Who's got the guts to go to the moon?

OR: "Look, ma! I'm pretending to cure cancer!"

photo cred: my dad

Everybody’s trying to do a moonshot these days. A moonshot for covid, a moonshot for climate change, a moonshot for brain maps, a moonshot for semiconductors, a moonshot for, uh, teenagers building robots.

People apparently agree that there are big problems in science and we need to shake things up: bring on the breakthroughs! Bold, transformative ideas! Let’s revolutionize science! 

But here’s the thing: despite all these supposed moonshots, nobody has gone to the moon. As far as I can tell, nobody is even aiming at the moon. All this noise about moonshots is, at best, a farce. At worst, it’s a con.

CURING CANCER REQUIRES YOUR WHOLE ASS

Take, for instance, the NIH Cancer Moonshot¹. It was originally funded with $1.8 billion over seven years, and it continues to pull down hundreds of millions every year. The organizers assure us that “remarkable progress and notable scientific accomplishments have been made” in that time.

So what did those billions buy us? A new cancer vaccine? Chemotherapy drugs that don’t make your hair fall out? A way to screen for prostate cancer that doesn’t require someone to stick their finger up your butt?²

No, none of that. Instead, the Cancer Moonshot has been:

• “working to build the evidence base on multilevel interventions to increase rates of colorectal cancer screening”

• refining “electronic medical records and clinical workflows to ensure routine delivery of evidence-based tobacco cessation treatment services”

• doing research that “suggested that some children with B-cell acute lymphoblastic leukemia that recurs or resists treatment may benefit from certain immunotherapy drugs”³

Discovering that some kids might benefit from some drugs is, I guess, better than setting the research money on fire. But this ain’t a moonshot. It’s so far from a moonshot that it needs a different name. Earthshot? Groundshot? How about, “normal research”?

If there had been a webpage monitoring the progress of the actual moonshot in the 1960s, it would have said stuff like “we built a rocket” and “we figured out how to get the landing module back to the ship.” In 1969, it would have just said, “hello, we landed on the moon.” It would not have said, “we are working to establish the evidence base on multilevel interventions to increase the rates of moon landings.”

Maybe curing cancer in the 2020s is way harder than going to the moon in the 1960s. I have no idea. But it doesn’t sound like we’re even trying to cure cancer.

Here’s a dead giveaway: one of the first things the NIH touts about its Moonshot is that it has published over 2,000 papers. I’ve been in this game long enough to know that when a scientist actually has something important to tell you, they tell you about what they did, not what they published. Besides, how many more papers do we need before we cure cancer? Another 2,000? Another 10,000? “I’m so sorry to inform you that you have colon cancer, but the good news is that if you give us your data, we can use it in a Nature paper.”

There’s a useful adage here: “Institutions will try to preserve the problem to which they are the solution.” I don’t think anyone involved in the Cancer Moonshot literally wants cancer to exist forever. But they all seem to assume that it will, and that the process of curing it will go on indefinitely, and they should all be well-funded in the meantime.

To be clear, I much prefer that the government drop billions on half-assed cancer research than, say, cruise missiles. At least half-assed cancer research sometimes makes progress on cancer, even if it’s by accident. But cancer kills about 10 million people every year, so we’re gonna need to put our whole asses into this one.

BOLDLY GOING WHERE MANY PEOPLE HAVE GONE BEFORE

This seems to happen every time somebody claims they’re going to fund “high-risk” research.

Here’s another example. The National Science Foundation gives out “Early Concept Grants for Exploratory Research” (EAGER) that are supposed to support “high risk-high payoff” work that “involves radically different approaches, applies new expertise, or engages novel disciplinary or interdisciplinary perspectives.” These are some projects they’ve funded:

• Studying how to recycle lithium-ion batteries

• Creating a network of people who study disasters

• Figuring out whether scientists are sharing their data

Likewise, the NIH gives out a Pioneer Award to “highly innovative researchers at any career stage who propose bold research projects with unusually broad scientific impact.” Here’s what the most recent winners are up to:

• Studying clinical information systems

• Trying to figure out which neural circuits generate “pain, touch, and body schema perceptions, and sensorimotor behaviors”

• Using computational methods to study decision-making

These projects might be great, they might be important, but they are not even close to “bold” or “radically different.” This is normal research, indistinguishable from the stuff the NSF and NIH fund through their regular channels. Seven of the eight Pioneer Award recipients are affiliated with super-elite universities. Three of them are at Stanford alone! The NIH was like, “let’s do something so crazy that those uptight muckity-mucks at HQ would never go for it” and they came up with, “let’s mail some checks to Stanford.”

