“[We are] about to “break in” one or more staff members. This sounds like a somewhat violent process; and it is true that the almost unique character of the activities…makes indoctrination both difficult and necessary. The only real way to become experienced in this strange but marvelous business is through experience itself.”
Without more context, you’d be forgiven for thinking that the organization about to “break in” its staff members was a Silicon Valley tech company, perhaps, or a cult. But you’d be wrong — It’s an excerpt from a 1946 How-To guide for new program officers in the Rockefeller Foundation’s Natural Sciences Division.
During the 1930s-1950s, this division funded the revolution in molecular biology; the very term was first coined by then-director, Warren Weaver, in the Rockefeller Foundation’s 1938 Annual Report. In the dozen years after the discovery of DNA’s structure, in 1953, all but one of the 18 scientists who received a Nobel Prize for genetic molecular biology research had been supported by Weaver’s team at the Rockefeller Foundation (Foreword, Science and Imagination: Selected Papers of Warren Weaver).
If the Rockefeller’s Natural Sciences Division shaped and enabled the midcentury revolution in molecular biology, then studying their work is instructive for contemporary funding organizations aiming to similarly accelerate modern science.
Weaver’s team funded Linus Pauling and his development of a general theory of protein structure. They funded George Beadle and Edward Tatum, who discovered that genes act by regulating definite chemical events while studying the fungus, Neurospora, and for which they shared a Nobel Prize in 1958. And grants made to Salvador Luria and Max Delbrück helped them to demonstrate Darwin’s theory of natural selection in bacteria, for which they shared a Nobel Prize in 1969. Weaver’s team steered the cross-disciplinary application of then-recent advances in physics, chemistry, and mathematics to produce seminal discoveries in biochemistry, molecular genetics, and immunochemistry.
Notably, they didn’t achieve their funding success through the now-familiar approach of decentralized decision-making by a sprawling bureaucracy of study sections, program officers, and peer review. Weaver saw himself, instead, as a “manager of science.” He led his small team of program officers in a highly opinionated grantmaking process that focused on the organizational and social environments of research institutions over the specifics of any individual project. And once his team selected a field to focus on, it funded people over specific ideas.
Somehow, Weaver’s team did all of this with relatively little domain knowledge. Weaver’s background was in physics, and the program officers that he hired — and who crisscrossed the world and recommended scientists for grants — were rarely the top scientists in their field. At one point, Weaver even deflected an employment inquiry from Leo Szilard.
Weaver also avoided the temptation to exert his influence by insourcing funded research, as was commonplace at The Rockefeller Institute for Medical Research (now Rockefeller University). This allowed the Natural Sciences Division to back out of its grantmaking role once new fields and institutions had established themselves in their own right.
In this essay, I draw from the Rockefeller Foundation’s archives, particularly its program officer diaries, and other sources to explain how Weaver’s Division accomplished these remarkable feats, and what modern science philanthropy can learn from their success. I discuss Weaver’s background and role, and dissect his approach for building relationships with the scientific community; special emphasis is given to Linus Pauling and Max Delbrück.
Later, I explain how Weaver scaled his impact by hiring program officers and maintaining a harmonious relationship with the Rockefeller Foundation trustees, who controlled the purse strings. The essay ends with lessons for contemporary philanthropies with similar goals, including Arcadia Science, Convergent Research, and New Science.
But first, I highlight Weaver’s key Funding Principles; those fundamental things that made his team so successful in its day.
Several crucial takeaways from the Rockefeller Foundation, and their funding of molecular biology, are directly applicable to modern, life sciences grant-making organizations. Many of these takeaways mitigate the second- and third-order effects of grant-making, such as the ways in which grant recipients might adversely alter their actions in response to funding, or the potential of future funds.
Triangulate to excellence: Weaver’s officers lacked domain expertise across the ever-shifting research areas they funded, and so they developed heuristics to find researchers worthy of funding.
This is the most counterintuitive, yet useful, guiding principle. It is still applicable today. Science funding organizations that want to back high-caliber researchers, according to their own criteria, can efficiently locate them by repeatedly asking the right questions.
What to do: Natural Sciences officers would proactively ask independent experts in a given (sub)field, “Who is the best scientist studying X?”
What not to do: Natural Sciences officers were instructed not to reactively (in response to a grant application) inquire, “Is scientist Y a good candidate to receive funding to study X?”
