Truth Rather Than Belief

Why science has to stay open to its own data.

Some of the most important new medicines and new companies start where the field isn’t looking: a result it can’t explain, a non-consensus idea, or an alternative interpretation. In my experience, this is where real innovation sits, and I’ve spent much of my career trying to find, create, and develop ideas like these.

Finding them depends on following the data, including the data that arrives after a conclusion has been written. That is what ​“follow the science” ought to mean. In practice it has come to mean accept the conclusion, which is an odd thing to ask of a discipline whose conclusions are the part most likely to change.

The trouble starts when a finding gets promoted to a rule. A finding has a date on it and a population behind it. A rule is a finding that has lost both, so people stop retesting it, and before long they stop studying the cases it can’t explain. Those cases are where the next ideas come from.

The tumors that broke the rule

Cancer is one of my favorite examples. The idea that tumors are caused by genetic mutations has been enormously productive. Oncogenes, tumor sequencing and most of the targeted therapies since imatinib came out of it. Along the way it also became an expectation that every tumor would have a mutation to find if you just sequenced hard enough.

Nonetheless, in 2014, a consortium led by Michael Taylor sequenced 47 hindbrain ependymomas, an aggressive brain tumor of infants, and found no recurrent mutations.¹ The mutation rate was very low, and nothing recurred from one tumor to the next. The worst tumors had one thing in common: epigenetic changes that switched off genes a cell needs to mature.

That could easily have been filed as an oddity in a rare tumor. Because people followed it up, we now know these tumors respond to epigenetic drugs in the lab, and since 2019 we have known much of what drives them.² They overproduce a protein called EZHIP, which blocks the same gene-silencing enzyme as the histone mutation behind diffuse midline glioma. Two lethal childhood brain cancers that were being studied separately turned out to share a mechanism.

The mirror image appeared a year after the ependymoma paper. Iñigo Martincorena and colleagues at the Sanger Institute sequenced normal eyelid skin from four healthy people and found a cancer-associated mutation in about a quarter of the cells, none of which was a tumor.³

A child with one of these tumors has no mutation for a targeted drug to hit, so a field that looks only for mutations has nothing to offer that child. An epigenetic cause gives drug developers something to aim at. The eyelid result is just as useful, because if a quarter of normal cells can carry these mutations and stay healthy, then whatever restrains them could be a route to preventing cancer. Neither line of work had anywhere to start while the rule was treated as complete.

When physics was finished

Around 1900 Albert Michelson, America’s first science Nobel laureate, wrote that ​“the more important fundamental laws and facts of physical science have all been discovered.”⁴ Relativity and quantum mechanics arrived within a generation.

The cost of believing him would have been most of what followed. Semiconductors, lasers and MRI all rest on quantum mechanics, and GPS has to correct for relativity to work at all. A large share of the modern economy is built on physics that was discovered after physics had been declared finished.

It is tempting to call a question settled, because a settled question is easier to teach and to administer. But once a field is officially closed, the most talented people go elsewhere, the funding follows them, and whatever was sitting just outside the rule stays there.

Great companies start as rejected ideas

I have watched this from the company side for a long time. If an idea sits comfortably inside the consensus, an established company is usually already pursuing it with more money than a startup will ever have. The easy and obvious ideas are taken and often crowded. The companies that end up mattering are more often built on something that qualified people looked at and turned down.

Cancer immunotherapy is one of the clearest cases. In the 1990s, Jim Allison showed in mice that blocking CTLA‑4, a molecule that acts as a brake on T cells, could make tumors disappear.⁵ Large drug companies thought the approach was too risky, and many experts doubted it could ever be used in people.⁶ A small biotech, Medarex, developed the antibody anyway. It was approved in 2011, Allison shared the Nobel Prize in 2018, and checkpoint inhibitors are now among the most widely used cancer drugs. This same phenomenon occurred with PD‑1, which leverages a similar biology. Merck had the molecule that became Keytruda on the out-license list until Bristol Myers Squibb published surprising data.⁷ Keytruda generated over $30B in revenue in 2025—approximately half of all of Merck’s revenue that year.⁸

Technology has the same history. In 1999, Larry Page and Sergey Brin offered to sell Google to Excite, then one of the big web portals, for $1 million. They were talked down to $750,000, and Excite still said no.⁹ In 2008, Airbnb’s founders met with seven investors and asked for $150,000 in exchange for a tenth of the company. Five declined, and two never replied. Some said they didn’t invest in travel, and others couldn’t see who would use it.¹⁰ Neural networks had been largely set aside by AI researchers since the 1970s, and as late as 2012 almost none of the leading computer-vision papers used them.¹¹ Every major AI company is now built on them.

What strikes me about these stories is how little the rejections had to do with the evidence. Allison had the mouse data. Page and Brin had a search engine that worked. The people saying no were mostly reporting what the field believed at the time, and that was the thing about to change.

Rejection on its own proves nothing, and plenty of rejected ideas deserve it. The idea also has to be true. 

Advice with no expiry date

Advisory bodies are where a consensus gets written down, and what they write down tends to stay in place long after the data has moved.

American parents are told to keep children out of the front seat until they are 13. The rule dates from the mid-1990s, when first-generation passenger airbags were killing children, and it was the right call at the time.¹² The American Academy of Pediatrics still bases the recommendation on crashes from 1992 to 2004, although airbags have been redesigned twice since then and car safety has otherwise dramatically changed.¹³ In newer vehicles, the back seat still cuts a young child’s risk of death by at least half.^14,15 For 9‑to-12-year-olds, though, the two modern studies find either no difference or a higher risk in the back.^14,15 The academy’s 2018 report does not cite the earlier study, even though one of its own authors led it, and I have yet to find a study that compares 13 with 11 or 9.

