The experience of Katalin Karikó, who was initially not supported by most scientists in her field, is not uncommon.
After analyzing a large number of examples of key scientific advances, mainly from chemistry and physics, Thomas Kuhn concluded (1) that innovative work is frequently opposed by researchers following the prevailing scientific paradigm. Kuhn analyzes many historical cases, including the classic examples of the initially reception of the work of Copernicus, Galileo and Darwin. He made clear that his theory also applies to small-scale innovations in specialized fields (1). Kuhn’s point of view has since being cited by many successful scientists, like Nobel winners Baruch Blumberg and Sidney Brenner, and National Medal of Science awardee Carl Woese (2-4) as helping them to understand the opposition they initially encountered. Baruch Blumberg wrote that his paper reporting the discovery of the hepatitis B virus (which had later a very large beneficial effect on human health, leading to blood screening and effective vaccination) was initially rejected and that his work was generally viewed with skepticism by experts in virology (2). He tells that after reading Kuhn’s book he could make sense of what was happening to him (2). Blumberg cites as an additional example the response to Carl Woese first announcing his discovery of the archea (2, 4).
One of the most important medical advances in the therapy of several cancers, the use of CAR-T cells, had to overcome substantial obstacles. Carl June, the immunologist, who led the development of CAR-T technology, encountered severe skepticism and setbacks, and the NIH wouldn’t fund a clinical trial. He had to look for philanthropic support for the first clinical trial (5).
The story of one of the early contributors to the development of CRISPR has been described (6):
“Recognizing the importance of the discovery, [Francisco] 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.”
An analysis of the development of a novel effective therapy for Chronic Myeloid Leukemia (CML) (7) reports that the process was delayed for many years by disagreements between different departments of the pharmaceutical company which participated in the development of the drug (7). Concerns were of a scientific and financial nature and were both later proved unfounded (7). A key role in advancing the clinical development of this therapy was played by Brian Druker (7).
According to his Nature obituary (8), Seymour Benzer, one of most influential scientists of the last century in multiple biological fields, used to say: “If everyone you talk to says you shouldn’t do something, you probably shouldn’t do it, and if everyone says you should do something, you should also probably not do it; but if half the people you talk to tell you to do it and half say you’re crazy, then you should definitely go ahead.”
An interview (9) with Harry Markowitz (Nobel Economics 1990, for his work on portfolio theory), describes his experience in 1954 with his examiner Milton Friedman (1976 Nobel in Economics): “When Mr. Markowitz defended his doctoral dissertation — a treatise on portfolio theory — Mr. Friedman raised a disturbing objection. Portfolio theory wasn’t economics, Mr. Friedman said, and the university couldn’t grant a degree in economics based on it. A few minutes later, Mr. Markowitz learned that he would receive his degree after all, but he endured some nervous moments. “
From an interview (10) with Barry Marshall (Nobel Medicine 2005, for determining the bacterial origin of many peptic ulcers) about their initial troubles in getting their work published and accepted:
"You can't rely on everybody else's opinion in science," he said. "Science is not a democracy. In fact, any new discovery in science is going to be controversial and initially most people won't believe it because you are going to be knocking over some kind of dogma - and that's where we were.”
The experience with reviewers of Mario Capecchi (Nobel Medicine 2007) has often been told (11, 12):
In 1980 Mario Capecchi sent a grant proposal to NIH and was told that the reviewers considered one of the projects as "not worthy of pursuit," “so Capecchi gambled and diverted money from other projects into the new research. If the gamble didn't pay off, Capecchi risked losing all his research funding, a death sentence for researchers in today's publish-or-perish universities. ... The professional gamble Capecchi took with his research funding in 1980 paid off, and he was on his way to harnessing the machinery of mammalian cells to precisely mutate any gene he wished. ... When he reapplied to NIH in 1984, the reviewers admitted their goof: "We are glad that you didn't follow our advice." “
Craig Venter (13) says the following about the initial reception of the genome shotgun sequencing method, which proved to be a key strategy for the sequencing of the human genome:
" ... we received the inevitable and expected reply from NIH on the Haemophilus grant application that Ham and I had submitted earlier that year. The score was low, and it had not even come close to being funded. The verdict of the reviewers reflected that of the genome community: like Waterstone, they thought what we were proposing (and unbeknownst to them, already putting in practice) would not work and was not even worth attempting. I did take some comfort from the NIH response in the (highly unusual) form of a minority report from a small group of peer reviewers who dissented from the majority view and believed that our program should be funded."