(Perhaps they should have called their program “Normal Operational Research Money for the Already Loaded [NORMAL]).

It’s obvious that the NIH never intended to fund anything other than normal research. They admitted as much when they first described the Pioneer Award:

Part of the High-Risk, High-Reward Research program, the award supports scientists with outstanding records of creativity [emphasis in original]

I gotta laugh at that because otherwise I’d cry. Kudos to the NIH for taking the bold step of supporting people who have outstanding records.

(By the way, grants like these comprise 0.15% of the NIH external funding budget. So 99.85% of the budget is going to projects that are even lower risk than this.)

If that’s what you consider “high-risk,” then I’m excited to introduce you to the Experimental History High-Risk Investment Fund: for a nominal fee, I will accept cash from you and use it to purchase US Treasury bonds.

MY BODY IS A MACHINE THAT TURNS MONEY INTO PAPERS

Clearly, this “high-risk” thing hasn’t panned out. We need a different strategy here.

We can start by admitting that most research is already “high-risk”, in the sense that it’s very unlikely to amount to anything. It’s just people playing the Science Game, doing Mad Libs in the lab.

You know those kids who stuff their résumés so they can get into good schools? Some of them grow up to be Principal Investigators, stuffing their CVs so they can get grants. These are the same people who think that turning $1.8 billion into 2,000 journal articles is a cause for celebration, rather than a national embarrassment. It is indeed risky to hand a million bucks to a person like that, because they’re probably not going to do anything useful with it.

The real problem with science is not the lack of riskiness; it’s the lack of seriousness. The first question we should ask isn’t “How likely is this project to fail?” but “Does this person believe in truth and seek it sincerely? Are they going to produce papers, or are they going to produce knowledge?” If the prerequisite for getting on the grant review committee is “you’ve produced a lot of papers,” good luck with this one.

There is, however, a different kind of risk that nobody seems willing to take: reputational risk. As in, how much will people make fun of you for funding this idea, especially if it doesn’t work? 

Sending checks to Stanford carries zero reputational risk. If they use your money to produce fake papers, nobody will judge you for it—all you did was trust the experts. But if you send a check to some no-name weirdos and they blow it on a bizarro project that goes nowhere, everybody will blame you for not sending it to Stanford instead.

The goal isn’t to maximize reputational risk; the goal is to ignore it. Some good ideas look like good ideas, and everyone will cheer when you pick them. But some good ideas look like bad ideas, and everyone will boo when you pick them. Courage is picking the good ideas regardless of whether people are cheering or booing.

Amidst all these scientific agencies and organizations throwing around billions of dollars, I don’t see anybody taking on even a smidge of reputational risk. That means there’s a huge opportunity here. If you’ve got the cash, taste, and guts necessary to find and fund stupid-looking-but-good ideas, you have zero competitors. As a guy who used to teach at a business school, I can tell you: that’s the optimal number of competitors.

THE PARABLE OF THE BULGING NECKS

Let me show you the kinds of low-hanging fruit waiting out there for anyone willing risk embarrassment. Alarmingly often, this is how breakthroughs happen:

1. A weirdo/outsider proposes some new idea

2. Experts and authorities ignore or suppress it because it seems stupid. This can go on for a long time.

3. Eventually the new idea wins out because it’s better.

#2 is where the money is waiting to be made. If you’ve got a good eye for ideas and you’re brave enough to tiptoe a bit outside the mainstream consensus, you can make a breakthrough decades or centuries earlier than it would have happened otherwise.

For example, people used to get giant bulges on their necks (“goiters”), and no one knew why.⁴ It was particularly bad in Switzerland. In the 1800s, there were some Swiss towns where pretty much everyone had a goiter, not to mention crazy high rates of what we used to call “cretinism”—children born with profound developmental disabilities.

At the beginning of the 1900s, the two leading theories for Goitergeddon were “there’s some bad microbes in Switzerland” and “Swiss people are undergoing racial degeneration.” When a rural doctor named Heinrich Henziger was like, “Maybe it’s caused by a lack of iodine,” the medical authorities shouted him down. One leading expert published a piece in the main Swiss medical journal saying the iodine deficiency theory “must be vigorously opposed.” 

This was, in fact, at least the fifth time in 50 years that someone put this theory forward, and the same thing had happened every time. The Most High Very Esteemed Experts pooh-poohed it, and it never went anywhere. The thing that causes goiter is indeed a lack of iodine, but the thing that prevented goiter from being cured was a lack of courage.

