Machinations


“Astonish Us”
February 4, 2011, 7:57 pm
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Great post today on the Tomorrows-Professor Mailing list – the advice is clearly applicable to any mathematical or scientific discipline.  It took me surprisingly many years to realize this secret, but now it is the first thing I think about in my research.  I’m including the post below in its entirety.

The Astonishing Secret to Getting Jobs, Grants, Papers, and Happiness in Biomedical Research

I didn’t notice at the time, but there was a point in my life when I more-or-less stopped asking successful scientists how they did it, and someone asked me. And while I offer neither evidence nor assertion that I am successful (indeed, I think I have a great way to go), the fact that I somehow can continue to do this, and occasionally be asked about it, might be regarded as a kind of success. There are some of us who mark success by tenure (a concept that serves as high comedy among my friends who are in business), “impact factor” (ditto), or the recognition of our peers (which is a wonderful thing, but not why I embarked on this career). But I’m going to go with the first definition: getting to do this thing we do, biomedical research, for now and for the foreseeable future.

But like many of my closest colleagues, for a long time I felt like the farm boy Wesley, who was kidnapped by the Dread Pirate Roberts from the movie “The Princess Bride” (which, if you haven’t seen, will be far more useful for your scientific career than anything I can offer here). Every day, Roberts would say “Goodnight, Wesley, I’ll probably kill you in the morning.” Wesley studied hard at swordsmanship and other piracy skills, and one day, when his captor retired, Wesley was given the ship and the title, and became the Dread Pirate Roberts himself. More or less, this is what happened to me, without the pirate part, and my mandate here is to try to tell those of you who may be looking for some success yourselves how you might do this, too.

So here goes. If you are committed to this path, and want papers, grants, and employment for now and tomorrow, I can sum up in two words what it is that is asked of you, and really, everyone who works in science: Astonish us. That’s it. (There is a maxim that says, “If it fits on a bumper sticker, it isn’t true.” While I generally ascribe to this, it does not apply in this particular case. That said, no, I do not have this on my car’s bumper. It might encourage the wrong sort of driver.)

Really. Look at it this way: When I have a great stack of grants to review, I know that only one in ten or so will likely be “F’ed”. (On U.S. study sections, we are not allowed to say the word “Funded.” Somewhat foolishly, we say “F’ed,” and we know what it means. Such is the way of government. It also lightens the mood when we are reviewing grants. Of course, most proposals will be “F’ed,” which in this context means “Not Funded.”) But if in an astonishing proposal the data look compelling, if the approaches are sound, and if the experiments will most likely work, and in so doing possibly change my thinking about the universe (okay, my little corner of the universe) then it will move to the top of the stack. It has to. I have to do whatever I can to make sure it gets done.

I hear a line of advice all the time that I can confidently tell you is nonsense. It goes like this: “In order to get your grant supported, it has to be letter perfect, with absolutely no mistakes, and every experiment you propose has to already be done.” Don’t believe this, it just ain’t so. We get this advice from folks who don’t get their grants supported (and hey, I’ve been there), who see nit-picky reviews that point out every little problem, no matter how trivial. Hence the advice. But this misses the subtext. A favored application has astonished the reviewers, who can be very forgiving about mistakes, chancy experiments, and the occasional missing control if they are convinced that the work has a real chance of affecting how we think about something important.

So okay, you have to astonish us. And if you do this with what you propose, and if you follow through, great papers and a promising career will come in time. But how can you do this? Most likely, nothing in your training has ever prepared you for this challenge. Indeed, it sounds impossible. But here’s the thing: Most of you, reading this, already know the answer.

Sometime in your past, you read, saw, or heard something about the universe that astonished you, so much so that you simply needed to know more about it. And the more you learned, the more astonished you became. And this approach to knowing something amazing, which could not have been known by reason or belief or any other method, convinced you that however astonishing it all is, it is as close to “true” as we can get, in a way that satisfied you. Many people love to be astonished by all sorts of means, but this path to astonishment worked for you, and hopefully still does. It’s why you became a scientist.

The rest is relatively easy. The trick is for us to remember to apply this to our own research: Which avenues of investigation will lead us, not only to information that may be useful, but to something remarkable? Sure, much of what we do is not surprising, amazing, or astonishing, but has to be done anyway. But go beyond the drudgery? Why do we need to spend time, energy, and resources to answer a question? Somewhere at the end of the Yellow Brick Road of your efforts there must be something wondrous you can envision. If not, follow another road.

This is not salesmanship, branding, or trickery; it is not “grantsmanship.” This is at the most fundamental core of what we do, as humans, following our evolutionarily selected impulses to explore our world, in this case with the technical and conceptual tools available to us as scientists. And there is a bonus as well. When we actually achieve our own moments of astonishment in our own research, however fleeting, these represent our real success. The sort of success we got into this to attain. The other kinds will follow, and we may not even notice.

* Douglas R. Green studies cell death and survival at the Department of Immunology, St. Jude Children’s Research Hospital, Memphis, TN. He recently wrote “Stress in biomedical research: Six impossible things,” Mol Cell, 40:176-178, 2010. He is also the author of Means to an End: Apoptosis and Other Cell Death Mechanisms, available from Cold Spring Harbor Press. He is a member of the Faculty of Cell Biology at F1000. For his latest evaluations, click here.

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4 Comments so far
Leave a comment

It is good advice, and is a good test to eliminate a lot of research that people like to do.

Comment by Suresh

True. Arguably, there are times when a grad student is just starting out that it is useful to have one project that is run-of-the-mill, “easy” research. But I think that everyone should always have at least *one* problem they are actively working on that will astonish if successful.

Jared

Comment by Jared

[…] Astonish Us has to be one of the more persuasive pieces of any genre I have read in a very long time. […]

Pingback by “Astonish Us” « Another Word For It

Great article Jared! Thanks for posting it.

Comment by navin rustagi




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