In the science policy world a term often heard is "high-risk, high-reward" activities; funding initiatives, projects, or researchers that individually are likely to fail but that also hold potential for truly radical, breakthrough discoveries. But what about "low-risk, high-reward", wouldn't that be nice?

One more of Stripe Press' beautifully edited tomes, Scientific Freedom: the elixir of civilization, is Donald Braben's theoretical case for the existence of such scientific opportunities as well an account of his own experience running a funding program—Venture Research (VR)— that proves that the author is not merely cheap-talking us. I won't go into the details of how VR came to be, focusing instead on the theory and discussing a few examples of projects they funded.

The book itself fits the adage that most books should be blogposts; while insightful, a lot of the content could have substantially compressed, with the exception of the final chapter that details individual Venture Researchers' (VRs) projects. Hence if you have not read the book you can get an idea by reading this RAND report followed by these slides from Braben himself and you'll get the gist of it unless you need to compulsively collect all of Stripe Press' big beautiful books.

So what does the book say?

  1. The number of researchers that are doing truly groundbreaking research is small, akin to a club.
    1. An historical example is the varied set of scientists the author dubs the Plank Club (Planck, Einstein, Brenner, Bohr, or McClintock to name some)
    2. Braben puts the number at around 300 truly innovative researchers in the 20th century, with everyone else doing just incremental work
  2. This groundbreaking research requires a specific environment to enable it, affording researchers freedom to research as they wish without any mandate, for a prolonged (multi-year) period of time, with little accountability
    1. For example Peter Higgs thinks he would be unhireable under the current system, Wilczek and Philip Ball consider that perhaps Einstein would be as well, and so does David Deutsch about himself.
    2. In the book itself a few more examples are given, Sydney Brenner, a pioneer in molecular biology remarked on his Nobel Prize address: Such longterm research could not be done today, when everybody is intent only on assured short term results and nobody is willing to gamble. Innovation comes only from the assault on the unknown.
  3. Such environment has been lost with the rise of the modern post-WWII research system (Or post 1970s?), characterized by the massification of the research enterprise, and the publish-or-perish culture
    1. Or, as the author would put it, the current system would fail the "Planck test": it would reject Max Planck et al.
  4. That has led to a slowdown in scientific progress since the 1970s
  5. This scenario leaves literal trillion-dollar bills on the sidewalks of science, because with just an open-ended grant for a handful of handpicked members of a hypothetical Planck Club V2 one could restore the pre-1970s conditions and allow the stream of knowledge to gush forth once again
  6. The experience of Venture Research (VR) is a practical demonstration that this is indeed true: A private funder with a small amount of resources can achieve outsized knowledge returns; perhaps even financial returns as well.

Venture Research itself as a funding initiative was targeted at successful researchers, or researchers that were proposing research with the potential of altering the field they were working on, or even creating new fields altogether. Hence in Chapter 7 of the book we find that some of the VRs had Nobel prizes to begin with, or were widely praised professors like Edsger Dijkstra. Some of the questions that were asked to VRs when deciding whether to fund them:

  • If you had infinite resources and freedom what would you do that you are not doing now?
  • Might the proposed research radically change perceptions?
  • Might your research be recommended for a Nobel prize?

These are not quite the same questions that NIH R01 grantees get!

Braben doesn't like peer review (And I'm of the same view), but given that there is a need for a mechanism to allocate funding among competing proposals, he had to choose something, and he chose Braben-review. Some formalities aside, he seems to have had ample discretion to allocate the grants, in a way similar to the role played by Tyler Cowen in the Emergent Ventures grants. The reason this might work could be that due to his lack of deep domain expertise (He knows in depth just about his own field, and that's good to avoid consensus thinking) and lack of conflict of interest (He is not a potential recipient, nor he stands to lose relative status if the grantee is successful, unlike a peer who is also a competitor of the researcher under consideration). To be sure, this mechanism can introduce false positives as well; a potential case might be Stan Clough and Tony Horsewill's 1989-1992 research project (p. 171) that Braben as of 2007 points to as a "significant milestone if not a revolution in the development of physics". Suffice to say, their work remains relatively unknown over a decade after and I couldn't find much about it other than this blog (With basic research one can always say that it will take time for it to be acknowledged, but it has been a few years already). Nonetheless it can be argued that the more stagnant a field is—and fundamental physics definitely is—the more interest there should be in finding wild weird works of science, in the hope of tilting the balance of the field away from exploiting arid research grounds and towards exploring alternatives; it is in this category where I also put Quantized Inertia and the various warp drive proposals as I mention in the link above; both are generally opposed by the physics community as clearly wrongheaded. They are the exception though, most of the proposals described in the final chapter of the book seem to have gone somewhere.

