Ed Boyden on the State of Science

I just listened to Tyler Cowen’s in­ter­view with Ed Boy­den (link and tran­script). The sec­ond half con­tained a lot of ques­tions about cur­rent sci­en­tific in­fras­truc­ture, and Boy­den had a lot of in­ter­est­ing com­ments, so I’ve re­pro­duced a few par­tic­u­lar quotes here and added head­ings.

(Things I’ve not quoted that LWers might be in­ter­ested in: Boy­den said that whole brain em­u­la­tions prob­a­bly work in prin­ci­ple, that he med­i­tates ev­ery day and has used an in­ter­nal fam­ily sys­tems med­i­ta­tion for 10 years.)

The Sur­pris­ingly Poor State of Funding

COWEN: How should we im­prove the fund­ing of sci­ence in this coun­try?

BOYDEN: I like to look at the his­tory of sci­ence to learn about its fu­ture, and one thing I’ve learned a lot over the last cou­ple years — and it’s even hap­pened to me — is that it’s re­ally hard to fund pi­o­neer­ing ideas.

Brian Ko­bilka, who re­cently won the No­bel Prize for solv­ing the struc­ture of the G-pro­tein-cou­pled re­cep­tor — and for con­text, one-third of all drugs tar­get this class of molecules, so it’s a very, very im­por­tant class of drugs — he lost his fund­ing be­cause he wasn’t mak­ing progress fast enough. If I re­call, he had to moon­light as an emer­gency room physi­cian to keep go­ing on his re­search.

Doug Prasher, who cloned the gene for green fluores­cent pro­tein, which has been used in some­thing like a mil­lion biol­ogy stud­ies, bal­l­park — he lost his fund­ing and even­tu­ally left sci­ence, ended up driv­ing a shut­tle bus for, I be­lieve, a rental car fa­cil­ity or some­thing.

Any­way, there’s so many sto­ries. For me, it be­came per­sonal be­cause when we pro­posed this ex­pan­sion microscopy tech­nol­ogy, where we blow up brain spec­i­mens and other spec­i­mens a hun­dred times in vol­ume to map them, peo­ple thought it was non­sense. Peo­ple were skep­ti­cal. Peo­ple hated it. Nine out of my first ten grants that I wrote on it were re­jected.

If it weren’t for the Open Philan­thropy Pro­ject that heard about our strug­gles to get this pro­ject funded — through, again, a set of links that were, as far as I can tell, largely luck driven — maybe our group would have been out of busi­ness. But they came through and gave us a ma­jor gift, and that kept us go­ing.

Boy­den also said this sen­tence in pass­ing, which seemed strik­ing to me about the in­su­lar­ity at the high­est ech­e­lons of sci­ence.

BOYDEN: I read a statis­tic that 40 per­cent of the pro­fes­sors at MIT trained at one point in their ca­reer at Stan­ford, Har­vard, or MIT.

How to Im­prove Funding

COWEN: Let’s say you had $10 billion or $20 billion a year, and you would con­trol your own agency, and you were start­ing all over again, but cur­rent in­sti­tu­tions stay in place. What would you do with it? How would you struc­ture your grants? You’re in charge. You’re the board. You do it.

BOYDEN: Yeah, three thoughts. The first thing that I thought a lot about — study­ing these past cases and then go­ing through it my­self — is think­ing about peer re­view. What is peer re­view?

When you pro­pose a pro­ject, a bunch of your peers will then cri­tique it. The prob­lem that a lot of these dar­ing-sound­ing pro­jects en­counter is that they sound bad dur­ing peer re­view be­cause they’re so off the wall, or they bring to­gether mul­ti­ple fields that maybe no­body’s qual­ified to eval­u­ate them.

One thought is, what if — in­stead of tak­ing peo­ple’s opinions and then just sort of com­bin­ing those opinions, and then, okay, you’re in or you’re out in terms of get­ting the money — what if we take a step back, and we think about why the peers are think­ing this way?

If some­body cri­tiques a pro­posal, but they’re do­ing it from a van­tage point that doesn’t see a cer­tain part of the pro­posal as valuable be­cause they’re miss­ing an un­der­ly­ing piece of knowl­edge, or they’re eval­u­at­ing a pro­posal — based upon opinion — that, if we think about the log­i­cal un­der­pin­nings of it, the ra­tio­nale is ac­tu­ally pretty solid in terms of its be­ing linked to ground-truth­able sci­ences, like physics and chem­istry.

