One of the points that Braben makes in Scientific Freedom, and one that others have made elsewhere, is that science is not as welcoming of new ideas as it may seem. The process of peer review stands in the way of new breakthroughs, and one man's crankery is another's brilliant insight, or so goes the story.
The examples of this that probably come to mind are old: Galileo and heliocentrism or perhaps Semmelweis and hand washing and in general the germ theory of disease. So one may think that science used to be like that and now it is self-correcting to the point where it's not an issue: Peers are now fair judges; great ideas are immediately recognized by domain experts.
But this is not true. It's hard to say if the situation has changed relative to how it used to be, but here I want to make the smaller point that a non-trivial number of key discoveries have been at some point rejected, mocked, or ignored by leading scientists and expert commissions. Sure, eventually they succeeded, this is why we know about these cases. But they could have succeeded earlier, faster.
The point I want to make here is not the precise examples themselves; rather what the examples reveal about science. In many of these cases the papers were eventually published when one or two journals rejected them. In others, the ideas were ignored for decades, or were vigorously debated.
The most worrying thing is not peer review in the context of publications, after all there are a lot of journals and while publishing in Cell Structure and Function looks not as nice as a Nature publication, it's still something, especially if it's actually important. The issue is when giving grants. The examples illustrate that very important feats of science weren't judged as such by peers in a journal context; so it is not unreasonable to assume that the same peers when handing out grants in a study section at NIH may decide to bin a proposal to do research they consider of little consequence.
Of course, it would be unreasonable to ask of a system with non-infinite resources to be able to do perfect filtering of what gets funded or published. A number of false negatives is to be accepted. But If one could do better than the peer reviewers in a given discipline, or at least rate proposals differently, then one could find those false negatives and get them funded. This is again what Braben did with Venture Research.
I'd be great to collect even more examples, if you have some send them to [email protected].
Examples of underrated science
The ornithine cycle
Hans Krebs is most famous for his discovery of the Krebs cycle aka the tricarboxylic acid cycle (TCA) aka the citric acid cycle (CAC) which lies at the heart of cellular energy production. Prior to his discovery of the TCA, Krebs was working on the ornithine (or urea cycle). Back then in his early thirties, Krebs was working in the lab of Otto Warburg and his research involved suspending slices of liver with various reagents to see what the liver would do with them (Ultimately, uric acid is what they were searching for). Well turns out that Warburg - who had pioneered the liver slice technique - thought that it was only useful for catabolic processes like respiration or glycolysis. But not the synthesis of new proteins.
Warburg did not support Krebs’ idea, perhaps because he thought that energy-absorbing reactions (as contrasted with oxidation reactions) would not go forward in tissue slices. When Krebs got freedom to initiate a major research enterprise of his own, in 1931, he decided to begin experiments of the sort he had conceived.
The great majority of scientists accepted the evidence presented in 1932 as convincing and commented enthusiastically. Warburg arranged a formal invitation for me by the Kaiser Wilhelm Gesellschaft, signed by Max Planck, the President, to speak on the subject in Berlin. [...] But there were also adverse criticisms. [...] As late as 1956 Bronk and Fisher reported ~ from my own Department at Oxford that under certain conditions citrulline is less effective than ornithine in promoting urea formation from ornithine and they concluded that citrulline cannot be an intermediate. The results of London and of Trowell were due to inadequate perfusion technique. The conclusions of Bach and Williamson were based on the wrong assumption that arginine and ornithine readily penetrate liver slices. In fact the rates of penetration are relatively slow. While the observations of Bronk and Fisher were correct their interpretation was mistaken.
My idea was that the in vitro system of liver slices, incubated in a saline medium, provided a novel and easy method for measuring accurately the rate of urea synthesis under a variety of conditions. As one small rat liver supplies numerous samples, it is possible to carry out many parallel tests. No comparable method had been available before. Many biochemists and physiologists—including Otto Warburg—were quite surprised to learn that slices are capable of performing synthetic energy- requiring processes
Another driving force, especially in my earlier days, was my ambition to justify my choice of career as a scientist vis-à-vis those who were doubtful about my ability to make a success in this field. These included my father, a surgeon who had inspired me to take up medicine, my teacher Otto Warburg (I believe)—and myself.
Jet engines were simultaneously invented by von Ohain and Whittle (in 1937). While von Ohain got immediate buy in from Ersnt Heinkel (owner of the eponymous aircraft manufacturer), Whittle did not. He faced initial pushback from the the Air Ministry in the UK while research in the US was stalled by NACA (NASA's precursor) as well as the National Academy of Sciences' very pessimistic assessments of the technology:
While serving at the Royal Air Force (RAF) Staff College in the late 1920s, Whittle developed a proposal for jet aircraft development. Both the Air Ministry and the aircraft industry found Whittle’s proposal too radical. In 1935, with financial assistance of two ex-RAF officers, he formed a private firm, Power Jets, to exploit his ideas. With the assistance of the Thompson Huston Company, Whittle had an engine ready for testing in February 1937. Although the test was only partly successful, the Air Ministry made a small grant to Power Jets to continue the tests. After successful tests in October 1938, Whittle received a contract from the Air Ministry to build a flight engine. [...] The initial lack of enthusiasm on the part of the Air Ministry was due to reluctance to divert funds from efforts to improve the performance of the piston-propeller engine (Cook 1991, pp. 97–114; Bobo 2001).
Even as Germany and Britain were pursuing advanced jet aircraft research and development in the late 1930s, the NACA staff and board remained skeptical of the technical and economic viability of gas turbines for aircraft propulsion (Hunsaker 1952).
In its present state, and even considering the improvements possible when adopting the higher temperatures proposed for the immediate future, the gas turbine engine could hardly be considered a feasible application to airplanes mainly because of the difficulty in complying with stringent weight requirements imposed by aeronautics. The present internal-combustion engine equipment used in airplanes weights about 1.1 pounds per hp, and to approach such a figure with a gas turbine seems beyond the realm of possibility with existing materials.
