The incentive problem at the heart of modern science

In 1883, the British physicist Joseph John Thomson wrote his master’s thesis, A Treatise on the Motion of Vortex Rings, exploring the fluid dynamics that govern the motion of phenomena like smoke rings and circular underwater vortices. It was brilliant. The essay laid the mathematical foundation for knot theory (the study of closed loops in three-dimensional space), showed that single rings could be stable, and gave an explanation for chemical bonding.

There was just one problem: The idea was wrong. Thomson’s paper rested on luminiferous ether — a hypothetical invisible substance scientists then believed filled space — which was ruled out just four years later by the Michelson-Morley experiment of 1887. However, it was from this failure that Thomson gained the insight that atoms are not indivisible, but rather have discrete pieces. The result of this was his 1897 discovery of the electron, which won Thomson the Nobel Prize.

History shows that many of science’s greatest breakthroughs emerged from ideas that initially failed. Yet modern research increasingly punishes the very kind of ambitious failure that makes paradigm-shifting discoveries possible.

How modern science punishes ambition

At the Foundational Questions Institute (FQxI), where I am Chief Scientific Officer, we encourage high-risk, high-reward research. We generally have one interpretation of “high reward”: that the scientific value of success in the research project would be significant.

“High risk” can be taken to mean two things.

First, it means a high probability of failure. When undertaking research into areas in which there has been little progress — take a field like quantum information as an example — this kind of risk is understandable. Here, “safe” research is insufficient. If inquiries into a quantum theory of gravity had a high probability of success, the problem would have been completed long ago.

In these cases, we seek to overcome low odds of success with high numbers of attempts; the value of a single success often outweighs the costs of hundreds of failures by a large margin both in scientific and later economic terms. For instance, the cost to Edison’s team of testing and discarding over six thousand candidate materials was a drop in the ocean of profits from successfully identifying carbonized bamboo as a viable filament for the lightbulb. The expected outcomes are such that we should strongly encourage researchers to undertake high-risk, high-reward research.

The second meaning of “high risk” is the cost of failure in personal or professional terms. One can consider the impact of a failed research trajectory on the career path of an early career researcher. In a “publish or perish” environment typical of the modern university, a failed project leads to the end of an academic career. This has personal ramifications — it can mean being unable to support one’s family, and is often accompanied by negative mental health impacts.

The two forms of risk often overlap; research that has a low probability of success has a high probability costing a researcher dearly. In the 1990s, Katalin Karikó faced such consequences. She had spent years working on reprogramming living cells to produce a urokinase-type plasminogen activator receptor to reduce the risk of blood clots following heart surgeries. Though the delivery method had some success, ultimately the research appeared doomed: Receptor production didn’t last long enough, and scaling up the dosage led to a toxic immune response.

Kariko’s university forced her to opt between demotion and abandoning her research. Fortunately for us all, she chose the former, despite the substantial personal and professional risks. Kariko shared the 2023 Nobel Prize in physiology and medicine, with the committee noting that her research “enabled the development of effective mRNA vaccines against COVID-19.”

A system that feeds and fosters caution

With research time a precious commodity, it would seem a poor career choice on the part of the researcher to devote effort to work with a low probability of success. Thus, many researchers are strongly incentivized to play it safe, and work close to what they know to be successful. As a PhD supervisor, I find it difficult to justify risking the career of a bright student on a risky project, knowing that an unwanted outcome may result in them failing the PhD entirely. Instead, I encourage them to work on models that are far less exciting but will be guaranteed to produce publishable results and ensure they receive their doctorate.

Thus, a brilliant young mind full of original ideas about the arrow of time is redirected to work on calculating the effects of a small change to a known and working theory, to ensure they have the necessary publication history to compete in the market for postdoctoral research positions. The net effect across the whole field is to direct talent away from pursuing big problems and focus on tractable minutia.

There is also unwelcome personal risk in undertaking research in an area that is new — either to the researcher, or to science in general. Such research typically will yield fewer publications, and without an established community, fewer citations. Funding of such areas is rare, as grant schemes are often tied to established arenas. With academic departments hiring on narrow criteria and a tendency of many to devalue research far from their own areas of expertise, truly novel work carries unacceptable levels of risk to an early career researcher.

For those seeking to progress to a faculty position, it is far better career move to work in popular areas whose value is easily demonstrated to a hiring committee or grant evaluation referee. I have sat in such committees, hearing arguments based on productivity metrics for hiring the “safe pair of hands” over the “exciting but risky” candidate to ensure we deliver on publication commitments. With my own research future dependent on satisfying funders and remaining competitive for future grants, I had to weigh the risk to my career against what I thought was better for science.