In other words, if we take a step back and ap­ply more log­i­cal prin­ci­ples of eval­u­a­tion to the out­comes of peer re­view, can we ac­tu­ally im­prove the rank­ing of these pro­pos­als? This is some­thing I’m think­ing a lot about right now. As I eval­u­ate peo­ple and eval­u­ate ideas that peo­ple pro­pose to me as well, I’m try­ing to hone those skills in my­self. That’s one of the three things I would do.

[...]The sec­ond thing I would do is to be more dy­namic in my fund­ing. Right now, maybe there’s a grant that you ap­ply for, and then a year later you get the money.

But what if some­body tries some­thing out one Fri­day af­ter­noon, and whoa, that could cure dis­ease, or that could yield an amaz­ing new in­sight into biol­ogy, or that could al­low us to di­ag­nose brain dis­eases early, or what­ever? Why wait a year? What if one could dy­nam­i­cally al­lo­cate fund­ing up and down based upon the real-time met­rics of sci­ence?

In my own group, some­times we get a pro­ject out of the blue, and hey, that’s pretty cool. Then we’ll dy­nam­i­cally try to un­der­stand if we can re­al­lo­cate re­sources. That’s an­other thing I would do.

The third thing I would do is I would go look­ing for trou­ble. I would go look­ing for serendipity. If you look at CRISPR for genome edit­ing — that was found by some sci­en­tists work­ing on yo­gurt. If you look at fluores­cent pro­teins — that was iden­ti­fied by a per­son who just was ob­sessed with jel­lyfish.

In my own field, if you look at our op­to­ge­net­ics work or our ex­pan­sion microscopy work — these fields owe a debt to ba­sic cu­ri­os­ity about crit­ters liv­ing in bod­ies of wa­ter for op­to­ge­net­ics, and ex­pan­sion microscopy goes back to the 1980s where peo­ple were won­der­ing why do cer­tain polymers swell so hugely, with no prac­ti­cal-pur­pose im­pli­ca­tions of it.

One idea is, how do we find the di­a­monds in the rough, the big ideas but they’re kind of hid­den in plain sight? I think we see this a lot. Ma­chine learn­ing, deep learn­ing, is one of the hot top­ics of our time, but a lot of the math was worked out decades ago — back­prop­a­ga­tion, for ex­am­ple, in the 1980s and 1990s. What has changed since then is, no doubt, some im­prove­ments in the math­e­mat­ics, but largely, I think we’d all agree, bet­ter com­pute power and a lot more data.

So how could we find the trea­sure that’s hid­ing in plain sight? One of the ideas is to have sort of a SWAT team of peo­ple who go around look­ing for how to con­nect the dots all day long in these serendipi­tous ways.

COWEN: Does that mean fewer com­mit­tees and more in­di­vi­d­u­als?

BOYDEN: Or maybe in­di­vi­d­u­als that can dy­nam­i­cally bring to­gether com­mit­tees. “Hey, you’re a yo­gurt sci­en­tist that’s cu­ri­ous about this weird CRISPR molecule you just found. Here’s some bioin­for­mat­i­cists who are look­ing to find pat­terns. Here’s some pro­tein en­g­ineers who love — ”

COWEN: But should the eval­u­a­tors be fewer com­mit­tees and more in­di­vi­d­u­als? The peo­ple do­ing the work will always be groups, but com­mit­tees, ar­guably, are more con­ser­va­tive. Should we have peo­ple with more duke­doms and fief­doms? They just hand out money based on what they think?

BOYDEN: A com­mit­tee of peo­ple who have mul­ti­ple non-over­lap­ping do­mains of knowl­edge can be quite pro­duc­tive.

What if I brought to­gether to eval­u­ate a pro­posal, and I have a physi­cist who can tell me, “You know what? That amount of en­ergy won’t kill the brain.” Then I have a biol­o­gist who says, “You know what? That’s a re­ally im­por­tant prob­lem.” And then a chemist who would say, “You know what? That molecule prob­a­bly won’t be toxic.” You ac­tu­ally need a com­mit­tee to judge some of these ideas

Why is Science Slow­ing Down?

COWEN: Is progress in sci­ence slow­ing down right now?

BOYDEN: That’s a good ques­tion. I think what’s hap­pen­ing is we’re tack­ling big­ger prob­lems. Let me ex­plain what that means.