National Academy of Sciences, Committee on Gas Turbines (June 1940)
Source: STAT (2020)
Very recently thrown into the spotlight by their application for COVID, when research first started, Katalin Kariko, the key scientist involved, had trouble getting funding and almost quit:
Katalin Karikó spent the 1990s collecting rejections. Her work, attempting to harness the power of mRNA to fight disease, was too far-fetched for government grants, corporate funding, and even support from her own colleagues. [...]
It was a real obstacle, and still may be, but Karikó was convinced it was one she could work around. Few shared her confidence.
“Every night I was working: grant, grant, grant,” Karikó remembered, referring to her efforts to obtain funding. “And it came back always no, no, no.”
By 1995, after six years on the faculty at the University of Pennsylvania, Karikó got demoted. She had been on the path to full professorship, but with no money coming in to support her work on mRNA, her bosses saw no point in pressing on.
She was back to the lower rungs of the scientific academy.
“Usually, at that point, people just say goodbye and leave because it’s so horrible,” Karikó said. [...]
That discovery, described in a series of scientific papers starting in 2005, largely flew under the radar at first, said Weissman, but it offered absolution to the mRNA researchers who had kept the faith during the technology’s lean years. And it was the starter pistol for the vaccine sprint to come.
Related to this, the paper introducing stabilized coronavirus spikes, part of what goes in the COVID vaccines was rejected five times including rejections from Cell, Nature, or Science.
Airplanes are boringly safe and widespread these days. But not that long ago you had people writing:
It might be assumed that the flying machine which will really fly might be evolved by the combined and continuous efforts of mathematicians and mechanicians in from one million to ten million years, provided of course, we can meanwhile eliminate such little drawbacks and embarrassments as the existing relation between weight and strength in inorganic materials. No doubt the problems has attractions for those it interests, but to the ordinary man it would seem as if effort might be employed more profitably. [Note: The Wright brothers successfully flown their first airplane two months later]
We do not query the interest or excellence of the Wrights’ mechanical achievement. There is no reason apparently why they should not vastly better any recorded performance—fly thousands of feet high, or hundreds of miles in distance. Our skepticism is only as to the utilitarian value of any present or possible achievement of the aeroplane. We do not believe it will ever be a commercial vehicle at all. We do not believe it will find any very large place in the world of sport. We do not believe its military importance is as great as is commonly supposed, or will extend (except accidentally) beyond the range of scouting and courier service.
Also, for aerodynamic theory in general, these two quotes are separated by 75 years, just showing that even if something doesn't seem promising or useful, it can end up being core to a discipline:
Mathematics up to the present have been quite useless to use in regards to flying (14th Annual Report of the Aeronautical Society of Great Britain, 1879)
Mathematical theories from the happy hunting grounds of pure mathematicians are found suitable to describe the airflow produced by aircraft with such excellent accuracy that they can be applied directly to airplane design. (Theodore von Karman, 1954)
The structure of DNA
At this point, Watson realized that DNA was the kind of puzzle he could probably solve, and he began to take an interest in interpreting X-ray crystallography images.
This interest led him to apply for a transfer to the University of Cambridge, where Sir Lawrence Bragg, the founding father of X-ray crystallography, worked.
However, this process proved to be more complicated than he’d expected. His first request was rejected because Watson was considered under qualified. But, after establishing a phony partnership with another virus scientist at Cambridge, he was able to convince the admissions committee. [...]
Yet, when they made their first 3-D models, and invited Franklin and Wilkins to have a look, Watson and Crick were dismissed and heavily criticized by their colleagues as they’d recorded Franklin’s X-Ray measurements incorrectly.
Sir Lawrence Bragg, the head of their research department at Cambridge University’s Cavendish Laboratory, was also a harsh critic of their method of model-building, calling it unsophisticated and childish. [...]
Even Chargaff wasn’t pleased. Prejudiced against Watson's American accent and haircut, he wanted nothing to do with the duo and scolded them when they couldn’t immediately recall the chemical difference between the four bases.
At this point, Sir Bragg decided to finally shut down Watson and Crick’s research.
It was during this calm period that an advanced copy of a manuscript by Linus Pauling – in which he attempted to identify the structure of DNA – arrived at Cavendish.
When Sir Bragg received it, he tried to keep it away from Watson and Crick, assuming they’d just waste their time on DNA if they saw it.
The mechanism for the synthesis of ATP
Source: Cross (2018)
ATP is the energy currency of the cell, which is manufactured by, chiefly, ATP synthase, in turn one of the most beautiful proteins there is. An actual motor that rotates, driven by protons. Paul Boyer got the Nobel for it in 1997 for it. Yet, the leading journal in the field, The Journal of Biological Chemistry, declined to publish his work.
As is often the case with transformational ideas, early reactions were negative. When the Journal of Biological Chemistry rejected our manuscript containing data supporting this concept, Boyer told me without animosity that he could see why they would do that — “It was a very striking claim.”
Also known as Oxphos for short, this is the whole process in which ATP synthase is embedded. Peter Mitchell had to fight an uphill battle that continued even after he was given a Nobel Prize in 1978 for his contribution! He was only able to keep going thanks to private funding, as he established his own private research institute in Cornwall.
‘The years after the late 1950s were a particularly difficult time for me, when most biochemists (but not David Keilin) were rejecting suggestions concerning chemiosmotic coupling. I had to work very hard to get my colleagues to take these ideas seriously. Now, I find it a little sad that this work has become so much taken for granted that it is as though the chemiosmotic theory was self-evident from the beginning [...]
