Acknowledgements: written with feedback from Daniel Goodwin, Stuart Buck, Adam Mastroianni, Mark Hammond and Isabel Kepson

Only variety can absorb variety. – W. Ross Ashby

On April 17, 2013 a 55 year old “part-time calculus teacher at the University of New Hampshire” submitted a proof that transformed number theory. With only one paper published (12 years prior and another posted on arxiv which he himself recognises contained fatal mistakes) it’s extremely hard to imagine how Yitang Zhang would have ever convinced a research funder to take seriously the prospect of his success in solving the problem, which had stood until that point for 150 years.

Zhang’s primary innovation was in the design of a ‘sieve’ for finding prime numbers less selectively. This article is in turn about the 'sieve' used to identify radical thinkers prior to undertaking their most important work. In Zhang's case, our selection principles for funding would have undoubtedly failed, with peer review fortunately catching his monumental contribution. While earlier support might not have changed the outcome in Zhang’s specific case (we might go so far as to say Zhang’s ideas only came to fruition because he didn't require substantial funding to explore them), it is this precise fact that meant his example came to light where innumerable others could not and therefore can act as a leading indicator of a universe of neglected thinkers.

In much the same way that Zhang found a way to make his sieve less selective, if we take seriously the idea that science is a strong link problem, i.e. that “overall quality depends on how good the best stuff is, and the bad stuff barely matters,” then we too must find innovative ways to reduce the selectivity of research funding and acceptance into specific programmes. One way of doing this is to stimulate and build a new, diverse class of scientific institutions designed specifically for the purpose of testing different principles for identifying and backing outliers. I call these organisations “unshackled research organisations”. The idea is deceptively simple - by varying selection criteria for researchers and research projects, we can encourage a greater variety of research angles and so increase our understanding of the world more quickly. It is not my idea, it is an idea championed by many, but the people who have been most influential on my becoming obssessed with this idea are Adam Mastroianni, Michael Nielsen and Stuart Buck.

My motivation for exploring this question comes from visceral experience of the vicious cycle of absent conviction that exists early in the lifecycle of every radical idea: before there is sufficient momentum or evidence to justify a PhD research project (or even a PhD sidequest), or $40m to form an FRO, or $100m+ to start a Lovelace Lab there exists a moment where the idea is a just a question, the ideator themself uncertain or unproven, with little evidence in support and therefore very little reason to spend resources answering that question. The more radical the idea, the higher the esteem of the target, the higher the burden of proof.

In retrospect, once the idea has broken through, we always realise that whilst there were excellent reasons for ignoring this idea, there were also excellent reasons for taking it seriously. As long as the excellent reasons to ignore dominate funding decisions, then we continue to fail to treat science as a strong link problem.

Unshackled research organisations are therefore research organisations that aim to break the vicious cycle of absent conviction by loosening their selection filter in some critical way and as such have two key ‘success’ criteria, primarily, that they a) select outliers more often than inliers and b) have a differentiated and specific definition of what is ‘important’ in assessing the impact of research. They ignore some excellent reasons for rejecting ideas, whilst emphasising others.

Without a (targeting outliers), they are not measurably unshackled, without b (a philosophy of importance), they are not just unshackled but potentially entirely pointless. Unshackled research organisations are differently selective, rather than unselective. They have a specific philosophy of importance rather than resorting to vagaries such as ‘curiosity-driven’ or ‘unfettered’ research. They are research organisations that have achieved escape velocity and broken free of the regression to the mean in ways that make them discernibly and sustainably distinct. They are therefore profoundly unlikely to be places where you are pushed to publish or patent (or perish). They are also (therefore) unlikely to be places where you would necessarily go to progress in your academic career (though you may nevertheless perish there). It seems less likely that unshackled research organisations will be places run with top down hierarchies or that resort to ‘original thought by committee’. I suspect most unshackled research organisations would be environments inimical to an imperial group-building campaign backed by a legion of 100 post docs.