[1]. Braben says most of it was successful, but one'd need an impartial careful assessment to truly believe that

Whether VR is "low-risk, high-reward" research depends on what comparison group is, and what would count as success1 or fail. If you take, say, Y Combinator, how much risk are they taking? Eyeballing it, the failure rate of the earlier cohorts may be 50%. Is that high risk? Low risk? In any case, the VR model does show that funding proposals that everyone else had rejected (Braben explicitly acknowledges that playing the role of funder of last resort is something they explicitly aimed for) in general can lead in successful research.

Regarding the decline of science in general, the book is scant in quantitative evidence and rich in anecdote. The belief that science is in crisis comes and goes; Charles Babbage wrote back in 1830 on this same question thinking back then there was a decline. Assessing whether Babbage was right and to what extent, or if Braben is right and to what extent (And if so, what exactly were the changes that led to science to go into decline, then revival, and then decline again) is a complex enterprise that personally interests me and I was hoping to learn something new here but I did not.

Throughout the book there are some interesting discussions of specific cases of substantial discoveries that took over two decades to accomplish, one of them Perutz's determination of the structure of hemoglobin. Achievements that take that long makes one wonder why; was it just slow toil in one direction? Lots of false starts? If you take this particular case, it seems to have been lack of good tooling, which had to be built over time (for protein crystallography).

That would be an interesting thing to do in the future: Look at projects that took a long time and figure out why (And if they could have taken less time)

Where are the breakthroughs and great scientists

As I was reading through the book, I noted that while I had heard of most of the members of the Planck Club (Sorry, Charles H Townes) I had heard of none of the VRs with the exception of Dijkstra (And even then the award was not for the man himself, but for his friend and student Netty van Gasteren).

It would be unfair to say VR failed because it didn't produce a name as recognizable as Einstein's, but the fact that I couldn't recognize any of the names prompted me think that a reason why that might be is the same reason you don't know who most of the newer Nobel Prizewinners are, or why you can't think of an immediate answer to "Who is the living successor of Darwin".

The answer is that the great ideas and breakthroughs are here, it's just that they are evenly distributed, to paraphrase William Gibson. What used to be large, easily recognizable steps a single researcher could take (As in Einstein's relativity, with due credit to Poincaré, Lorentz, and others), now has been salami-sliced among an increasing number of researchers; even the Higgs Boson is, in some sense, a shorthand for the Englert–Brout–Higgs–Guralnik–Hagen–Kibble boson, not Peter Higgs's sole theorising.

Why scientific freedom

Scientific freedom is necessary for the same reason economic rights (the right to start a business, organize it in arbitrary ways) are necessary: because what is going to be successful is not always obvious to the incumbents, and so the challengers have to be able to circumvent them. This is a matter of degree: The current landscape of scientific funding also has space for fringe science: Mike McCulloch got funding from DARPA, until recently Harold White was employed at NASA, Salvatore Cezar Pais is employed by the US Navy. Judgment of thoughts not our own often comes via heuristics, where if something sounds obviously false to us we don't bother spending a lot of time trying to grapple with it, as we expect the time spent won't make up for a tiny expected probability of it being right. Think of homeopathy.

On the other hand, the other end of the spectrum (mission-oriented research, industrial research, or FROs) is necessary as well. Science can't just be making discoveries, those discoveries should also be put to good use and it can often be the case that the basic research has been done but no one has stepped in to collect bits of it and cobble together a new invention. Or it can also be that engineering work is required to enable that basic research to begin with.

In this context, Braben is to be understood as saying that we are doing too little of the former, so little that even marginal increases can still be impactful. I don't know if he goes as far as saying that all science should be free.

The Planck Club

The book suggests that only a handful of the total number of scientists mattering for opening up new fields and challenging dogmas. How should they be identified? From the book, a clear way is considering someone part of the club if they have won a Nobel or some similar field-specific high prestige award. You could them give them a nice salary for life and free them from any explicit duties. It's not fully clear what one will get out of this though, because yes in theory this can enable those Planck Club members that have already proven their genius to pursue then other projects without having to explain why, and at least one of the VRs follows this pattern, Nobelist Dudley Herschbach. But not every scientist post-Nobel Prize does interesting research, or research at all. Peter Higgs famously has not published anything after his 2013 Nobel. It could well be that he is slow-cooking some stunning results, or that it is unfair to demand that (more publications) of him (He's 91 years old), but it could also be that Nobel status (Who would fire him?) and the associated reduced pressure to think and publish means reduced, or in this case null, output.