Perhaps the difficulties are summarized in the words of Efraim Racker who observed that Mitchell’s ideas, his ‘hypothetical proton gradient and imaginary membrane potential’ resembled the ‘pronouncements of a court jester or a prophet of doom’
Nuclear Magnetic Resonance
Source: Ernst (1991)
NMR is the foundation for fMRI, and it is a technique used in molecular biology to determine the structure of proteins. Richard Ernst was awarded the Nobel Prize in 1991 for its development. And yet
The response to our invention was however meager. The paper that described our achievements was rejected twice by the Journal of Chemical Physics to be finally accepted and published in the Review of Scientific Instruments.
Source: Kroemer (2000)
The final step came in 1963, while I worked at Varian Associates in Palo Alto, CA. A colleague – Dr. Sol Miller – gave a research colloquium on the new semiconductor diode laser. He reported that experts had concluded that it was fundamentally impossible to achieve a steady-state population inversion at room temperature, because the injected carriers would diffuse out at the opposite side of the junction too rapidly. I immediately protested: “But that’s a pile of … ; all you have to do is give the outer regions a wider energy gap.” I wrote up the idea and submitted the paper to Applied Physics Letters, where it was rejected. I was talked into not fighting the rejection, but to submit it to the Proceedings of the IEEE, where it was published, but ignored. I also wrote a patent, which is probably a better paper than the one in Proc. IEEE.
Then came the final irony: I was refused resources to work on the new kind of laser, on the grounds that there could not possibly be any applications for it. By a coincidence, the Gunn effect had just been discovered, and having a long-standing interest in hot-electron negative-resistance effects, I worked on the Gunn effect for the next ten years, and did not participate in the final technological realization of the laser.
Polymerase Chain Reaction
PCR is among the most common of the lab techniques. Kary Mullis got a Nobel for it in 1993. And yet the paper presenting PCR was rejected both from Science and Nature, being published in a rather more obscure Methods in Enzymology in 1987. EDIT: See here for nuance
John Polanyi helped pioneer the field of chemical lasers, and Theodore Maiman is credited as the inventor of the laser. The former got a Nobel prize. There's no need here to explain what lasers are useful for.
Physical Review Letters rejected the paper as lacking scientific interest. Shortly thereafter they rejected T. Maiman's report of the first operating laser, on the same grounds. Polanyi read about this second rejection, quite by chance, while holidaying on an island in Georgian Bay. On returning to Toronto in September of 1960 he submitted the identical manuscript to the Journal of Chemical Physics, where it was promptly published.
Since then, vibrational lasers and, in particular, chemical lasers (due, respectively, to C.K.N. Patel and G.C. Pimentel) have developed into the most powerful sources of infrared radiation. Polanyi is fond of asking sponsors of basic research who insist on evident promise of applications, whether they would have been far-sighted enough to support studies of barely detectable luminescence as a means to the development of the most powerful lasers in existence.
Famously, Maiman's write-up was rejected by Physical Review Letters, whose editors judged it just another episode in the stream of research related to masers, led by Charles Townes and others. Equally famously, the laser was dubbed “a solution looking for a problem” — which Townes has said he regarded not as a joke but as a challenge
Sources: Watts (2011)
This technique involves using an anti-body to which a radioactive isotope is stuck, the antibody will bind to the target of interest, and that will be visible with radiation. It was developed by Rosalyn S. Yalow, which got her a Nobel in 1977. But it wasn't trivial to get there:
Using immunoassay, she and Berson had shown the presence of insulin binding antibody in the circulation of insulin-treated research participants. Such a finding ran contrary to the orthodoxies of immunology in the 1950s, which held that the immune system could not recognise entities as small as protein molecules. Science rejected the paper; so did the Journal of Clinical Investigation. But after a discreet change to the paper's title, the latter relented. The report appeared in 1956. In later years Yalow delighted in illustrating her lectures with a slide of the rejection letter.
Undeterred by the initial reluctance to accept their findings, Yalow and Berson persevered. It was a further paper published in 1960 on the use of RIA to measure endogenous insulin in human beings that, as Professor Jesse Roth describes it, “took the field by storm”. An endocrinologist who now works at North Shore Long Island Jewish Health System in New York, Roth first encountered Yalow and Berson in the early 1960s as a young physician bent on learning how to do research. “The 1960 paper was long and detailed”, he says, “because they were trying to deal with all the opposition to RIA”. Once this had been achieved, clinicians began to see the appeal of RIA.
When I first learned about mitochondria back in high school, I thought hmm these look like little bacteria, could it be that cells somehow ate them and then became part of them? Turned out, yes, and Lynn Margulis had already shown that back in the 60s. But convincing the scientific community that she was right was not trivial!
Lynn Margulis: In 1966, I wrote a paper on symbiogenesis called “The Origin of Mitosing [Eukaryotic] Cells,” dealing with the origin of all cells except bacteria. (The origin of bacterial cells is the origin of life itself.) The paper was rejected by about fifteen scientific journals, because it was flawed; also, it was too new and nobody could evaluate it. Finally, James F. Danielli, the editor of The Journal of Theoretical Biology, accepted it and encouraged me. At the time, I was an absolute nobody, and, what was unheard of, this paper received eight hundred reprint requests
Source: Yandell (2015)
Clustering analysis is routinely used to more easily visualize datasets of, for example, gene expression.
More recently, David Botstein, now at Princeton University, Michael Eisen, now at the University of California, Berkeley, and their colleagues had their paper on cluster analysis, a widely used method for interpreting microarray data, rejected by Science. Botstein recalls phoning the editor to unsuccessfully appeal the rejection. “The only thing I remember telling her was that it was my thought that this would someday be a citation classic, and in this case I was right,” Botstein says. The paper, which was eventually published in PNAS (95:14863-68, 1998), now has nearly 15,000 citations, according to Google Scholar.