Leroy Hood, one of the pioneers of the technology used for automated DNA sequencing, said in an interview (14):
“When I was developing the automated DNA sequencer back in the early 1980s I remember putting in several major grants to NIH on this, and both of them received the lowest priority scores I have ever got. What they wanted was to be convinced that the instruments could really be done and of course in the beginning you don't know whether it can be done."
Stanley Prusiner (Nobel Medicine 1997) is the discoverer of prions, a new biological principle of infection.
He has said that many scientists were “very unhappy” when he published conclusions that violated accepted dogma. For years he felt “the long arm of the scientific community pressing down on me.” (15)
Fred Hoyle, an astronomer famous for his contribution to the theory of stellar nucleosynthesis, wrote (16): “To achieve anything really worthwhile in research it is necessary to go against the opinions of one’s fellows”.
Hoyle is however also well known for his rejection of the now standard "Big Bang" theory of cosmology, a term he coined.
Albert Einstein was employed as a patent officer in Bern from 1902 to 1909. In 1907 he had already proposed the special theory of relativity and published a series of key papers in 1905, which earned him the Nobel prize in 1922. In that year (1907) he was however turned down for a job as an unsalaried lecturer at the University of Bern. The head of Department, Aimé Forster, dismissed the relativity paper as incomprehensible (17).
Later in life Einstein himself could not be convinced by some aspects of quantum theory, by then (and certainly now) accepted by most other physicists. In a letter to Max Born he famously wrote (18):
“Quantum mechanics is certainly imposing. But an inner voice tells me that it is not yet the real thing. The theory says a lot but does not really bring us any closer to the secrets of the “Old One”. I, at any rate, am convinced that He is not playing at dice.”
More recently, the confirmation at CERN of the existence of the Higgs boson has been called the most important physical discovery of the century. The particle is named after Peter Higgs, who has received the 2013 Physics Nobel Prize for this contribution. Higgs original paper (19) was rejected by the journal Physics Letters. A detailed account (20) of the resistance Higgs encountered states: “To his dismay the article was rejected, ironically by an editor at CERN. Indignant at the decision, Higgs added two paragraphs to the paper and published it in a rival US journal instead. In the penultimate sentence was the first mention of what became known as the Higgs boson. At first, there was plenty of resistance to Higgs's theory. Before giving a talk at Harvard in 1966, a senior physicist, the late Sidney Coleman, told his class some idiot was coming to see them. "And you're going to tear him to shreds." Higgs stuck to his guns. Eventually he won them over. Ken Peach, an Oxford physics professor who worked with Higgs in Edinburgh, said the determination was classic Peter: "There is an inner toughness, some steely resolve, which is not quite immediately apparent," he said. It was on display again when Stephen Hawking suggested the Higgs boson would never be found. Higgs hit back, saying that Hawking's celebrity status meant he got away with pronouncements that others would not.”
Similar determination was shown by Mitchell (21):
“The Nobel Prize for Chemistry in 1978, awarded to Peter Mitchell as the sole recipient, recognized his predominant contribution towards establishing the validity of the chemiosmotic hypothesis, and ... the long struggle to convince an initially hostile establishment. ... The challenge of the upstart chemiosmotic hypothesis to the prevailing chemical view of mechanism was to become a running battle, in which Peter engaged the establishment single-handed for several years before the first of a growing band of brothers (and sisters) joined him in the fray.” Mitchell set up and independent lab with his family financial resources and was able to continue his work and prove his theory (22).
Andrew Viterbi, who was awarded the National Medal of Science in 2008 for the development of the Viterbi algorithm, tells that the publication of his first paper on his method was delayed for almost a year and that there was disagreement among reviewers about the opportunity of including the description of the algorithm that is now named after him (23). Viterbi’s work then led not only to important scientific and technological advances but also contributed to the founding of a major global telecommunication company, Qualcomm.