Unshackled research organisations must therefore go beyond a philosophy of “people not projects”, lotteries or faster grants if they would have some prospect of truly starting to uncover effective principles for detecting important work that has as of yet not been completed. Whilst those fulfil a (they loosen the filter), they miss b (they have no philosophy of importance, or rather, what to focus on instead). These organisations must be able to withstand a variety of outcomes and to eliminate the procedural obstacles that have lead to some of the greatest thinkers in history having been disregarded for so long.

So in our endeavour to loosen the filter, to be ‘differently selective’ and to enrich the population of research supported with a greater population of outliers, what are some of the reasons why great thinkers have been incorrectly filtered out? I have not attempted a comprehensive survey, but have listed a few possible ‘blindspots’ candidates new models might consider altering their selection criteria so as to capture:

• Illegible idea - Work of this kind does not fit into existing departments or research-funding agendas or strategies, perhaps because it constitutes a new field, focuses on a new class of phenomena or because it revives an older research question that many consider ‘closed’. Similarly, at the other end of the ‘idea maturity scale, an idea may suffer from nebulosity - we might not know what the focus of the research is or should be yet or where it ‘fits’ or how to describe it
• Illegible communication - Thinkers who communicate in ways that are at odds with the style, modality or language of funders or research departments - for example, publishing in blogs or twitter instead of in peer-reviewed papers, using github when funders are not software-literate, creating many of their own terms or words or using terms or words unfamiliar in the domain of research funders (for example, borrowed from social sciences, philosophy or from historic texts). Venture Capital investors are notorious for requiring that communicators conform to a specific format in how they tell their ‘story’, this being predictive of their ability to persuade the set of VCs at the next round (and so continue to secure funding - usually a pre-requisite for success for a VC-backed business at any stage)
• Undercredentialed - Thinkers who are insufficiently or differently credentialed or have been wrong in the past - examples abound particularly of female scientists through history ignored by male contemporaries, for example, the omission of Jocelyn Bell Burnell from the 1974 Nobel Prize for the discovery of radio pulsars, justified by her status as a student at the time (the prize was given to two of her male colleagues) - just one example of the systematic under-recognition of women in science that has sometimes been referred to as ‘the Mathilda Effect’. Yitang Zhang was almost discounted because a past paper he’d posted was incorrect. For my part, whilst working at Imperial College running an entrepreneurship competition I was told by one department head not to bother with the undergraduates and PhD students because “they don’t have important ideas”. This is one of the reasons why we started our own PhD programme, which puts students back into the driving seat to determine the course of their own research
• Illegible credentials - Anecdotally this applies to scientists applying to work on questions in disciplines other the one they’ve previously published in. I once met a game theorist who had a theory as to how certain cancer cells might be modified to outcompete their neighbours who could not get even a small grant to explore the concept. Another recent example recently shared with me is of a highly accomplished and extremely well-regarded scientist at an elite research institution attempting to understand learning in different organisms who had his grant application rejected because he had not previously published on the specific organism he wanted to explore the hypothesis in
• Useless - The importance of the idea is not identified until its utility is revealed by something which later requires this knowledge. Bayes Theorem is a great example of this - we have only in the last few decades had the computational capability to make productive use of the theorem to model scenarios of sufficient sophistication to be interesting. Another great example is Gregor Mendel who spent 20 years in obscurity and died before the utility or importance of genetics was ever truly brought to light by de Vries, Correns and von Tschermak in the early 20th century
• Useful but not understood - There’s a key explanatory component missing in connecting some observation with the phenomenon being described. An example of this is Semmelweis, who discovered the importance of hand-washing in preventing childbed fever in the mid-19th century - the observation alone, without ‘germ theory’ as developed by Pasteur and others, was insufficient to garner traction for the practice
• Constrained - There’s a well-known reason why this won’t work - a ‘hard constraint’ - for Karikó - this was the body’s possible immune system to synthetic mRNA, not the importance of mRNA itself. But even armed with supporting evidence that this constraint was solveable (by incorporating modified nucleosides into mRNA), Karikó was still ignored