The weak interaction
Source: Wikipedia (2020)
Fermi got the Nobel Prize in Physics in 1938 and discovered what would eventually be called weak interaction, one of the fundamental interactions of nature recognized in modern physics, along with the strong interaction, electromagnetism, and gravitation.
Fermi first submitted his "tentative" theory of beta decay to the prestigious science journal Nature, which rejected it "because it contained speculations too remote from reality to be of interest to the reader." Nature later admitted the rejection to be one of the great editorial blunders in its history. Fermi then submitted revised versions of the paper to Italian and German publications, which accepted and published them in those languages in 1933 and 1934. The paper did not appear at the time in a primary publication in English. An English translation of the seminal paper was published in the American Journal of Physics in 1968.
Crystals are ordered structures that are periodic, formed of a basic unit that repeats itself. Quasicrystals are ordered but not periodic. Sounds innocent enough, but apparently quite controversial!
Dan Shechtman submitted a paper on quasicrystals to Physical Review Letters, but it was rejected on the grounds that it would not be of any interest to physicists. He then submitted his work to the journal Metallurgic Transactions, which published the paper; this work formed the basis of Shechtman winning the Nobel Prize in 2011.
From the day Shechtman published his findings on quasicrystals in 1984 to the day Linus Pauling died (1994), Shechtman experienced hostility from him toward the non-periodic interpretation. "For a long time it was me against the world," he said. "I was a subject of ridicule and lectures about the basics of crystallography. The leader of the opposition to my findings was the two-time Nobel Laureate Linus Pauling, the idol of the American Chemical Society and one of the most famous scientists in the world. For years, 'til his last day, he fought against quasi-periodicity in crystals. He was wrong, and after a while, I enjoyed every moment of this scientific battle, knowing that he was wrong."
Linus Pauling is noted saying "There is no such thing as quasicrystals, only quasi-scientists." Pauling was apparently unaware of a paper in 1981 by H. Kleinert and K. Maki which had pointed out the possibility of a non-periodic Icosahedral Phase in quasicrystals (see the historical notes). The head of Shechtman's research group told him to "go back and read the textbook" and a couple of days later "asked him to leave for 'bringing disgrace' on the team." Shechtman felt dejected. On publication of his paper, other scientists began to confirm and accept empirical findings of the existence of quasicrystals.
The Higgs boson
Source: Efron (2019)
Aka the Englert–Brout–Higgs–Guralnik–Hagen–Kibble boson, no need to say much about this one.
Peter Higgs submitted a short paper describing what came to be called ’the Higgs model’ to the journal Physics Letters, but it was rejected. He then resubmitted to the journal Physical Review, and was awarded the Nobel Prize in Physics in 2013, after researchers at CERN detected evidence of the Higgs boson at their ATLAS and CMS experiments.
Bose-Einstein condensates and statistics
Source: Slavov (2014)
Satyendra N. Bose did not get a Nobel Prize (he was 'merely' nominated for one), but he gave his name to one of the two families of elementary particles, bosons (The other being fermions, like quarks) .
Late in 1923 [Bose] submitted a paper to the subject to the Philosophical magazine. Six months later the editors of the magazine informed him that (regrettably) the referee’s reports on his paper were negative. Undeterred, he sent the rejected manuscript to Einstein …
The market for lemons (adverse selection)
Source: Akerlof (2001)
An extremely well known paper in economics from Nobel Prize winner George Akerlof, it has its own wikipedia page. The paper discusses the circumstances under which markets will or will not exist, and at which price. This has been used (wrongly) as an argument in debates around healthcare, but in any case the original paper provides a useful framework to reason about these situations and it is now very well regarded. But it wasn't so at first:
By June of 1967 the paper was ready and I sent it to The American Economic Review for publication. I was spending the academic year 1967-68 in India. Fairly shortly into my stay there, I received my first rejection letter from The American Economic Review. The editor explained that the Review did not publish papers on subjects of such triviality. In a case, perhaps, of life reproducing art, no referee reports were included.
Michael Farrell, an editor of The Review of Economic Studies, had visited Berkeley in 1966-67, and had urged me to submit “Lemons” to The Review, but he had also been quite explicit in giving no guarantees. I submitted “Lemons” there, which was again rejected on the grounds that the The Review did not publish papers on topics of such triviality.
The next rejection was more interesting. I sent “Lemons” to the Journal of Political Economy, which sent me two referee reports, carefully argued as to why I was incorrect. After all, eggs of different grades were sorted and sold (I do not believe that this is just my memory confusing it with my original perception of the egg-grader model), as were other agricultural commodities. If this paper was correct, then no goods could be traded (an exaggeration of the claims of the paper). Besides — and this was the killer — if this paper was correct, economics would be different.
I may have despaired, but I did not give up. I sent the paper off to the Quarterly Journal of Economics, where it was accepted.
Early work in cognitive neuroscience
Published in an obscure journal (Proceedings of the Institute of Radio Engineers) in 1940, What the Frog's Eye Tells the Frog's Brain is considered a foundational paper in cognitive neuroscience, having been cited 2.7k times since then.
These important results were initially dismissed. “We had the utmost trouble. We were laughed off the stage, literally, at the American Physiology Society in Atlantic City, where we tried to present it,” Lettvin told his collaborator Luis Amador in 1986. The NIH even threatened to withdraw his grant if he didn’t “start behaving,” he recalled. Then he got his break. “IRE [the Institute of Radio Engineers] was after me to write a paper on electrodes,” he told Amador. “I made a trade with them—I’d write the paper on electrodes if they would publish the paper on the frog’s eye.” The editor’s response? “All right, but we want a good paper on electrodes.”