From an interview (24) with Sidney Brenner, (Nobel Medicine 2002):
“Now, you ask why did we accomplish so much? ... I think, first of all, in the early days of molecular biology, it was an evangelical movement. Most people were against us. Most of the biochemists didn’t understand the nature of the problems that we thought were interesting and important. They had a completely different set of attitudes. But we didn’t feel too upset by this. We all had, in fact, healthy disrespect for the establishment, and a group of us throughout the world got on with the work.”
In another book (25), about a later period, but still using the same metaphor, he wrote:
“ ... science goes ‘from the heroic period to the classic period’ as Gunther Stent used to say. Which is, of course, exactly where molecular biology stood in about 1961. There were no longer great heroes who were evangelists bringing a new message. Now the church was admitting everybody and everybody was becoming converted”.
Gunther Stent gave an insight (24) into the ethos of the group of scientists led by Max Delbruck that had a profound influence on molecular biology (as we also discuss in the History and Science section): “Delbruck’s ... role was essentially moral. ... All of the group, the so-called phage group, felt that way. So it created order. Now the point was that very often Max’s opinions were incorrect, and so it was also a test. You often had to do something against his views, but he would respect it. You would say ‘I want to do this’, and he would say ‘It’s nonsense. It will never show anything’. But one did it anyway, and if you could then show him good results, then he would of course immediately honor them. He would feel even better than against his advice, you had prevailed”. Delbruck is an important figure because before entering biology he was a physicist and a member of the Copenhagen school that started quantum mechanics, led by Niels Bohr. It has been commented (26) that “Delbruck had become a Bohr-like figure in the new field of molecular biology. ... He had created Copenhagen-like atmospheres for young biologists”. Quantum mechanics is a major achievement of modern physics, and the Copenhagen spirit, which encouraged open criticism and disagreement, is credited with fostering its birth and development (26).
One of the most influential scientific figures of the last century is Enrico Fermi (Nobel Physics 1938). Fermi wrote in 1933 a fundamental paper on beta decay, that he considered “the most important piece of work he had ever done or would ever do in his life”. The paper was sent to Nature and rejected, with the motivation “The conjectures are too removed from physical reality”. The paper was later published and is now considered “one of the cornerstones of elementary particle physics” (26).
Michael Bishop (Nobel Medicine 1989), in a autobiographical book (27) tells how he abandoned prematurely an experiment for which Temin and Baltimore later received the Nobel prize, due to “skepticism on the part of several of my older, more experienced colleagues”. He then writes:
“The discovery of reverse transcriptase [by Temin and Baltimore] was a devastating blow to me. A momentous secret of nature, mine for the taking, had eluded me. I grieved for months; I still grieve in weaker moments. I had learned three lessons the hard way. First, the outsider often sees things more clearly than the insider and should not be intimidated by his inexperience. Second, the scientist must trust her or his own imagination, even if, perhaps especially if, it runs counter to received wisdom. Third, there is no substitute for intellectual daring: if you want to rise above the pedestrian, you must be prepared to take risks.”
Hans Krebs (Nobel Medicine 1953). The article describing his most important discovery (the Krebs cycle) received a very polite rejection letter from Nature (28).
““This was the first time in my career, after having published more than fifty papers, that I experienced a rejection or semi-rejection,” Krebs wrote in his memoir.”
A Nature Editorial (29) about peer rejection and conservatism in science states:
“But there are unarguable faux pas in our history. 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. ...
We can take more respectable comfort from a little-celebrated positive accomplishment of editors, which is to champion submitted papers in the teeth of referees' (and sometimes colleagues') resistance. One such submission, according to his Nobel lecture, came from Thomas Cech. The three referees ("outraged enzymologists", as Cech described them) all opposed the idea that self-splicing RNA could be a catalyst, but Nature published it nevertheless.”
A paper listing many other examples of resistance by scientists to novel discoveries was published by Bernard Barber several years ago in Science (30).
The interviews with Robert Langer and Napoleone Ferrara described their experience conducting research that was initially not supported by the majority of their scientific community. Robert Langer acknowledges the help he received from two mentors, Judah Folkman at Harvard University and Nevin Scrimshaw at MIT (31,32). Napoleone Ferrara was discouraged from pursuing his work on angiogenesis in academia and when he was hired at Genentech was only able to continue it by taking advantage of an unusual policy that allowed scientists to pursue their personal scientific interests on weekends and during spare time.
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