Natural Sciences officers could move between subfields while incurring minimal switching costs. This allowed Weaver and his officers to adapt to the Rockefeller trustees’ shifting interests in different areas of research.
Weaver could recruit Natural Sciences officers without respect to their preexisting domain expertise, giving him flexibility to optimize along other axes instead.
Researchers who were reclusive or not highly regarded by their peers (for example, due to having non-consensus scientific views) were probably less likely to receive funding compared to their gregarious peers.
If one funds a specific subfield for extended periods of time, it is probably more efficient to develop a technical understanding of the space.
Hire foxes, not hedgehogs: If you asked anyone today who Harry Milton Miller, Jr., Gerard Pomerat, or Farnie Loomis were, they wouldn’t be able to tell you. But these are the men who identified and funded so many Nobel Prize-winning scientists.
What to do: Hire scientific foxes as your program officers. They will triangulate to success.
What not to do: Hire successful scientists as your program officers. Leo Szilard was rejected for a Natural Sciences officer position by Weaver in 1952.
Pro: Scientific foxes can be found and recruited from the same academic environment inhabited by grant recipients, thus allowing each program officer trip to double as a recruiting trip.
Con: Whereas the Rockefeller name was sufficient for program officers to stand out amongst scientists in Weaver’s day, a name of such singular prominence does not exist today. Having program officers of some scientific fame may be helpful for modern organizations.
Avoid creating long-term dependence: Weaver’s team took great pains to ensure that its grants did not make researchers dependent upon, or come to expect, continued Rockefeller funding.
For any contemporary private science funding organization, this is a critical principle of practical import. Large quantities of government funding are unlocked for fields of scientific inquiry once they become commonly accepted as worthwhile of study. Therefore, driving underfunded areas of inquiry into the mainstream of science is key to alternative funding efficiency.
What to do: Make grants contingent on the researcher’s demonstrated ability to obtain matching funds from third parties. This policy tests whether they will eventually be able to survive on their own.
Embrace relationship-driven grant-making, as long as it helps to eliminate indefinite dependence on Rockefeller Foundation grants. Back scientists and research that would entice other benefactors to provide matching and subsequent funding.
This very principle was included in Natural Sciences Notes on Officers’ Techniques (1946), and was emphasized to newly initiated program officers.
What not to do:
Give grants that cover the majority of a researcher’s salary. It isn’t easy to stop paying someone.
Allow grant recipients to designate junior personnel with the title of “Rockefeller Foundation Assistant” or similar.
“Make the peaks higher”: Carrying on a philanthropic principle established by John D. Rockefeller himself (see: The Story of the Rockefeller Foundation), Weaver’s team sought to reinforce naturally existing advantages amongst scientific institutions and investigators, so as to maximize the chance — and speed — that Natural Sciences grants would catalyze important advances.
This principle is a useful corollary to the first principle. Assuming that you have already found the scientists you want to fund, ensuring that their environment is also ideal makes their work more likely to succeed.
What to do: Create concentrations of researchers at specific institutions, rather than encouraging or allowing them to fan out.
Ex: Natural Sciences provided funding to Caltech in the late 1930s to build on Linus Pauling’s success by recruiting Thomas Hunt Morgan (from Columbia) and George Beadle (from Stanford).
What not to do: Natural Sciences did not provide much funding for biology research at Harvard, despite it being favored by the Rockefeller Foundation, because much of biology there sat in the shadow of Harvard’s dominant medical school.
By incentivizing collaborations between scientists at a single institution, such as Caltech, Weaver’s team implicitly lowered the barriers to new, out-of-the-box projects. This was particularly important, at the time, because long-distance communication was limited.
Grants for individual projects, the most scalable and repeatable vehicle of funding that Natural Sciences possessed, were not very useful for institution-building. Rather than delegating to his officers, Weaver was often personally involved in major grants.
Ex: The $350,000 grant to Caltech in 1936 for a center for molecular biology.
Stick to a fairly informal application process: Natural Sciences had no application forms for grants. Applicants were encouraged to organize their applications in whatever format made the most sense for them.
Although informal grant application processes remain unusual in science funding, this approach is widely used in other domains, such as by the tech startup accelerator, Y Combinator.
What to do: Natural Sciences officers often gave situational advice to specific researchers on what grant applications would be most likely to receive funding.