A general form of this argument would be the standard critique against scientific freedom: That scientists will grow lazy without someone keeping them accountable. Ultimately it is an empirical question, and one that I expect will yield results along the lines of: Yes, for many, perhaps most scientists this is true. But not for Planck Club members. A true genius is internally motivated and will continue to work as long as they have the resources and faculties to do so. Or so seems to be the case from my reading of Genius: The Natural History of Creativity.

But limiting funding to those already successful would fail the Planck test. How could we have spotted Einstein while he was at the patent office? Braben is also aware of this and VR awarded grants to younger researchers as well, going off their enthusiasm for the science and Braben's own individual judgement. Some details of the process they used:

[2]. Though I don't know to what extent this was true, or how practical it would be. I can imagine the application examiners being overwhelmed by cranks that really want to have their crackpottery funded and relentlessly try to engage them
[3]. Braben says they did had some peer review, but in a comically diminished way: “However, even Venture Research was not entirely free of peer review ’ s clutches. Such is its all - pervasive power that our BP board could not bring itself to forgo it, and we were obliged to find a form that would satisfy us all. The solution was to split the problem into two; we would first make up our own minds, but before we took our recommendation to the board we would approach a single peer selected by the researcher as being the most important person likely to be supportive. We then fully briefed that person, both verbally and in writing, and did what we could to persuade him or her to endorse our decision. However, even this farcical, vestigial form of peer review often failed to produce the support we requested. In every case, we were able to persuade the board to go ahead anyway.”
  • They strive to be "Nature's Ambassadors" and "apply the same criteria that Nature herself might have imagined to use in today's circumstances", which means being as objective as possible or so I gather.
  • The applicant needs to require that long term freedom and must be aiming for truly new science, not mere incrementalism.
  • Applicants always get a response, they can keep insisting until they give up. 2
  • Once applicants have passes the first filter, they are invited for open ended discussions that "foster mutual trust", "encourage a spirit of adventure" or "focus exclusively on concepts". Braben and team may also tour the scientist's lab.
  • It then goes to a panel of "VIP scientists" from various disciplines. Braben and his team and the experts meet to make the final decision. 3

This still looks kind of arbitrary, ultimately the core criterion is "Is Braben impressed?". Who could or could not play that role? For example, you could come up with the following ideas for funding scientists:

  • Hire your reviewers (Your "Brabens", not peer reviewers) among Nobelists. Maybe even have 3 of them and as long as one approves of the proposal, it goes forward, or
  • random retired professors, or
  • researchers that have published across field lines, or
  • researchers whose discoveries have only proven useful decades later, or
  • people that score in a certain way in some standardized tests, or
  • generally interesting individuals

And you could mix and match plausibly. Say you take a Nobel Prize in Chemistry winner, one particle physicist who is also a UFO conspiracy theorist, a PhD student doing research on distributed systems, and for good measure your favorite blogger. You have them all review each proposal, and you have some mechanism to decide what goes or not. Would this work better (As a team) or would it be better to have this group working separately, each having final authority?

Or we could also ask instead: Who should not be awarding these grants? Maybe someone who works in the same field (On the premise that they will be too steeped in the current paradigm), but they could be retained for advice. Someone who does not have at least a level of understanding of the relevant field and is not curious enough to learn more as needed would be excluded as well.

Make Science Great Again!

I've tweeted about the idea of efficient nepotism, this is when you can make decisions that affect people (hiring or funding say) without any formal process, using your personal tacit knowledge about the individual to make the decision, bypassing cumbersome red tape and the opinions of those who know less: The HR-person instead of the HR-department. Science used to be like this and Braben is proposing a return to this mode of allocating human and financial capital.

The book makes a good case for at least a second trial at a Venture Research-type of funding mechanism, and leaves us with a few interesting questions:

  1. How to pick the individual or team that will do the funding? Is it efficient nepotism all the way up the best way?
  2. Should there be a built-in bias towards certain fields that should or should not get funding?
  3. How do youth and prestige play together as predictors of future accomplishment?
  4. How should we think about funding individuals vs funding teams?