In physics, there’s a small num­ber of build­ing blocks, like pro­tons and elec­trons, and a small num­ber of ways they in­ter­act, like elec­tro­mag­netism and so forth. Chem­istry — there’s more stuff. There’s a hun­dred-odd things in the pe­ri­odic table, al­though maybe there’s only 30 to 50 that you ac­tu­ally have to work with if you’re try­ing to make some­thing ac­tu­ally hap­pen. Again, there’s a small num­ber of bonds: co­va­lent and ionic and so forth.

I think the prob­lem right now is that a lot of the sci­en­tific ques­tions we’re wrestling with, whether it’s in biol­ogy and medicine — but I’m not an ex­pert in this; you know more about some of these things than I do — but in eco­nomics and ed­u­ca­tion and so forth, it also seems like — from my dis­tant view — some of these prob­lems re­late to this idea that there’s a lot of differ­ent build­ing blocks and a lot of ways they in­ter­act.

In biol­ogy, we have what, 30,000 genes in the hu­man genome, and while we know their se­quence, for the most part, we have no idea how these gene prod­ucts in­ter­act with each other, and how they’re ar­chi­tected into cells and tis­sues and or­gans, and how those go wrong. The prob­lem is this cog­ni­trone ex­plo­sion of pos­si­bil­ities is so stag­ger­ingly huge that a lot of what we try will fail.

What do we do about it? One point of view is, “Well, if we had bet­ter tools, and we could map those build­ing blocks and those in­ter­ac­tions, maybe we could re­duce the risk of biomed­i­cal sci­ence.” Again, it’s not my field. You know more about this than I do. I’d love to hear your opinion. But in eco­nomics and in other fields, it also seems like peo­ple are try­ing to make bet­ter maps of things and how they in­ter­act.

That’s one idea. What if we could make these prob­lems . . . Progress might seem to be slower be­cause the prob­lems are so hard. But with bet­ter tools, maybe we can level the play­ing field and make 21st-cen­tury sci­ences more tractable, in the same way that 20th-cen­tury sci­ences gave us lasers and com­put­ers and the in­ter­net.

COWEN: In eco­nomics, we have more good em­piri­cal pa­pers than ever be­fore, but vir­tu­ally no more the­o­ret­i­cal break­throughs, and I’m not sure we’ll ever have them again.

BOYDEN: Oh, how in­ter­est­ing.

COWEN: That may just be diminish­ing re­turns. There are so many fun­da­men­tal ideas, and you learn those, and you stop, and then you mea­sure things.

BOYDEN: Hmm. Well, in biomedicine, sys­tems didn’t evolve to be un­der­stood. They evolved to sur­vive and re­pro­duce and all that. One can hope for struc­ture. Biol­ogy does give you more struc­ture than we de­serve, I think. DNA has a dou­ble he­lix, and you can read out the ge­netic code.

There’s always this ques­tion of why is the uni­verse un­der­stand­able in the first place, and maybe now we’re en­ter­ing the realm of com­plex­ity where things are less un­der­stand­able. But again, we have to ac­cept re­al­ity for what it is.

How to Hire Good Scientists

BOYDEN: …in our group at MIT, I have two PhD stu­dents. Nei­ther finished col­lege, ac­tu­ally. I can’t think of any other neu­ro­science groups on Earth where that’s true.

Later in the in­ter­view.

COWEN: What kind of stu­dents are you likely to hire that your peers would not hire?

BOYDEN: Well, I re­ally try to get to know peo­ple at a deep level over a long pe­riod of time, and then to see how their unique back­ground and in­ter­ests might change the field for the bet­ter.

I have peo­ple in my group who are pro­fes­sional neu­ro­sur­geons, and then, as I men­tioned, I have col­lege dropouts, and I have peo­ple who . . . We re­cently pub­lished a pa­per where we ran the brain ex­pan­sion pro­cess in re­verse. So take the baby di­aper polymer, add wa­ter to ex­pand it, and then you can ba­si­cally laser-print stuff in­side of it, and then col­lapse it down, and you get a piece of nan­otech­nol­ogy.

The co–first au­thor of that pa­per doesn’t have a sci­en­tific lab­o­ra­tory back­ground. He was a pro­fes­sional pho­tog­ra­pher be­fore he joined my group. But we started talk­ing, and it turns out, if you’re a pro­fes­sional pho­tog­ra­pher, you know a lot of very prac­ti­cal chem­istry. It turns out that our big demo — and why the pa­per got so much at­ten­tion — was we made metal nanowires, and the way we did it was us­ing a chem­istry not un­like what you do in pho­tog­ra­phy, which is a silver chem­istry.