Example: Program officer, Frank B. Hanson, told Linus Pauling in 1934 that a grant application for x-ray crystallography of biological molecules would receive funding, while a similar application for inorganic molecules would not.
What not to do: Natural Sciences never required researchers to adhere to formalities in their applications
Contemporary example: the font size requirements of the NIH.
Preordained formats for applications would have constrained creativity and added friction for researchers, giving an advantage to academic bureaucrats over true scientists.
There were fewer opportunities to game the funding rules, particularly when Natural Sciences’ focus shifted from year to year.
In today’s scientific era — which is dominated by academic bureaucrats skilled at responding to hyper-specialized Funding Opportunity Announcements from institutions like the NIH — nimbler organizations have a massive advantage in funding high-value research proposals that inevitably slip through the gaps of government bureaucracy.
Con: This approach may not scale very well, as it is dependent on program officers skillfully reviewing informal ideas.
Natural Sciences funded $1.9M of experimental biology research in 1939, equivalent to $41M today. The NIH today funds 1000x that, or $40B/year.
Minimize the influence of salesmanship: Although no specific format or content was required for Natural Sciences grant applications, its officers were warned not to be drawn in by scientific salesmanship.
Although this seems logical, this is the hardest principle to enforce, since it requires constant vigilance and self-awareness.
What to do:
Enforce some form of a written application requirement.
Ignore verbal pleas in lieu of reviewing those applications.
What not to do:
Get taken in by a charismatic scientist.
This occurred to Weaver with Linus Pauling at times, culminating in Natural Sciences funding in vitro antibody production experiments in the early 1940s that proved to be shoddy science. Ultimately, Natural Sciences officer Frank B. Hanson cut Pauling’s funding.
To understand how these principles came to be, it’s important to understand the history of the Rockefeller Foundation’s Natural Sciences Division; where Weaver came from, what he looked for in program officers, and how he shaped his management philosophy.
Molecular Missionaries: A Brief History
Weaver’s Early Days
That so many breakthroughs in molecular biology were funded by grants emanating from within the four walls of the Rockefeller Foundation’s New York buildings was far from preordained when Weaver was named Natural Sciences director in 1932.
The numerous Rockefeller charities had just exited a tempestuous period of consolidation. Trustee Raymond Fosdick (future Rockefeller Foundation president and confidante of John D. Rockefeller Jr.) had pushed the organization away from its prior focus on societal initiatives, such as improving public health and promoting education. There had long been a secondary focus of funding academic research at institutions, but only with minimal involvement in the specifics.
Fosdick reconstituted the Rockefeller Foundation and pushed it to, instead, focus on funding the creation, diffusion, and application of scientific knowledge. Fosdick’s ultimate goal, as a Progressive social reformer, was to solve societal challenges by advancing science (see: Chapter 9 of Partners in Science).
Having spent almost his entire adult life immersed in the land-grant progressivism of the University of Wisconsin, Weaver wholeheartedly embraced Fosdick’s agenda upon his arrival. Weaver prepared a detailed program in natural and medical sciences, together with the Medical Sciences director, Alan Gregg (see Table 10-2). Weaver’s program largely adhered to Fosdick’s Progressive agenda, avoiding “science for science’s sake” (Chapter 10 of Partners in Science). A focal point of Weaver’s plan was “psychobiology” (now known as behavioral neuroscience), a field that attempted to unearth the physiological underpinnings of psychiatric and psychological phenomena.
However, Fosdick’s wrenching changes to Rockefeller philanthropy were not universally accepted by the trustees. Internecine strife persisted well into Weaver’s tenure, and placed his new proposals on shaky ground.
In late 1933, when former Rockefeller trustee, Simon Flexner, was tasked with reviewing the joint Natural Sciences/Medical Sciences program proposal, he took it as an opportunity to attack the very concept of “managing” science, and Weaver in particular. Flexner was a close confidante of John D. Rockefeller, Jr., a respected physician-scientist, and a former professor at the University of Pennsylvania. Weaver, by contrast, was a novice in life science research, and a newcomer to the Rockefeller Foundation and its hegemonic, Northeast social circles.
A Midwestern mathematical physicist who had never stepped foot in New York City before interviewing for the Rockefeller Foundation job, Weaver was now endeavoring to put his thumb on the scale of scientific inquiry by funding specific avenues of research that he deemed most worthy of philanthropic support. In particular, Weaver saw an opportunity to “create a new science of Man” by applying quantitative methods to biology, the study of which had, until then, been largely descriptive (see: Chapter 10 of Partners in Science).