Luckily, this time around, another rural GP named Otto Bayard gave iodine to some of his goiter patients, which completely cured them. Despite vigorous opposition, this eventually snowballed into an international effort to add iodine to salt, and that’s why almost no one gets goiters anymore. If a brave billionaire or a thick-skinned government agency had been willing to take a flier on a low-status idea, we could have cured the horrible neck bulges half a century earlier.

Anybody who wants to revolutionize science, then, should be looking for the Henzigers and the Bayards. They’re hard to find because they don’t work at Stanford University, they don’t look good on applications, and they often sound ridiculous: “Hi, I’m Henrich Henziger, and I’m a doctor from the middle of nowhere. I think all of the experts are wrong about goiter. I’m the only one who knows how to cure it. Could I have some money please?”

Governments struggle to do this because governing requires consensus-building, while revolutionary science requires consensus-breaking.⁵ Private foundations struggle to do it because—as I’ve heard from people who work for them—even when their stated goal is “change the world,” their actual goal is often, “make our billionaire donor look good.” 

But we know it’s possible, because both private organizations and public agencies have found it within themselves to do the right thing long before it looked like a good idea. The Rockefeller Foundation supported almost every molecular biologist who won a Nobel Prize between 1954 and 1965, and they did it, on average, 19 years before the prize was won. They didn’t fund the hot thing; they made it hot.

The government can do the same thing. The original moonshot wasn’t popular. People very reasonably wondered why the government was launching dudes into space when there were so many problems back on Earth.⁶ The public only started to warm up to the idea decades later. So you can only call something a moonshot if what you really mean is, “we’re attempting to do something important that won’t be appreciated until years after we accomplish it.”

The Bene Gesserit would make great NIH program directors.

THE KARIKÓ TEST

I’ve got a test for all the aspiring moonshotters out there.

Katalin Karikó recently won a Nobel Prize for her work on mRNA vaccines, which saved millions of lives. Before that, however, she was barely staying afloat in academia. She had trouble getting grants, and her papers didn’t make a splash. Her bosses at the University of Pennsylvania denied her promotions and restricted her access to lab space and supplies, describing her at one point as “not of faculty quality.” Now they’re all singin’ a different tune, not least because the technology she patented has since earned UPenn more than a billion dollars.

So here’s the test: whatever “high-risk high-reward” program you’re running, would it have funded Karikó before she got famous? Do you have the courage and insight it takes to see someone’s potential when they aren’t legibly successful yet? If so, hats off to you. If not, you’re not doing a moonshot. You’re just doing normal science in a futuristic font.

Unfortunately, spotting Karikó is as easy as it gets. Funding her 20 years ago was, at most, medium-risk. She was still a professor at an Ivy League university, and nobody thought she was crazy. They just didn’t think her work was going to end up stopping a global pandemic. So passing the Karikó Test is a bit like passing the Bechdel Test: you’ve only cleared the lowest bar.

That said, it’s okay to fail the Karikó Test, as long as you’re honest about it. Normal science needs love too. “Incremental” sounds pejorative, even though it describes basically all research done inside traditional institutions. That’s too bad. If you’re doing serious work and you actually decrease cancer deaths by 3%, that’s a lot of lives saved. It’s just that, if you call 3% “revolutionary,” you’re going to crowd out the actual revolutionaries who are gunning for a 100% reduction in cancer deaths.

THINGS YOU CAN DO

All right, enough criticism! Time to incur some reputational risk myself. Here are three ideas that I think would make for true moonshots. 

1. Endow scientists for life.

Most scientists say they would spend their grant dollars differently if they could, and some of the most important discoveries have come from researchers who were allowed to screw around. People have noticed this, and now there’s a widespread feeling that we should “fund people, not projects.”

I say: that’s a great idea, so let’s actually do it. Fund a few scientists for the rest of their lives, no strings attached. Drop $5 million in a scientific trust fund for each individual, pay them out the ~$200,000 in interest every year, and let them do whatever they want with it.

A program like that could create a new era of gentleman scientists—you know, the ones who got us evolution, chemistry, microbiology, etc.—except they wouldn’t have to be gentle or men. The problem with our previous crop of gentlemen scientists, of course, was that the vocation was only open to people who had been born wealthy because, say, their grandpa sold a lot of guns. We can do a lot better at picking researchers than simply waiting for arms dealers to produce offspring.

(See also: trust windfalls.)