Even after the paper was published in 1959, the findings met with considerable skepticism. One disgruntled scientist—fellow MIT researcher Walter Rosenblith—”felt we were … liars, held a meeting on perception, visual perception, and didn’t invite us,” Lettvin told Amador. Another colleague circumvented the snub by taking conference attendees on an unannounced visit to his lab so they could see for themselves how the experiment was done. The visiting audience was convinced, and Rosenblith soon apologized. “And that,” Lettvin concluded, “was the time that we began to be taken seriously.”
A method for modeling fatigue damage
Source: Paris et al. (1999)
Fatigue occurs when a cyclic load is applied to a material. Small cracks start to form, leading to a complete breakdown. This is a problem because the threshold required to start the fatigue process is way lower than the force required to break the material in one go. Some early work, that ended up being widely cited and used by aerospace manufacturers, was rejected by multiple parties:
The paper written on that work at that time was not published until 1960 , since it was delayed by rejection by three journals (ASME, AIAA, and Phil. Mag.). Though that method is widely accepted today, in the late 1960s at Boeing it was rejected by an outside review panel for federal supersonic transport exploratory studies as ‘it simply won’t work’. Moreover, the federal agency funding the most extensive fatigue studies on multiple occasions stated ‘no interest’ in such work, although since 1970 they have funded more work than any other source. It was a study of rejection by authority with preconceived notions and blind self-interest, with a total reversal after more than 10 years. This was an interesting personal and historical lesson on ‘radical’ discoveries.
Source: Wikipedia (2020)
Hey, doesn't it seem like South America fits with Africa? is another of those slam dunks that happens to be true. Today we recognize that it's no coincidence that they fit, as is explained by continental drift (later, plate tectonics) laid out by meteorologist Alfred Wegener. The theory took a very long time to be accepted, perhaps due to the fact that it was hard to do experiments, one could only look at existing data (from the Earth's crust) and theorise.
Although now accepted, the theory of continental drift was rejected for many years, with evidence in its favor considered insufficient. One problem was that a plausible driving force was missing. A second problem was that Wegener's estimate of the speed of continental motion, 250 cm/year, was implausibly high. (The currently accepted rate for the separation of the Americas from Europe and Africa is about 2.5 cm/year). It also did not help that Wegener was not a geologist. Even today, the details of the forces propelling the plates are poorly understood. [...]
In 1939 an international geological conference was held in Frankfurt. This conference came to be dominated by the fixists, especially as those geologists specializing in tectonics were all fixists except Willem van der Gracht. Criticism of continental drift and mobilism was abundant at the conference not only from tectonicists but also from sedimentological (Nölke), paleontological (Nölke), mechanical (Lehmann) and oceanographic (Troll, Wüst) perspectives. Hans Cloos, the organizer of the conference, was also a fixist [...]
David Attenborough, who attended university in the second half of the 1940s, recounted an incident illustrating its lack of acceptance then: "I once asked one of my lecturers why he was not talking to us about continental drift and I was told, sneeringly, that if I could prove there was a force that could move continents, then he might think about it. The idea was moonshine, I was informed."
The theory of relativity
It has its own very lenghty wikipedia page!
Source: Loewenberg (1933)
Again there is a wikipedia page that focuses on social and religious rejection of the theory. But many scientists of renown like Agassiz initially rejected Darwinism as well.
Agassiz's consistent and unrelenting opposition has led to consider- able speculation as to the motives which inspired it. [...] His preponderating influence in scientific circles prevented a too hasty acceptance among professional naturalists who were wary of espousing views which the greatest authority of the day branded as a "mere mine of assertions"
The cause of stomach ulcers
It was bacteria all along! Not stomach acid. But this took a while to be established, getting Marshall and Warren a Nobel in 2005.
As Paul Thagard notes, gastroenterologists were less receptive to the bacterial theory of ulceration than microbiologists. At the Second International Workshop on Campylobacter Infections in Brussels, where Marshall next reported his findings, microbiologists began research projects to find the bacteria while many gastroenterologists scoffed, calling Marshall's theory "preposterous". Marshall and the international medical community had to generate more evidence before gastroenterologists would admit the relationship between H. pylori and ulcers.
October 2: Marshall presents his and Warren's results at a local College of Physicians meeting. He meets with criticism, which Marshall later admits was well-founded (at least in part)
February: Gastroenterological Society of Australia rejects Marshall's abstract to present his research at their yearly conference. They deem it in the bottom 10% of papers submitted. The same abstract is accepted for presentation at a Campylobacter workshop in Brussels.
Marshall and Warren's paper is accepted by The Lancet in May and published in June. Many reviewers dislike the paper.
June 12: Marshall intentionally consumes H. pylori and becomes ill. He takes antibiotics and is relieved of his symptoms.
Source: Wikipedia (2020)
Hand washing sounds like common sense, but famously Ignaz Semmelweis was mocked for proposing washing hands in lime and chlorine as disinfectant as means to reduce infections in a hospital. Note here that hand washing with soap was already the standard practice which is often ignored in Semmelweis' story, as well as his data not being crystal clear. He was not fully right, but he was directionally right. The germ theory of disease would still take decades to be established by the likes of Pasteur and others.
The consensus theory of cancer is that cancer occurs via DNA mutations. But some of these can be induced by viruses. This latter was not initially known, and early attempts to show otherwise were met by skepticism. Peyton Rous did some early work in the area in 1910s, but his Nobel would have to wait a few decades. Note as Becsei-Kilborn notes, as with Semmelweis' case, Rous was trying to prove too much, he was trying to argue that cancer was viral in origin in general, while the current consensus is that only some cancers are such.