The misalignment at the heart of science

This all leads to a disconnect between the interest of advancing science, where undertaking high-risk, high-reward research is good, and the interest of the individual researchers, for whom the prospects of such work are predominantly negative. This is a problem of alignment — in game theory terms, the optimal moves for each individual do not correspond to the optimal moves for the field as a whole. Punishing failure risks forcing researchers into ethical tensions: Who is really going to admit that their ideas have hit a dead end if their future livelihood depends on convincing a committee that they still have promise? How should I balance my ethical obligation to support my students’ careers against my obligation to produce novel research, which carries the risk of being incorrect?

The standard response to such analysis is to cite tenure as providing this freedom. For a tenured professor, where is the professional risk? The flaw in this argument is twofold. First, even for a tenured professor, low research “success” will mean less time allocated to research, as grant funding is required to keep teaching loads manageable. It is also a reckless move for a tenured professor to risk the success of their students, and thus they will find a lot of their time being justifiably still spent on low-risk work.

Secondly, the average age of tenure is now well into the 40s. At this point, we have already removed the majority of the risk takers from the talent pool, and the tenured have survived in a low-risk culture. They have been conditioned to play it safe throughout their careers. Why should we expect them to change? Karikó’s story could hardly be more conclusive: What is the point of tenure if a brilliant researcher who later won the Nobel Prize wasn’t protected by it?

Protecting the pursuit of the unknown

If we are to encourage researchers to take on work in which there is a significant probability of failure — a necessity if we agree scientific discovery is a priority for humanity — then we must overcome the serious disincentives keeping them from doing so. We have to decouple the risk of failure that’s intrinsic to ambitious projects from the risk to researchers’ careers and lives. There are a few ways we can do this.

First and foremost, we should embrace failure as a normal part of scientific progress. This means that, rather than never letting null findings see the light of day, we should broadcast failure the way we highlight successes. “This was why my idea didn’t work” should be a valid and welcome title in seminars. Academic journals should give the same prominence to articles about where and why a research direction has become stuck as is given to claims of new and groundbreaking results.

Second, we should evolve the methods by which we evaluate the quality of research. We must accept a well-motivated and rigorously attempted project that did not work as evidence not of a poor scientist, but rather of a strong one who was unlucky. At FQxI we ask, “Did the researcher carry out the right investigation?” and not “Did they get the result they hoped for?” A creative, rigorous program that runs into a wall is well received, and serves as evidence that the researcher is a strong candidate for future support.

Third, money should be detached from the probability of exciting findings. At FQxI, we build a high risk into our grant programs from the very start, accepting some degree of failure as an unavoidable cost of success. This has meant supporting researchers whose beliefs are diametrically opposed — such as Lee Smolin, who believes time to be absolutely fundamental, and Carlo Rovelli, who argues we should forget time entirely.

We have also supported an adversarial collaboration between Kelvin McQueen, for whom consciousness forces the resolution of quantum uncertainties, and Markus Mueller, who believes that physical reality doesn’t exist outside our experience. Mueller and McQueen have worked together to devise a test to distinguish between their competing ideas, and potentially press one into failure. Although only one can emerge unscathed, both have advanced science and should be rewarded for their courage. I know future funding rounds at FQxI will look favourably on their effort to develop both the successful theory and the explore the false starts. Adversarial collaborations now sit at the core of our ongoing Foundational Answers program.

Finally, we must move away from the crude productivity metrics used to assess researchers. Publication and citation counts may be high for those who were lucky, but for the most part they work against those who took the right risks. Instead, search committees, tenure assessments and funding organizations should make the effort to understand what a researcher has done, what they have tried and where they have failed. Expert reviewers should be instructed to report on the ideas, creativity and efforts of a researcher, not on their successes. Grant funding should not be assigned on past outputs, but on the manner in which past projects were undertaken.

The big questions of science aren’t scaled to the human lifetime or our little, fickle economies. Thus we have to value the process, not the outcome. We have to ensure that those who make the right decision for scientific progress are not punished for doing so. Thomson and Karikó’s early failures should be seen for what they are: not signs of a problem, but evidence of brilliant minds whose ideas were worth a risk. Today’s scientists should have the support they need to explore the widest array of creative ideas, most of which will not work. If we really value scientific advancements, we have to give researchers the freedom to fail.

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