was at the Cold Spring Harbor Ion Channels course as a grad student. Rod MacKinnon was a visiting speaker (already having made important contributions to the field). As was tradition for speakers, he accompanied the students to lunch. We were asking him what he was working on and what he thought were good projects, etc. He went on a bit, but then said, in a sort of sad exasperated way, that he thought we would never really get answers without solving the structure of ion channels, and that he really wanted to learn crystallography for that reason. Now, you have to remember that almost no membrane proteins had structures solved at the time, and the task was considered damn near impossible for even experienced crystallographers. That fall, Rod took the Cold Spring Harbor crystallography course as a student, then went off to Rockefeller U with lots of money and some time. He was successful. By chance, I happened a couple years later to attend a small ion channel meeting in Salt Lake City, even though it wasn’t really my field anymore. Rod gave a talk and announced the structure at that meeting for the first time. He is an incredible speaker anyway, but the clarity of the structure and the fact that suddenly a decade of observations was explained put it over the top. It is the only scientific talk I’ve ever been to that got a standing ovation. A few years later Rod got the Nobel in chemistry for that structure and continuing structure-based insights.
A couple years after that, as a postdoc, I was at the (then small) international C. elegans* meeting in, I think, Madison WI where in a methods session a couple guys described how their antisense experiments were getting screwy results. The sense strands were knocking down expression more than the antisense. They couldn’t make sense of it, and asked other people to see if they could replicate it. Turned out the effect was real, they figured it out, and Andy Fire and Craig Mello got a Nobel in medicine for RNAi.
For both cases, I guess one could credit ‘insatiable curiosity’, or maybe ‘persistence’. It didn’t hurt that all investigators already had a string of lesser success, giving them the freedom and money to pursue something they found necessary and/or intriguing.
[*C. elegans is not my field anymore either]
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December 30, 2008 at 6:39 pm
juniorprof @#8 reminds me of a prior Zuska post and my repost in response.
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December 30, 2008 at 6:44 pm
i love talking to others at meetings. especially if you go to a very focused meeting- my field has a regional gathering every year. i have walked away from the last few of those feeling very mentally invigorated.
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December 30, 2008 at 7:57 pm
In my experience, generating new ideas is easy. Getting them funded is the problem.
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December 30, 2008 at 8:04 pm
In my experience, generating new ideas is easy. Getting them funded is the problem.
In my brief experience, this appears to be the case.
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December 30, 2008 at 8:09 pm
“(1) Future research arises from current research.”
The last 18 years of my career were spent on a novel scientific concept that was generated from current research at the time. It was involved in testing a prevailing dogma with a relatvely new in vitro model system. Though the model system has proved itself worthy as such, we were unable to generate results that agree with said dogma. The only way to explain our results was to turn the dogma on its head. While the majority of the leading scientists in the field at the time furiously objected to our interpretation of the results, Science accepted them for publication with a cover picture and the rest is history. Though the debate is still going on, I am not standing alone anymore in a large international meeting where the majority of the audience is almost hostile. Today, the concept we generated two decades ago, which was confined to brain tissue, has spilled into other tissues.
Another way to generate new and novel scientific concepts is to closely observed one’s own experiments and not discount outliers. This way we were lucky to make several discoveries that led to new concepts in the field of neuroprotection.
As was suggested by other commenters, experience in different scientific fields, experience with different methodologies, instruments and approaches to solving specific questions can also help tremendously in generating new scientific concepts.
The field of molecular biology has developed mainly thank to the interests of several physicists of the day in macrophages.
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December 31, 2008 at 9:58 am
Not macrophages: bacteriophages.
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December 31, 2008 at 11:18 am
Silly me, PP, you’re right, bacteriophages, of course.
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December 31, 2008 at 1:59 pm
I second the “blind squirrel” strategy outlined by Isis. One of my mentors, the author of more than 1000 papers, was a master of this approach. Specifically, this mentor was an expert at what I call “TOC-scanning.” This is a skill that can be learned and improved with practice. It’s the art of quickly reading the tables of contents of journals outside your field and identifying connections to your own. We are talking about 20-40 journal TOCs per month. If you only do Medline keyword searches, you only find what you are looking for. If Medline is your only strategy for keeping up with the literature, over time you learn more and more about less and less.
A more specific example of obtaining intellectual cross-pollination involves playing neuroscience off of immunology–and visa versa. The nervous and immune systems are two of the most complex cellular systems in the body. Sometimes they evolve recognition, signaling, and memory mechanisms to a much more complex degree than other tissues. The challenge is that the terminology of neuro is often foreign to immuno and visa versa. Learn to understand the language of the other field and then ask how it might relate to yours.
Then, create a new method to interrogate your idea–like the Prof sez–and you’ll have built a niche for yourself that will pay dividends for years beyond the initial intellectual investment.
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December 31, 2008 at 3:27 pm
My ideas always come from a combination of technology development and cluelessness. I take what I know (makin’ stuff) and start thinking about something I have never thought or heard about before. That’s when I get the most fired up and excited and learn the best, and it’s also when I think up the things that make me excited for weeks about how cool they are.
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January 5, 2009 at 10:57 am
I’m a little late here because of grant writing, but novelty in science to me is just exploring the diversity of nature. Using established, or sometimes new, methods to look and nature’s odd balls has provided a wealth of novelty over the years.
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