The finding clashed with the emerging consensus in that it implied that an ultramicroscopic agent, a virus, could be involved in causing the cancerous tumor. At the time, however, Rous was unable to convince his colleagues of the presence of the infective agent. In 1915, after numerous failed attempts to determine the nature of the Rous sarcoma virus (RSV) and to isolate a virus from a mammalian host, he decided to move on to other areas of research. Although Rous returned to cancer research in the early 1930s, he never again took up his work on the chicken sarcoma. In 1966, however, Rous was given the Nobel Prize for the much earlier RSV discovery and for the impact he had had on the develop ment of cancer research. Today, Rous is regarded as one of the founding fathers of cancer virology and is recognized to have had a major shaping influence on cancer research. [...]
Renato Dulbecco, for instance, a leading virologist, claimed that Rous' work did not receive the attention it deserved for 40 years "because the minds of the scientists were not prepared to think of viruses as agents of cancer."5 The well known British virologist Christopher H. Andrewes, who was an enthusiastic supporter and friend of Rous, simply noted that Rous' "outstanding discovery of a virus causing a tumor in fowls was disregarded."6 There were some, on the other hand, who attributed the relative neglect of Rous' work to a failure to recognize its full significance. One view, typical of many at the time, was that Rous "was so far ahead of his time that he was not properly recognized."7 In 1989, Nobel recipient, cancer scientist, Harold E. Varmus, who never failed to express his own indebtedness to Rous' work, referred to Rous' receiving the Nobel Prize, as "a tribute to... the principle of delayed recognition."8 In other accounts of Rous and his work, Rous is portrayed as a scientist who had been ignored, marginalized and even ridiculed for his 1911 discovery.9 Sigismund Peller explained that the 1910's and 1920's did not favor microbial theories of cancer causation and that it was almost inevitable that Rous' discovery would be condemned or "deprecated," since it constituted a tangible territorial threat to the scientists then pursuing the dominant lines of research.10 Ralph W. Moss in his critique of the cancer establishment writes that Rous was "scorned."11 Some of Rous' fellow scientists also disparaged Rous for having abandoned the sarcoma experiment in 1915 after only having devoted a few years' work to the problem.12 [...]
Rous had a lifetime commitment to and interest in the study of cancer and its etiology. He suspended his work on cancer and viruses several times during his career because he had learnt by experience that in order to "maintain oneself scientifically" one would have to work on other themes.31
The immune system can fight cancer to some extent. But back a few decades ago the prevailing view was that cancer, being part of the "self" would not be able to be detected by the immune system at all; if it could then it seems we would be constantly being attacked by it.
James Allison got the Nobel Prize in 2018 for his work on showing that it could, and furthermore, that the mechanism by which it does could be targeted therapeutically, opening the door to cancer immunotherapy.
There’s one person — I won’t say his name here — who all along insisted it would never work. Then in 2011, after ippy was approved by the FDA for melanoma, he went, “Well, it’ll be a good melanoma drug, but it won’t work in anything else.”
For whatever reason, there’s sometimes been a lingering skepticism. But the situation for immunotherapy is much different from 15 years ago. In those days, 90% of people I encountered thought it was not worth doing because it wouldn’t work.
I’d go, “I’ve got something that can cure cancer,” and they’d go, “What kind of cancer would you use it for?” I’d say, “I don’t think the [specific] cancer matters much,” and that would be the end of the meeting. There had been a lot of failures with attempts to make vaccines for cancer. No one wanted to go there.
In fact, with no theoretical framework suggesting that tumours could be rejected (Table 1), the general feeling amongst immunologists was that it would be impossible for the immune system to recognize and respond to malignant cells. Woglom expressed this view in dramatic terms in a review in 1929 by stating that ‘It would be as difficult to reject the right ear and leave the left ear intact as it is to immunize against cancer’ [...]
In this regard a particularly influential paper was published in 1976 where it was claimed that, unlike chemically induced transplantable tumours, spontaneously arising tumours are not recognized by the immune system. In this paper the authors state that, based on isotransplants of 27 different spontaneously occurring tumour types, no evidence of spontaneous tumour regression was observed, despite approximately 20 000 tumour transplants being performed. I distinctly recall that by 1980 cancer immunotherapy was generally regarded as an approach with little or no chance of success.
Early work on the kinetic theory of gases
Source: Brush (1963)
You've probably never heard of Herapath and Waterston and you probably know Joule and Maxwell. To some extent this is a historical accident:
On 24 May 1820 a manuscript entitled 'A Mathematical Inquiry into the Causes, Laws and Principal Phenomena of Heat, Gases, Gravitation, etc.' was submitted to Davies Gilbert for publication in the Philosophical Transactions of the Royal Society. The author was John Herapath (I790-I868), and his article included a comprehensive (if somewhat faulty) exposition of the kinetic theory of gases. Sir Humphry Davy, who assumed the Presidency of the Royal Society on 30 November 1820, became primarily responsible for the fate of the article and wrote several letters to Herapath concerning it. After it became clear that there was considerable opposition to its publication by the Royal Society, Herapath withdrew the article and sent it instead to the Annals of Philosophy, where it appeared in I82I (i). Herapath's theory received little notice from scientists until thirty-five years later, when the kinetic theory was revived by Joule, Kronig, Clausius, and Maxwell. [...]
While we have considered Davy chiefly responsible for the rejection of Herapath's theory, it should be clear that Davy's fault was mainly that he shared the prejudices of most of his contemporaries against theoretical physics.* Unlike Waterston, whose work on the kinetic theory was completely suppressed by the Royal Society twenty-five years later ( 5), Herapath at least got a public hearing for his views, and still failed to convert any scientists to them. What is remarkable isthat even in early nineteenth century England where scientists as influential as Davy were supporting the idea that heat is a mode of motion, a mathematical formulation of a particular theory consistent with this idea could win no support.