However, Weaver’s vision for, and evident skill in, cross-disciplinary research administration was not hastily formed upon his arrival at the Rockefeller Foundation. In the years immediately preceding his move to New York, Weaver had been involved in an attempt at the University of Wisconsin to create an interdisciplinary geophysics research center that pulled together several departments. This small-scale experience in the management of cross-disciplinary academic research proved fortuitous for Weaver when he received a call from Rockefeller Foundation President Max Mason to join him at the philanthropic giant.
Upon arriving in New York, Weaver worked with Fosdick to put his ideas to paper. But Weaver’s initial reports to the trustees hurt, rather than helped, his case. Weaver wanted the Rockefeller Foundation to play a still-controversial active role in planning and directing scientific research.
Fortunately for Weaver and his proposal, the tide had turned in broader society by the 1930s. The hardships of the Great Depression had highlighted the limits of the laissez-faire thinking of the 1920s, bringing to the fore a generation of New Dealers who believed they could manage society to superior outcomes (see: Scientists in the new deal: A pre-war episode in the relations between science and government in the United States).
When Fosdick consulted David Edsall, dean of Harvard Medical School and a member of the Rockefeller Foundation board’s executive committee, for thoughts on Weaver’s program, Edsall strongly supported both the cross-disciplinary bent and the active scientific management to be performed by Rockefeller Foundation officers.
Max Mason brought prominent natural scientists, Frank R. Lillie and Walter B. Cannon, onto the Rockefeller Foundation’s Committee of Appraisal. This committee had been formed by Fosdick a year earlier to provide oversight for Foundation officers and their programs on behalf of the trustees, who felt poorly equipped to evaluate the new scientific focus areas, compared to the Foundation’s earlier focus on public health and educational initiatives.
Both Lillie and Cannon attested to the benefits of programmatic research, allowing Weaver to fend off Flexner’s attack. When Weaver presented his five-year program proposal to the board of trustees in late 1933, he won their approval (see: Chapter 10 of Partners in Science).
Over the two decades that followed, Weaver’s division would provide more than $23M in grants as a part of their experimental biology program, ultimately funding nearly every scientist who would go on to win a Nobel Prize for research in molecular biology during the 1950s and 1960s.
Pauling and Caltech
Weaver wasted no time putting his agenda into practice. He swiftly funded Linus Pauling’s x-ray crystallography work at Caltech, and pushed Pauling to direct his methods toward the biological world.
Pauling had begun x-ray diffraction studies of crystals in 1922, when he first arrived at Caltech as a PhD student. By 1932, Pauling extended his techniques to deduce the molecular structure of organic compounds, such as urea and carboxylic acids, and to demonstrate the resonance of amide groups. Much of this pioneering work relied on Rockefeller Foundation funding provided before Weaver’s arrival at the philanthropy (Brief Account of Research in Chemistry Supported by Grant from the Rockefeller Foundation).
It was during his visit to Caltech in October 1933 that Weaver first introduced Pauling to the new Natural Sciences agenda. Pauling responded by writing up a grant proposal and sending it to Weaver’s team. In that proposal, Pauling laid out his plans to apply x-ray crystallography to biological molecules, such as hemoglobin and chlorophyll.
Weaver funded the proposal in the form of $10K for the following academic year. Eschewing a multi-year grant for the time being, the Foundation first wanted Pauling to demonstrate his commitment to Natural Sciences’ new program of cross-disciplinary research (see: The Molecular Vision of Life, Chapter 5).
Giving Pauling only 12 months of runway appears particularly prescient in hindsight. He moved with alacrity to study the structure of hemoglobin, a protein still poorly understood despite its central importance to life and medicine. Within eight months, Pauling had discovered that the chemical formulas reported in the literature for hemoglobin were incorrect.
Early results in hand, Pauling moved in September 1934 to expand the Rockefeller Foundation’s support for his research program, which encompassed not only the x-ray crystallography hemoglobin research, but also parallel pursuits to elucidate the structures of inorganic compounds. However, Weaver’s division was now focused solely on advancing “the science of Man,” and so he pushed Pauling to pursue research that Weaver himself felt to be most important.