2. Build a new scientific ecosystem.

It’s not just Karikó—lots of Nobel laureates say things like “I could never survive in academia today.” People have proposed lots of tweaks to make things more hospitable to our most promising scientists, but it’s a little bit like watching that scene in Indiana Jones and the Last Crusade where Harrison Ford has to get past a bunch of booby traps to get the Holy Grail, and then your takeaway is, “Oh, those booby traps are bad, we should have 10% fewer of them.”

I support de-booby-trapping academia, but a better route is to build new places that don’t have any trap doors or poison darts at all. Not an appendix to an existing institution, not a retirement home for scholars who have achieved mainstream success, not a place where academics can hang out for a while before they go back to running from giant boulders—a completely separate space that works on different principles and supports an entirely different species of scientist.

This has to start with building new on-ramps for young folk who want to learn how to do basic research. Naturally, I think Science Houses would be a good way to do this, but if someone came along and was like “I’m going to build lots of new scientific training institutions outside of academia, but I will never use any of your ideas!!” I’d be like “That seems vindictive, but ok!!”

3. Run the actually good study (RTAGS).

If those are too extreme for your taste, here’s an idea for moonshots that stick a bit closer to home.

Meta-analyses come out all the time that are like, “Unfortunately, all of the studies that try to answer this important question are so bad that we can’t learn anything from them.” Instead of running another 500 piddling, confounded little studies, someone with guts, taste, and money could run the actually good study.

For instance: 

• Does flossing work? “The evidence is low to very low-certainty.” You could randomly assign a big group of people to floss or not, or tell everybody to floss half of their teeth, and see whether dentists can tell the difference. 

• Does sunscreen prevent skin cancer? “The certainty of the evidence was low.” You could randomly assign a big group of people to wear different kinds of sunscreen, or none at all, and follow them for the decades that it would take for any differences to show up. 

• Does wearing masks slow the spread of respiratory viruses? “Our confidence in these results is generally low to moderate.” You could settle this once and for all by renting a bunch of cruise ships, sending volunteers on a free cruise, flooding the boats with cold virus, and randomizing some of the ships to wear masks while others go about their business as usual. (You should explain this to people before they get on the boats, of course.)

These would be less sexy than the Moon Moonshot, but only a couple of humans have ever been to the moon, while almost all of them have teeth, skin, and respiratory tracts—and perhaps more of them would if they flossed, wore sunscreen, and used masks. We just don’t know!

I hesitate to offer these ideas because the quality of the idea itself matters a lot less than the quality of the people doing it. Selection effects are far more powerful than incentives, and that’s why taste matters so much. But if you’re really trying to shake things up, you should be aiming at least this high, and hopefully higher.

Otherwise, you might as well just write a check to the NIH, and they will happily put it toward their Stanford Moonshot Program, a revolutionary new initiative where they send checks to Stanford.

1. The NIH Cancer Moonshot is not to be confused with the Biden Cancer Initiative, which was a short-lived nonprofit, nor the Cancer Moonshot 2020, which appears to have been a scam to sell one guy’s tumor diagnosis machine.

2. Seriously, I would love it if the NIH website on prostate cancer screening did not include this image:

3. Notice how these “significant achievements” fail the experimental history test: when you describe them as people doing things, they sound way less impressive. “We’re trying to get people to do more colon cancer screenings.” That’s all good, but it’s not gonna get you to the moon.

4. For this section, I am relying on Jonah Goodman’s terrific article about the discovery of iodine supplementation. I recommend reading it in full; it’s a great case study on how breakthroughs are often illegible at first.

5. Apparently DARPA solves this problem by keeping their research classified in the name of “national defense.”

“Why is DARPA giving cocaine to Japanese quails and then videotaping them having sex?”

“Sorry sir, that’s classified.”

That’s great for DARPA, but giving the military industrial complex carte blanche to do experiments has some extremely predictable downsides for the rest of us. For instance, in 1950, the US military decided to spray bacteria all over San Francisco to, uh, see how vulnerable San Francisco was to being sprayed all over by bacteria. (Answer: very.) This may have permanently changed the bacterial ecology of the Bay Area and might have killed a few people. The military didn’t tell anyone (“Why are you spraying bacteria all over San Francisco?” “Sorry sir, that’s classified.”) and so this harebrained scheme wasn’t even revealed to the public until 20 years later.

6. As the poet Gil Scott-Heron put it:

A rat done bit my sister Nell.
(with Whitey on the Moon)
Her face and arms began to swell.
(and Whitey’s on the Moon)
I can’t pay no doctor bill.
(but Whitey’s on the Moon)
Ten years from now I’ll be paying still.
(while Whitey’s on the Moon)