Cholesterol advice has aged in a similar way. In 1968 the American Heart Association told people to keep dietary cholesterol under 300 milligrams a day and to eat no more than three eggs a week.¹⁶ That limit lasted 47 years, until a federal advisory committee concluded in 2015 that cholesterol is ​“not a nutrient of concern for overconsumption.”¹⁷ Patients are still told HDL is the ​“good cholesterol,” even though drugs that raise it have failed in one trial after another^18,19 and a genetic study of 116,000 people found no protection from inheriting high HDL.²⁰ The advice to lower LDL is sound, but it’s missing what we already know to matter. ApoB levels, which reflect the particles that do the damage, have been the better predictor since a 2011 analysis of 233,455 people,²¹ yet the US guideline issued in March 2026 still lists it as optional.²²

Sometimes the cost has been higher. In 2000, pediatricians advised that high-risk infants avoid peanuts, with no trial behind the advice.²³ When a trial was eventually run, 17.2% of the children who avoided peanut became allergic, compared with 3.2 percent of those who ate it early.²⁴ Similarly, parenting guides went on recommending stomach sleeping until 1988, eighteen years after the data showed it nearly tripled the risk of sudden infant death.²⁵

The incentive to agree

Why does this happen? It follows from the incentives of the profession. A scientist’s standing depends on grants, publications, citations, and peers’ opinions, and each rewards work that extends what the field already believes.

Grants come first, because an academic career depends on them. They pay for the lab and often for part of the scientist’s own salary, and tenure decisions turn on them. In 2025, the NIH funded 18.5% of early-stage applicants for its standard research grant.²⁶ A grant usually runs three to five years, ties the scientist to aims declared in advance, and ends if it isn’t renewed. Under those conditions, you propose work you are fairly sure will succeed, and you think hard before writing a proposal that sets out to prove your reviewers wrong.

The reviewers are drawn from the established scientists in the field, which often means the people whose work the consensus rests on. In 2012, Joshua Nicholson and John Ioannidis looked at US biomedical papers that had been cited more than 1,000 times. Among the principal authors who were not NIH reviewers themselves, about 60 percent had no current NIH funding. They then took a random sample of 100 scientists who did sit on NIH review panels and found that 83 held NIH grants and only one had ever written a paper cited that often.²⁷

Publication and promotion work the same way. Novel papers tend to appear in lower-impact journals and take longer to be noticed, even though over time they are the ones most likely to end up among the most cited.²⁸ Hiring and promotion committees look mostly at recent citation counts and journal names, so an unconventional result costs a young scientist most at the moment a career is being decided.

Reputation matters as well. A senior scientist has usually built a career on a particular finding, sits on the committees that write the guidelines, and has little to gain from a result that overturns it. Max Planck is credited with the remark that science advances one funeral at a time, and Pierre Azoulay’s group has tested it. They followed 452 eminent life scientists who died while still active. After a death, papers in that field by the scientist’s collaborators fell by about 40 percent, papers by outsiders rose by 8 percent, and the outsiders’ papers were unusually likely to become highly cited. They concluded that outsiders had been reluctant to take on the leader of the field while that person was alive.²⁹

We also have a good idea of what different incentives produce, because the Howard Hughes Medical Institute already offers them. It backs a scientist for five years at a time, tolerates early failure and lets people change direction. Azoulay and his colleagues compared Hughes investigators with NIH-funded scientists who had won prestigious early-career prizes, and the Hughes group produced twice as many papers in the top 5 percent by citations and three times as many in the top 1 percent.³⁰

The cumulative effect shows up in the literature as a whole. Across 45 million papers, a standard measure of how often new work displaces older work, rather than building on it, fell by more than 90 percent between 1945 and 2010.³¹

I suspect this is also part of why people trust scientific consensus less than they used to. Anyone can now pull up the paper, check its date, and see how far a recommendation has drifted from its evidence; repeating the recommendation more firmly doesn’t change what they see.

Back to the endless frontier

The American research system began in 1945 with a report Vannevar Bush sent to President Truman, Science, the Endless Frontier. Bush wrote that progress ​“results from the free play of free intellects, working on subjects of their own choice,” and that ​“there must be stability of funds over a period of years so that long-range programs may be undertaken.”³² We kept the funding and dropped the terms. That 90 percent decline is measured from the year he wrote.³¹

I would go back to his terms. Fund people for long enough to fail and recover, as Hughes does. Reserve a fixed share of every research budget for testing what the field already accepts, have outsiders review those proposals, and give overturning a rule the same weight in a tenure case as a discovery. Award some grants by lottery among proposals that clear a quality bar, as funders in New Zealand, Germany and Switzerland now do.³³ A lottery has no friends on the review panel. Put a date on every guideline and let it lapse unless someone re-examines it, as the pediatric academy’s written policy already says.¹³ And use the computing tools we now have to keep each conclusion tied to its data and re-run it as new data arrives, starting with the things everyone already knows.

Bush was right that the frontier is endless. It only looks finished from inside a rule.

I have spent more than twenty years starting companies because it is the best way I know to build the future you want, free of what you are told to think. The ones that worked began with something true that few people believed. The next one is sitting in an exception or an area somebody has been told to ignore.