At the same time, Weaver knew it would be disruptive to simply cut funding off for Pauling’s ongoing, inorganic research agenda. The goal, as with all Natural Sciences grants at the time, was to enable preliminary work that could later be expanded into standalone institutes and research fields. Weaver wanted to wean Pauling off of Rockefeller Foundation support, and so rejected Pauling’s request and tasked him with finding an alternative source of funding (Pauling to Weaver, Sept 1934).
Weaver soon found a way to simultaneously achieve all of his goals. Natural Sciences officer Frank B. Hanson visited Pauling in November 1934. The two men came to an agreement: Pauling would try to convince Caltech’s President, Robert Millikan, to provide $5K each year (of Caltech funds) to support his inorganic research agenda. In return for that commitment, Weaver’s team would provide $10K/year for Pauling’s organic research. Moreover, the longer the commitment that Pauling could extract from Caltech, the longer the commitment from Weaver (FBH 1934 diary).
The following week, Weaver sent a letter to Pauling and notified him that an extended commitment from the Rockefeller Foundation was contingent on the Caltech contribution (Weaver to Pauling, Nov 23 1934).
Pauling soon persuaded Millikan, who agreed to a three-year commitment. With funds in hand, Pauling responded to Weaver’s letter the same day it arrived and told him about Caltech’s support (Pauling to Weaver, Nov 1934). This led to a three-year (1935-1938) Natural Sciences grant renewal for Pauling’s organic research agenda, at the agreed-upon $10K/year.
This longer-term funding enabled Pauling to continue his hemoglobin studies in the laboratory. During this time, he developed magnetic methods capable of measuring free oxygen with greater sensitivity. Using those methods, Pauling empirically demonstrated that hemoglobin oxygenation involved the formation of covalent (not ionic) bonds, in contravention to what might have been expected from theory. The application of physical science techniques to the interrogation of living systems, as Weaver and Fosdick had sought, was beginning to pay off.
By the summer of 1935, Pauling was applying the Gouy method to ascertain the magnetic susceptibility of hemocyanin obtained from keyhole limpets at Caltech’s marine laboratory in Newport Beach. That work led to Pauling’s landmark 1936 publication on the magnetic susceptibility of hemoglobin, in which he distinguished between arterial (oxygenated) and venous (deoxygenated) blood. Those discoveries would eventually lead to the first ever characterization of the molecular basis of a genetic disease, sickle-cell anemia, in 1949 (Sickle Cell Anemia, a Molecular Disease).
But word of Pauling’s progress reached Natural Sciences long before any of it had been published. Pauling visited Weaver in New York in April 1935 and shared updates on his research progress. While there, he piqued the attention of leading protein chemist, Alfred E. Mirsky (of the Rockefeller Institute for Medical Research), who had previously studied the reversibility of protein denaturation.
A few months after Pauling’s visit to New York, Mirsky took a sabbatical to join Pauling in California for the 1935-1936 academic year. During that time, they jointly produced a general theory of protein structure that included the crucial role of hydrogen bonds in stabilizing the tertiary structure of polypeptides (see: The Molecular Vision of Life, Chapter 5).
Why begin a history of Weaver’s tenure, and the rise of molecular biology, with Pauling? For two reasons.
Pauling’s work at the intersection of physics, chemistry and biology laid much of the groundwork for later advances in molecular biology, including the discovery of the structure of the DNA helix and proteins. And because Weaver’s investments in Pauling were so immediately impactful, their success amplified contributions to scientific research by sources outside of the Rockefeller Foundation.
Riding Pauling’s string of success, the Caltech chemistry department chair, Arthur Noyes, persuaded local steel magnate, Edward Crellin, to provide $350,000 for the establishment of a center for molecular biology in 1936. What started as a one-time $10K commitment for molecular biology research had quickly expanded by more than an order of magnitude.
Crellin’s funds, and the state-of-the-art facilities they enabled, played a key role in the recruitment of luminaries such as Thomas Hunt Morgan, Max Delbrück, and George Beadle to Caltech. Although each of those scientists was impressive in his own right, it was evident that Rockefeller’s Natural Sciences team was conscious of the broader institutional milieu inhabited by their grantees.
Caltech provided an ideal environment for institution-building. Compared to other leading research institutions, such as Harvard, Columbia, or Stanford, Caltech has no medical school. This meant that life science research at Caltech could stand on its own — basic research for the sake of advancing science — rather than exist in the shadow of medicine.