I re­ally try to un­der­stand how in­di­vi­d­ual peo­ple and their unique back­ground and in­ter­ests could change the world, but it means that we don’t re­ally have a for­mula. I try not to have for­mu­las, in gen­eral, when it comes to the ac­tual day-to-day of sci­ence. I of­ten say to peo­ple in my group, “We want to rev­olu­tionize the world for the bet­ter and do the right thing and be eth­i­cal, but be­yond that, let’s not try to make any ar­tifi­cial poli­cies.”

How to Find Good Ideas

COWEN: [H]ow do you use dis­cov­er­ies from the past more than other sci­en­tists do?

BOYDEN: One way to think of it is that, if a sci­en­tific topic is re­ally pop­u­lar and ev­ery­body’s do­ing it, then I don’t need to be part of that. What’s the benefit of be­ing the 100,000th per­son work­ing on some­thing?

So I read a lot of old pa­pers. I read a lot of things that might be for­got­ten be­cause I think that there’s a lot of trea­sure hid­ing in plain sight. As we dis­cussed ear­lier, op­to­ge­net­ics and ex­pan­sion microscopy both be­gin from pa­pers from other fields, some of which are quite old and which mostly had been ig­nored by other peo­ple.

I some­times prac­tice what I call failure re­boot­ing. We tried some­thing, or some­body else tried some­thing, and it didn’t work. But you know what? Some­thing hap­pened that made the world differ­ent. Maybe some­body found a new gene. Maybe com­put­ers are faster. Maybe some other dis­cov­ery from left field has changed how we think about things. And you know what? That old failed idea might be ready for prime time.

With op­to­ge­net­ics, peo­ple were try­ing to con­trol brain cells with light go­ing back to 1971. I was ac­tu­ally read­ing some ear­lier pa­pers. There were peo­ple play­ing around with con­trol­ling brain cells with light go­ing back to the 1940s. What is differ­ent? Well, this class of molecules that we put into neu­rons hadn’t been dis­cov­ered yet.

COWEN: The same is true in eco­nomics, I think. Most of be­hav­ioral eco­nomics you find in Adam Smith and Pi­gou, who are cen­turies old.

BOYDEN: Wow. I al­most think search en­g­ines like Google of­ten are try­ing to look at the most pop­u­lar things, and to ad­vance sci­ence, what we al­most need is a search en­g­ine for the most im­por­tant un­pop­u­lar things.

COWEN: Some­times I try do­ing searches. I take the words I want, and then I throw in a ran­dom word that is not re­lated at all, and I try googling that, or through Google Scholar, and I see what comes up.

BOYDEN: Ab­solutely. I do that a lot, too. That’s one thing where I re­ally value those six years I spent learn­ing a bit of chem­istry and a bit of physics and a bit of elec­tri­cal en­g­ineer­ing, be­cause it al­lows me to stitch to­gether some facts from differ­ent fields, and that can be very helpful for launch­ing a new idea or judg­ing whether an idea’s ac­tu­ally worth pur­su­ing.

In Summary

COWEN: Last ques­tion. As a re­searcher, what could and would you do with more money?

BOYDEN: Well, I’m always look­ing for new serendipi­tous things, con­nect­ing the dots be­tween differ­ent fields. Th­ese ideas always seem a bit crazy and are hard to get funded. I see that both in my group but also in many other groups.

I think if I was given a pile of money right now, what I would like to do is to find a way — not just in our group but across many groups — to try to find those un­fund­able pro­jects where, num­ber one, if we think about the logic of it, “Hey, there’s a non-zero chance it could be rev­olu­tion­ary.” Num­ber two, we can re­ally, in a finite amount of time, test the idea. And if it works, we can dy­nam­i­cally al­lo­cate more money to it. But if it doesn’t work, then we can de-al­lo­cate money to it.

If I think about op­to­ge­net­ics or ex­pan­sion microscopy, or these other tech­niques that we’ve been talk­ing about, the amount of money that we ac­tu­ally in­vested in it to get it go­ing was not that much. They were ac­tu­ally fairly in­ex­pen­sive pro­jects.

Then fi­nally, I would like to go out and trea­sure hunt. Let’s look at the old liter­a­ture. Let’s look at peo­ple who might be on the fringes of sci­ence, but they don’t have the right con­nec­tions, like the peo­ple who I talked about ear­lier. They’re not quite in the right place to achieve the rapid scale-up of the pro­ject. But by con­nect­ing the dots be­tween peo­ple and top­ics, you know what? We could de­sign an amaz­ing pro­ject to­gether.