“Nothing in the world can take the place of persistence. Talent will not; nothing is more common than unsuccessful men with talent. Genius will not; unrewarded genius is almost a proverb. Education will not; the world is full of educated derelicts. Persistence and determination alone are omnipotent. The slogan Press On! has solved and always will solve the problems of the human race.”
― Calvin Coolidge
 

Every lab has a multitude of research notebooks, physical or electronic.  As a student, the lab book is the most obvious record of your trials and tribulations: the experiments that worked and the many failed attempts. Alongside your thesis, lab books are also the most obvious sign of your passage.  They’re history in solid form.

Let’s talk about the future.

The tail end of a PhD isn’t just for sagely offering advice to incoming students and slowly reducing lab hours to focus on “writing.”  It’s also the time to buy a new notebook.  A nice one, faux leather or perhaps moleskin.  This book isn’t for your PhD, or the post-doc, if you’re planning on going that way.  Rather, it’s a place to collect all the ideas, potential projects, and marketable inventions that inspire you.  This is a book for your independent career [1].

Reading Ahead

To steal from Stephen King, if you want to be a scientist, you must do two things above all others: read a lot and write a lot. There’s no way around these two things that I’m aware of, no shortcut.

Great ideas require inspiration, and seeing the work of others inspires.  Over the past eighteen months I’ve read more papers than the past five years combined, even on one occasion skimming through the entirety of the the 1965 volume of the Journal of the Chemical Society (resumed) [2].  Voracious reading lets you link disparate observations into new ideas, and with your own experiences sometimes you see an experiment and wonder, “what would happen if I tried these conditions on this substrate?”  Conferences and seminars can have the same effect, but the literature is far broader and always available.

Being inundated with information, it’s important to view each paper in the context of your research interests [3].  This will skew your view, which means you just might see something the original authors didn’t [4].

Work It Out

Alright, let’s say you were browsing the JACS ASAPs, and you’ve hit on a connection to some 1980’s Tet. Lett. paper.  Quick, write it in the notebook!  Good.  Now, let’s see if it’s worth pursuing.

First, search the literature.  High impact research tends to be pretty obvious, so there’s a good chance that someone else has hit on the same connection.  A quick search on Scifinder, Web of Science, and Google can determine if the idea was worked to its logical conclusion long before you were born.

If you read enough, as the months go on you’ll start to accumulate a fair number of ideas, to the point where it’s not feasible to investigate them all.  To triage I focus on three core questions:

1. Is the idea novel?

Does it stand out from prior work?  If someone has hit on something related to your idea then there’s less to disclose and subsequently less impact.

2. Will this change how people work?

Does this meet an unmet need?  There are a lot of ways to making amides, but not too many for nitriles.  Nitriles are pretty useful, so that represents an unmet need that you could fill.

3. How can you demonstrate the impact?

If your idea is important, prove it.  If you have a new reaction, this generally means making an challenging natural product or therapeutic with ease.  If it’s a med. chem. project, you could demonstrate impact by testing against a whole cell or model organism (collaboration will probably be required; network early).  Keep the demonstration simple; the goal is not to wag the dog.

Show Your Work

Once you have about a half-dozen ideas, it’s time to take the best and start filling in the details.  Ultimately the goal is to get hired/get funded/start a company, and the only way to do that is to convince people that what you want to do will work.  Hope Jahren has put together an extremely good write-up on how to turn an OK proposal into a great one, so in the interest of brevity I’ll point you her way.  If you’re looking for a quick proposal outline, I wrote one up some time, and Kenneth Hanson covered his style as part of a larger series on getting an academic job.

Writing budgets and triple-checking for typos isn’t necessarily fun, but to paraphrase Hope Jahren, think of what you’re asking for.  Hiring and paying a new professor until tenure review costs any given university the better part of a million dollars in start up funds, overhead and salary.  If you had a million dollars lying around, how likely are you to give it to me?

I’d need to be pretty convincing.

Find the Time

Looking over everything, I’m asking for a pretty big investment of your time.  Say 20 hours per bolt of inspiration (~3 bolts per viable idea), another 20 to develop the idea, and anywhere from 20 to 80 hours to write and hone the proposal.  That’s almost a month of dedicated time, sandwiched in between all of your other responsibilities.

Like thesis writing, the best policy is to find a 1-3 hour block of time in your week that generally isn’t productive, and dedicate that to this effort.  For me this tends to be ~8-10 in the evenings (prime blog writing time, unfortunately), Sunday mornings, and Friday afternoons.  Your times may vary, but the point is to dedicate some period to producing excellent research ideas.  With persistent effort you can do anything.

 

[1] Think of the notebook as a cliffs notes guide to your ideas, not a comprehensive guide.  You’ll also need to accumulate supporting references and eventually prepare formal proposals and talks, but there’s no need to carry those wherever you go.

[2] By the end I had fifty or so papers worth looking into a little closer, and one or two that gave me ideas of my own.  Other sighs of obsessiveness include the Dictionary of Natural Products, and Wikipedia’s List of Organic Reactions, all 700 or so entries.  Most of the reactions didn’t stick, but I now know at least a half–dozen different transformations that are really just variations on the Swern Oxidation.

[3] As a bit of an explanation, one of my interests is nitrogen.  Whether that entails nitrogen containing natural products or reactions, I’ve decided my work must involve this bit of the periodic table in some way.  So whenever I see an Aldol, Heck and Pinacol reaction I start adding in nitrogen atoms.  The first two cases give me the Stork-Enamine and Hartwig-Buchwald reactions, but that third…hmm.

[4] Knowing what to focus on is a post in and of itself, and one that’s proven stubbornly resistant to writing.