My PhD supervisor was telling me a story, but for the life of me I can’t find it anywhere on the internet. Granted, I looked for all of three minutes, but let’s at least start with my retelling of his retelling of the story I can’t seem to find.
At the end of the Second World War, the U.S. Military had witnessed the tremendous success of atomic bombs and the work done at Los Alamos. They saw benefit of funnelling money into scientific research—to create bigger bombs and better weapons, of course. An army general, or some other type of military big shot, approached one of the lead scientists, and said to him plainly:
“Suppose I give you all of the money in the world. Infinite access to the U.S. treasury. You can buy whatever you need, hire whoever you want, and work on whatever it is you and your team see fit.
Who cares?”
Now, my three-minute search lead me to two Georges, and one of them likely heard this story (my supervisor says he heard it in some kind of interview, and I definitely believe him), and took it a few steps further. The first, world-renowned chemist George Whitesides (H-index 294), has an interview with the Caltech Heritage Project, in which he says:
“You sign up to be at a university, and then you work hard to get a Nobel Prize or something. Basically, who cares? Your next-door neighbor doesn’t care. You need to decide what standards you’re working for and will you cure a disease or make a better cell phone? Are there going to be jobs created, or academic awards that you’ve won, or what is it going to be? I have my view of that, and other people have different views, and you can take your choice from the menu of ideas that are out there. But I strongly believe that if my neighbor next door can’t understand what I am doing, then probably I should think of something else to do, at least in part.”
And the second George, George H. Heilmeyer, director of DARPA from 1975 to 1977, wrote a set of questions for researchers to think about with respect to their proposed research programs:
- What are you trying to do? Articulate your objectives using absolutely no jargon.
- How is it done today, and what are the limits of current practice? Why are improvements needed? What are the consequences of doing nothing?
- What is new in your approach and why do you think it will be successful? What preliminary work have you done? How have you tested your assumptions on a small scale?
- Who cares? Identify your stakeholders. Who will benefit from your successful project?
- If you’re successful, what difference will it make? What will your successful project mean for your research? For the infrastructure of your institution and future capabilites? For your discipline? Related disciplines? For society? For the funding agency? What applications are enabled as a result?
- What are the risks and the payoffs? Why are the potential rewards worth the risk? What have you done to mitigate risk? What’s Plan B?
- How much will it cost? How long will it take? Who needs to be involved to ensure success? What institutional resources need to be committed?
- What are the midterm and final “exams” to check for success? How will you assess progress and make midcourse corrections? What are the metrics for success? How will you know you’re done?
A few months ago, I gave a small presentation to a high school class, and one of the students asked me if I’d ever discovered something that had never been discovered before. Of course I have, I said, but it’s nowhere near as interesting as you’d think.
As a researcher, the easiest thing in the world is to plug away at our little niche topic, tinkering and probing free from outside constraints such as grant-writing or presenting. Unshackled by these commitments, the scientist can run free through the vast, fresh meadows of the unknown.
For those who aren’t actively-researching scientists, it’s probably extremely difficult to comprehend just how much we don’t know. We remember our university days, of rifling through thousand-page textbooks, and seeing hundreds or thousands of others on almost exactly the same topic, let alone all of the near-infinite other topics actively being investigated. But when you get started, you realise how shaky our foundational understandings can be, and how vast those meadows are.
It’s even harder to understand how many of us, the researchers, the boffins, the so-called best and brightest, wile away our days doing things that don’t serve much of a purpose further than scratching an itch, a scientific curiosity left to fester in our minds as we pass the months and years tucked away in a lab, often paying for our materials, staff, and our own salaries with public money. Free from criticism and the anxieties of passing time.
Because it’s fun. One of the best parts of being a scientist is spending so much time thinking about a single problem, attacking it from all angles, educating ourselves on how to better understand it. There’s often not much urgency, not many higher-ups pressing down on us with their thumbs to increase our performance. Churning out a few papers a year isn’t so hard, after a while, and nor is incrementally moving the needle.
But who cares? Once we’ve done yet another measurement to confirm our results, or we’ve improved our model’s accuracy by another 0.31%, does it actually make a difference(these things can make a big difference, by the way)?
Will the world be left any better because of it?