Dear Uncle Mole,
I'm sitting here writing to you on my beloved MoleBook Pro, listening to my iPaw, and idly monitoring my eye-phone on the chair next to me so I don't miss any text messages. It's that time of year when snow flurries (and more) make their appearance, so even though I'm not much of a coffee shop writer during the rest of the year, the winter doldrums are a different story. The funny thing is that looking around me, I'm surrounded by people wearing the white earbuds of a Grapple product. And with that I have to pause, yet again, to think about how much Steve J changed our lives.
His untimely passing was certainly a shock, a tragedy at the personal level for his closest family and friends. Yet it was also a loss for those of us who found our lives changed – even when we didn't know they needed changing – by one of the many products Mr. J created during a creative career the output of which can only be described as staggering. To be fair, did I really need an iPaw? Well, no, not exactly. But, my CD player didn't fit in the pocket of my lab coat, and without the music I don't think I would have stayed quite as late in the lab for quite as long as I did – and what would have happened to my work without those late-night epiphanies? Would the publications that are the currency for any budding scientist trying to make her way in the world have come together on another laptop, one that didn't have that bright and shining little pomegranate on the front of it? Probably. But it's one of my favorite possessions, nonetheless. Love him or hate him, Steve J was a unique and brilliant mind. And he stands as the perfect example of something I've been thinking about a lot lately, Uncle Mole, namely the idea of innovation. What does it mean to be an innovator and does it really matter?
I've been working on a little side project these days, and it's one that I'm really, really excited about. I can't be any more specific at the moment since right now, at least, it's not enough of an established project to justify anything more than ‘after hours’ work on my own time. The thing is, Uncle Mole, I think this might be the most inspired idea I've ever had. It's a bit of a wild intellectual leap – and it may well go nowhere – but if I get lucky, this could be big, the kind of thing that shapes a career. I still have a lot to learn before I'm ready to launch out on my own, and I know the training of my day job is crucial to gain the tools I need to be independent one day. Yet as I go about my day-to-day business, I can't help but contrast the approach we're implicitly trained to take, the play-it-safe, one-step-at-a-time, spend-a-career-on-one-protein model, with the big ideas that have truly shaped the field of discovery. Without people creative (or crazy?) enough to imagine the impossible, would we have PCR or nanoparticles or the human genome?
On the one hand, I can see the value in being methodical and systematic and longitudinal. Sometimes it's a challenge to see the forest for the trees, but alas, this Molette has the opposite problem. The most illuminating quote from my graduate school days: “A really lovely proposal, but you do realize you're not running a lab yet?” Flight of ideas – in the scientific sense, that is – does need to be reined in by the practicalities of manpower (should I say molepower?), funding, and time constraints. Navigating the process of scientific independence has also given me a new appreciation for the delicate balance between a fresh idea and one that is not too much of a risk to secure funding. And therein lies the rub: science isn't cheap. Someone has to provide the finances, and the powers-that-be like to reward proposals that offer a reasonable chance of a return – even a small one – on the initial investment. This seems to be especially true in these days of economic uncertainty. In the end, the establishment view is that it's better to be practical (even a bit stodgy, if need be) than be given to flights of fancy that deviate too much from what everyone else is doing.
The problem, Uncle Mole, is that I am not practical. I like 4-inch stilettos and dark chocolate infused with chili peppers and 6-mile runs at midnight. And now I have this crazy idea that has me more excited about science and discovery than I've ever been – and there isn't a government agency in existence that would give me a dime to explore it. So how do does one navigate the line between fun ideas and fundable ones?
I'm not sure I have it all figured out just yet. But what I have noticed are a few characteristics the most forward-thinking among us seem to share. First, taking risks is important. Safe ideas are rarely memorable. However, equally as important as the creativity of one's ideas is the timing of their introduction. As with everything in life, there is a time and a place to color outside of the scientific lines. The key to an innovative idea is letting it flourish at the right time, not, for example, in the midst of an interview for a first academic appointment or during one of those years when existing grants are competing for renewal. Yet just because it might not be the right time to introduce a novel concept doesn't mean we have to abandon the idea. In fact, what seems to be the hallmark of those creative thinkers whose footsteps I'd like to emulate is that no matter what they're working on, they never stop being inspired. And when you think about it, the world truly is a wondrous place. Keeping our eyes open to the intricacies of our own research, the work of our friends and colleagues, and even the multidisciplinary connections that come from reading a newspaper or going to the symphony or whatever it is that gets us engaged with the world… these are the things where an unexpected thought can flourish and blossom into something amazing.
I'm no genius in the making, and I know I must keep my nose to the proverbial grindstone to learn all of the things I will need to make a go of it on my own one day. Yet if there's one thing I want to take with me into this year, it's the openness of an always-inquiring mind. And stay tuned for news of my crazy project!