Persistance of memories outside of the brain in planarians
Source: Duhaime-Ross (2015)
Planarians are flatworms that have the peculiar ability of growing back even if they are chopped into tiny bits. Each bit can regrow a full worm. Planarians have a main ganglia in their head, a sort of primitive "brain". The standard answer for how memories are stored in some story about the synapses in the brain. So when you chop off the head of a planarian and grows a new one, anything you may have taught it (To avoid light say) should have been forgotten. But no. Somehow, the memories are stored somewhere else in the body. This probably sounds utterly implausible to you if you haven't come across this before, but this is what James McConnell found back in the 70s and the finding remained controversial, ultimately rejected and ignored until it was fished back from obscurity by Michael Levin, who used more modern techniques to show that yes, it happens.
Whether this generalizes to other species or what's the mechanism behind it remains unknown. Unlike the other findings in this list, this one in particular remains disputed, but perhaps to a lesser extent than it used to. I've chosen it to illustrate what it feels like to be looking at a finding that still stands outside of our usual model of the world, as is the closest thing that seems plausible enough that is yet in that gray area that is the outer rim of science. As far as I was able to find, there has been no formal critique or failure to replicate Levin's experiment.
But the fantastic takeaway of McConnell’s study — that cells other than neurons could store information — caused many to question the study’s methodology and conclusions. In 1960, he published a second experiment, one that pushed his theories far beyond what anyone would have imagined. This one left the scientific community completely stumped.
Widely known as "the cannibalism experiment," the study tested another McConnell theory: that memory could be transferred chemically from one flatworm to another through something called "memory-RNA." Memory-RNA, McConnell suggested, was a special form of RNA — the intermediary form of genetic information that fills the gap between DNA and proteins — that could store long-term memories outside the brain. His method was unorthodox, to say the least: McConnell fed bits of trained flatworms to their untrained brethren. As a result, McConnell claimed, the untrained flatworms performed behaviors that the trained flatworms had previously learned. In short, the dead flatworms’ memories had found a new home.
"Biologists and chemists said ‘no way,’" recalls Reeva Kimble, who did undergraduate research for McConnell in 1959 and 1960. Reeva later married Daniel Kimble, the student who gathered data for McConnell’s first regeneration experiment. McConnell’s opponents couldn’t make sense of his findings. For them, "there was no mechanism to understand his result, so it had to be hogwash," Reeva says. [...]
L’etoile readily admits that McConnell’s failures continue to loom large over Levin’s study. It’s a "cautionary tale in the field of experimental biology" — one that comes with "a lot of baggage," she says. The fact that so many research groups had trouble replicating flatworm training protocols in the ‘60s and ‘70s means that the bar to convince her has been set very high, she says. "I think I have a great deal of skepticism about [flatworm] training."
Source: Lander (2016)
Yeah, that CRISPR that is widely used as a cheap and reliable gene editing tool.
During the August holiday in 2003, Mojica escaped the scorching heat of Santa Pola’s beaches and took refuge in his air-conditioned office in Alicante. By now the clear leader in the nascent CRISPR field, he had turned his focus from the repeats themselves to the spacers that separated them. Using his word processor, Mojica painstakingly extracted each spacer and inserted it into the BLAST program to search for similarity with any other known DNA sequence. He had tried this exercise before without success, but the DNA sequence databases were continually expanding and this time he struck gold. In a CRISPR locus that he had recently sequenced from an E. coli strain, one of the spacers matched the sequence of a P1 phage that infected many E. coli strains. However, the particular strain carrying the spacer was known to be resistant to P1 infection. By the end of the week, he had slogged through 4,500 spacers. Of 88 spacers with similarity to known sequences, two-thirds matched viruses or conjugative plasmids related to the microbe carrying the spacer. Mojica realized that CRISPR loci must encode the instructions for an adaptive immune system that protected microbes against specific infections.
Mojica went out to celebrate with colleagues over cognac and returned the next morning to draft a paper. So began an 18-month odyssey of frustration. Recognizing the importance of the discovery, Mojica sent the paper to Nature. In November 2003, the journal rejected the paper without seeking external review; inexplicably, the editor claimed the key idea was already known. In January 2004, the Proceedings of the National Academy of Sciences decided that the paper lacked sufficient “novelty and importance” to justify sending it out to review. Molecular Microbiology and Nucleic Acid Research rejected the paper in turn. By now desperate and afraid of being scooped, Mojica sent the paper to Journal of Molecular Evolution. After 12 more months of review and revision, the paper reporting CRISPR’s likely function finally appeared on February 1, 2005 (Mojica et al., 2005) [...]
The authors proposed that the CRISPR locus serves in a defense mechanism—as they put it, poetically, “CRISPRs may represent a memory of ‘past genetic aggressions.’” Vergnaud’s efforts to publish their findings met the same resistance as Mojica’s. The paper was rejected from the Proceedings of the National Academy of Sciences, Journal of Bacteriology, Nucleic Acids Research, and Genome Research, before being published in Microbiology on March 1, 2005. [...]
In addition, they showed that the two RNAs could function in vitro when fused into a single-guide RNA (sgRNA). The concept of sgRNAs would become widely used in genome editing, after modifications by others to make it work efficiently in vivo.
Siksnys submitted his paper to Cell on April 6, 2012. Six days later, the journal rejected the paper without external review. (In hindsight, Cell’s editor agrees the paper turned out to be very important.)