Additionally, as a young institution, Caltech benefited from a distinct lack of competing, disciplinary traditions. Its closest competitor, the University of Chicago, also enjoyed robust Natural Sciences support in the early 1930s — biochemist F. C. Koch, geneticist Sewall Wright, and biologist Paul Weiss were all funded by Weaver’s team. However, by the late 1930s, many of Chicago’s prominent life sciences faculty members were approaching retirement, and the university was undergoing administrative reshufflings that would impact new faculty appointments and orient its life sciences research towards the clinic. Weaver’s team soon focused their grants elsewhere.
The lack of traditions at Caltech allowed its faculty to establish new ones. Max Delbrück’s phage group taught summer courses on physics- and math-focused approaches to biology to young scientists at Cold Spring Harbor from 1945 to 1970. Their teachings spread a ‘new’ kind of quantitative biology to institutions around the world (The Cold Spring Harbor Phage Course (1945-1970): a 50th anniversary remembrance).
However, Delbrück had been in much humbler circumstances when the Natural Sciences Division first sought to invest in him. A mediocre theoretical physicist who had failed the oral examination for his PhD at the University of Göttingen on his first try in 1929, he did not have a particularly bright future in physics. As contemporaries like George Gamow, Lev Landau, and Eugene Wigner were publishing notable research, Delbrück bemoaned his lack of success (Ordinary Geniuses, Chapter 6).
However, good fortune struck when Delbrück received his first Rockefeller Foundation grant in 1931, which he used to study with the famed theoretical physicist, Niels Bohr, in Copenhagen. Although Bohr was a physicist by training, he harbored a deep interest in biology, particularly the relationship of biological phenomena to the physicochemical phenomena that had been unraveled in recent decades. During his fellowship in Copenhagen, Delbrück recognized an opportunity to tread new scientific territory (Creating a Physical Biology).
Upon completing the Rockefeller Foundation fellowship with Bohr, Delbrück faced a pivotal decision: either become famed physicist Wolfgang Pauli’s research assistant in Zürich, and dedicate all of his energy to physics, or return to Berlin and join the Kaiser Wilhelm Institute for Chemistry. Although the latter path would not involve working with a luminary like Pauli, it would present a unique opportunity to freely collaborate with then-leading biologists in Europe, including geneticist Nikolai Timoféeff-Ressovsky and radiation biologist Karl G. Zimmer.
Delbrück chose the latter path and wrote to Bohr: “I have accepted Lise Meitner’s offer to go to Dahlem [in Berlin] as her ‘family theorist’ largely because of the neighborhood of the very fine Kaiser Wilhelm Institut für Biologie” (Ordinary Geniuses, Chapter 8).
Delbrück was soon making crucial advances in biology. For his seminal 1935 paper, “On the Nature of Gene Mutation and Gene Structure,” Delbrück induced mutations in bacteria and Drosophila with radiation. The paper was co-authored with Timoféeff-Ressovsky and Zimmer. And though its conclusions, largely, did not stand the test of time, it set the precedent for a model of cross-disciplinary collaboration between the physical and life sciences that was essentially unheard of at the time (Creating a Physical Biology).
When program officer Harry Milton Miller, Jr., a globetrotting parasitologist from Baltimore who oversaw Natural Sciences’ international fellowship program for three decades, visited Bohr in January 1935, Bohr requested that Natural Sciences fund a second fellowship for Delbrück to return to Copenhagen. Although Miller deflected the request for funds (Bohr, evidently, could have funded the fellowship for Delbrück himself), Bohr’s admiration towards the younger scientist was clearly well-known to Rockefeller Foundation officers (see: HMM diary, first half of 1935).
Thus, when Miller arrived at the Kaiser Wilhelm Institute in October 1936 to find Delbrück reading a book on biomathematics by the English statistician and biologist, R.A. Fisher, he sensed an opportunity to once again further the Natural Sciences program agenda through Delbrück.
Miller immediately suggested a second Rockefeller Fellowship for Delbrück, this time to study with Fisher in London. Delbrück was receptive to the proposal but, after thinking it over, instead suggested to Miller that the fellowship be with famed geneticist T.H. Morgan, at Caltech. Miller accepted (see: Interview with Max Delbruck, 1978). For Natural Sciences, the specifics didn’t matter so much as drawing Delbrück further into the Rockefeller orbit.