Always,
Molette
Dear Molette,
Wonderful to hear from you, as always! Surely, the stilettos are not dark chocolate? No, of course not, just me being dense (and I love chili in my chocolate!). And, like you, I love my Grapple products. Thank you, Steve.
Okay, to your rather important point: how do we do really novel work when the funding mechanisms are so antagonistic to risk-taking? Or to paraphrase what you said, “how can we put the ‘fun’ in ‘fund-raising?’”
Well, I've got a few things to say about this. But first of all, here's this: It's fantastic that you're thinking about things that are novel, wild, exciting, and that get you excited. This is one of the most important things you can do to succeed in this field, provided that you are actually right now and then. But that's sort of beside the point just now – keep thinking about cool things!
As you've mentioned, funding is really tough these days. But before we feel too sorry for ourselves, we need to remember that this has always been tough – the vast majority of proposals have always gone unfunded (it is only when things get tougher that we think that the ‘good old days’ were easy). The same rules apply, but perhaps more so now (and yes, many applications that have great merit sink below the waves in these hard times). So I'll tell you these rules as I see them, and then I'll tell you a couple things you can do about it.
First of all, we've got to remember the way applications are actually evaluated. A group of scientists sit down with a fairly large number of grant applications to evaluate, knowing that only a minority will actually be recommended. So a reviewer looks through the ones she has and decides if there are any that she really wants to fight for. This is necessarily subjective, but not as much as you may think – what makes an application exceptional for one scientist often makes it exceptional for many. And what makes it exceptional? It has to make them say, “wow.” It has to be amazing. Then, when they tell the other folks around the table what they read, those folks have to say “wow” as well. If they do, then there's a very good chance they'll support it. Okay, a good chance, anyway (as we agreed, times are tough). Think of it this way: if I am reviewing and I have one application that really makes me say “wow” and several others that make me say, um, “really nice,” then the wow has to be the one that I put first.
As a result, most of us get turned down, and we receive explanations (‘reviews’) that seem nit-picky; stating this or that small problem with the work or the proposal, and we complain that the reviewers want so much. We tell each other that the only work that gets supported is work that is already done. We tell each other how unfair it all is (and it is!), but then again, would it be more fair if really exciting work that is backed up by strong preliminary results was passed over because our proposal was in the stack?
But I know what you're thinking – my proposal was really exciting and it was passed over because someone else in the stack was more famous, or had more resources already to present more to the reviewers. And worse – it's an ‘old boy’ system where everyone just supports his/her friends (yes, many ‘old boys’ are female). Which brings me to the second rule.
There's a thing called ‘track record’. Some labs have a history of doing work that is wow, again and again. They don't just get it done – they get it done amazingly. What would be really unfair would be to deny them the opportunity to do this more; unfair not only to them, but to us, who will read about this potentially amazing work in the future.
But here is the thing, and it may make you feel a bit better about all this. Once you actually GTFM (get the frickin' money), you are not obligated to actually use it for the specific experiments you described. Indeed, you can go in an entirely different direction, should your research indicate that this will be more important, interesting, and amazing. The only thing is, there is a ticking clock, so there are consequences if you are wrong and produce nothing (at the very least, you won't get your grant renewed; at the worst, your lack of publications will make it even more difficult next time).
But isn't this exactly the sort of chance that our heroic entrepreneur inventors take? Using investments (or their own money) they gamble that their ideas will lead to the breakthroughs. Do you think Steve gave in to the conservativeness of the system and decided not to test his ideas, but rather go with the tried and true? Of course he didn't. And neither will you.
Really, it is so much easier for us than for people like Steve: We don't have to go door to door looking for sponsors of our research – we have government and private foundations coming to us for proposals, and they invest in our ideas, assuming we can convince them that they are exciting, important, and likely to work. Most things don't, you know, but show them that yours do, and you'll do great.
So finally, here's what I want you to do. Put on your fabulous shoes, eat some spicy chocolate, and think of the most exciting project you can imagine. Spend a few weeks generating data that suggests that you might even be right (and in the process, show us that you know how to do the sorts of experiments that you propose), and then generate a proposal that asks the most astonishing, amazing questions and shows that you can get the results to answer them. No, I can't promise that it will be approved the first time you try, but I can promise that the approach is the only one that will GTFM, eventually, and more importantly, will allow you to do the work that is actually worth your time and energy. After all, isn't this why we got into this in the first place?
As an aside, I have a feeling that others may be reading this, so I have a quick point to make to those who will flame me for taking this optimistic position. If you completely disagree with everything I've said, and you are angry at this system and angry at me for giving this useless advice, maybe you can let us know what is working for you, and how you get joy and satisfaction out of this endeavor we have undertaken? Because this is what works for me, and that's the best I can offer. Molette, I know you get it!
Love,
Uncle Mole