Notably, too, many did their landmark work in places that some might regard as off the beaten path of science (Alicante, Spain; France’s Ministry of Defense; Danisco’s corporate labs; and Vilnius, Lithuania). And, their seminal papers were often rejected by leading journals—appearing only after considerable delay and in less prominent venues. These observations may not be a coincidence: the settings may have afforded greater freedom to pursue less trendy topics but less support about how to overcome skepticism by journals and reviewers. [Note: Robert Root-Bernstein argues something similar for the early development of biochemistry, that many of the researchers did their work in the periphery of the reputed institutions]
Ed Boyden is by any measure a very successful scientist, having contributed to the development of optogenetics, which enables the direct control of neurons by means of light. Back in 2015 he published a paper presenting a new technique, expansion microscopy (ExM), whereby the sample to be studied is expanded prior to examination (By immunofluorescence, regular microscopy, etc). ExM has then led to the development of other techniques like ExSEQ that makes it possible to see not only what the cell is up to in terms of its transcriptome but also where in the cell these mRNAs are. But once again, getting funding for ExM wasn't trivial:
When neuroscientist Ed Boyden first approached the National Institutes of Health for funds to develop expansion microscopy, he was rejected. So he applied again. Second time around he was also rejected, but undeterred, he applied again and again and again and again.
"Many NIH grant proposals were rejected one after the other as people just didn't believe this could work," says Boyden, from the MIT Media Lab and the McGovern Institute for Brain Research. "But I always knew expansion microscopy was going to be really useful." [...]
For me, it became personal because when we proposed this expansion microscopy technology, where we blow up brain specimens and other specimens a hundred times in volume to map them, people thought it was nonsense. People were skeptical. People hated it. Nine out of my first ten grants that I wrote on it were rejected.
If it weren’t for the Open Philanthropy Project that heard about our struggles to get this project funded — through, again, a set of links that were, as far as I can tell, largely luck driven — maybe our group would have been out of business. But they came through and gave us a major gift, and that kept us going.
The structure of the G-protein-coupled receptors
What are the G-protein-coupled receptors you may ask. They have many functions, but what's relevant here is that they are an important class drug targets, with 50% of all drugs in the market targeting them! Brian Kobilka got the Nobel in Chemistry in 2012 for "understanding how G protein-coupled receptors function". Once again,
Kobilka’s single-minded pursuit, which took around 15 years before it actually yielded a successful crystal structure, could potentially have been his downfall. ‘It was a big risk that he took; at times he lost a lot of his funding, the lab could have been in big trouble,’ says Bouvier. [...]
But the size and flexibility of GPCRs was a problem for traditional x-ray crystallography. Kobilka's team needed ways to stabilize the floppy receptor, primarily the portion of the proteins that protruded outside the cells, as well as the G-protein binding site on the inside. Progress was painfully slow. Kobilka even lost his funding from the Howard Hughes Medical Institute when results sputtered.
Why does this happen?
I wrote two articles a while back, On the express rejection and acceptance of beliefs on how it is rational to discard evidence and theories that you consider very unlikely to begin with. In an ideal world, information acquisition and verification is costless, but when you introduce costs you are back to the real world where you need to prioritize what to pay attention to. So new, surprising, unexpected ideas may rationally be rejected by people that are experts in a given field, on the grounds of their prior experience and knowledge. Some have given this tendency the name of the Semmelweis reflex.
From many of these examples, a common thread is the following or a combination thereof:
- Someone is seen as an outsider within a field
- The data that supports or undermines claims is noisy. This I think is the core underlying reason, the root of most evil. In turn, the reason for this is lack of tooling to produce precise observations, or funding to increase sample sizes.
- Being right, for the wrong reasons. The reasons may be shot down. Rejecting "A->B" does not mean "B" is false, it just means "A"was not a good reason for B.
These rationales can play into each other into nasty feedback loops, into what I call scientific flip-flopping. If an idea has been prematurely rejected for the right or wrong reasons and the field has moved on, it may be difficult for the idea to be reconsidered again. This was the case for oncoviruses or cancer immunotherapy:
Plausibly then, as a heuristic for detecting huge if true, yet ignored findings:
- Get a team of outsiders (With the right scientific mindset, they need to understand what they read!)
- Find areas where flip-flopping has occurred, or where there are anomalies, or intense debate about whether they are true or not. Find "huge if true" results.
- Fund them
Appendix: Other cases
These include the rejection of Cerenkov radiation, Hideki Yukawa's meson, work on photosynthesis by Johann Deisenhofer, Robert Huber and Hartmut Michel, and the initial rejection (but eventual acceptance) of Stephen Hawking's black-hole radiation. Hindsight is always perfect. But we can take comfort, however dubious, from the fact that our unmitigated embarrassments are but a minority in a substantial list of journals' historical misjudgements. (Source)
I don't count Krebs' Krebs cycle because that rejection was not due to the quality of the paper, but due to lack of space in the journal. Barbara McClintock's case seems unclear. As is Prusiner's and prions. Or Arrhenius.
There are also a few other cases that may make it into this list that have not been proven yet. For example, the theory of the mitogenetic field which Langmuir derrided as pathological science was seen as potentially worth looking into in Ahead of the curve, edited by Michael Levin who is far from being a crank. The book itself, which lists a few more examples that could be added to this list starts:
The popular conception of science is of a continuous, steady, upward climb of progress. The reality is not as simple. Highly signi!cant discoveries may often stay unrecognized for decades, if they con"ict with the current paradigm or extend it in ways hard to imagine at the time. Recently, we were bemoaning how important scienti!c signals get lost in the noise generated by the sheer volume of data and the dominance of the latest trend, whatever it may be. Once we started listing our own favorite unknown classics, and soliciting other titles from colleagues, we realized that there are substantially more than enough such forgotten, never-noticed, or ignored papers to !ll a book. [...]
Part II is a compilation of papers that we believe describe important ideas and results that are, as yet, not widely known or used. We do not claim certainty that all of these papers will someday earn renown or prove useful; our argument is only that the ideas presented are supported by data and deserve closer inspection. Our claim is that all of these papers raise important questions or describe novel and essential ideas. Some go against conventional wisdom, some point out the importance of testing assumptions, still others contain known facts that are underused.
In academic work, please cite this essay as:
Ricón, José Luis, “Peer rejection in science”, Nintil (2020-12-02), available at https://nintil.com/discoveries-ignored/.