What started as a fellowship at Caltech for Delbrück turned into a close association with the Natural Sciences Division for the rest of his professional career. When Weaver checked in with Morgan in February 1939, Morgan spoke highly of Delbrück, describing him as a physicist who “really understands biological problems” (WW diary, 1939-1940).
Delbrück, for his part, told Weaver that he had no desire to return to Europe, which was inching ever closer toward war. With the Caltech fellowship expiring later that year, Weaver took responsibility for finding a new academic home in the U.S. for Delbrück. In September, whilst paying a visit to Chancellor O. C. Carmichael at Vanderbilt University, Weaver discovered that a physics faculty vacancy through retirement was only a few years out. Weaver obtained an agreement from Carmichael to make that faculty position immediately available for Delbrück. In return, Weaver’s team gave Vanderbilt University interim funding to support Delbrück’s appointment.
In classic Natural Sciences fashion, Weaver had engineered a desirable outcome without incurring an indefinite financial commitment (WW diary: 1939 - 1940). Sure enough, Delbrück joined the faculty at Vanderbilt the following year. While there, he collaborated with Salvador Luria, leading to their 1969 Nobel Prize in Physiology or Medicine for “discoveries concerning the replication mechanism and the genetic structure of viruses.”
The Rockefeller Foundation’s desire to stay in the background as Natural Sciences grant recipients went on to reshape humanity’s understanding of living systems means that, to this day, surprisingly little is publicly known about the peripatetic officers who made it all possible. A deeper understanding of where they came from and what drove them will be helpful for modern grant-making organizations seeking to emulate facets of the Rockefeller model.
Natural Sciences program officers had an appealing job. Their grants made important contributions to the advancement of science, the Rockefeller Foundation was an extremely prestigious employer, and program officers traveled frequently and flitted amongst leading scientists.
Many of the scientists with whom Weaver came into contact through the course of his work asked about joining him, and this was precisely how Weaver sourced most of his officers. Although it was unrealistic (and unnecessary) to expect an officer to possess domain expertise in any specific research areas, the most important criteria for a new hire were: broad familiarity with the topography of contemporary scientific research, and a deep understanding of the mores of the scientific community (see: How Knowledge Moves, Chapter 9).
Successful program officers required a moderate depth of understanding across a dizzying variety of fields, too. During his first five years in New York, Weaver taught himself genetics, cellular physiology, organic chemistry, biochemistry, and developmental biology (Scene of Change: A Lifetime in American Science by Weaver).
And, much like Weaver, none of the Natural Sciences program officers were well-known or had distinguished scientific careers. The unique combination of scientific and social aptitude possessed by a skilled program officer made them much more like foxes than hedgehogs (Rockefeller Bureaucracy and Circumknowing Science in the Mid-Twentieth Century). As Freeman Dyson aptly pointed out many decades later, scientific progress is dependent on these two types of scientists playing complementary roles (A Many-Colored Glass: Reflections on the Place of Life in the Universe, 2007).
When prolific physicist, biologist, and inventor Leo Szilard inquired with Weaver about a program officer job in March 1952, the answer was no—other scientists had already been selected (Leo Szilard Papers, Warren Weaver letters). Although they might not have been as successful as Szilard as scientists, they were much better fits for this particular role.
Other Natural Sciences officers included:
William Farnsworth “Farnie” Loomis, who came from an illustrious, medico-scientific family. He was the great-grandson of Alfred Lebbeus Loomis, who established one of the first clinical labs in the U.S. to diagnose illnesses of microbiological origins, and was the son of Alfred Lee Loomis, who developed the LORAN system for long-range, aerial navigation. Farnie taught himself biochemistry from scraps of textbooks mailed to him by his mother while serving as an OSS physician during WW2, where he parachuted into China behind Japanese lines (Hydra: Research Methods). It was during Farnie’s stint as a research associate in Nobel Prize winner Fritz Lipmann’s lab, in 1949, that Lipmann recommended him to Weaver for a job (see: WW 1949 Officer’s Diary).
Gerard Roland Pomerat also came from a medico-scientific family. Born in 1901 in Massachusetts, he was the son of a medical doctor, Charles Marius Pomerat, who originally hailed from France. After completing a PhD in cytology at Harvard in 1940, Gerard taught at the university until joining the Office of Scientific Research and Development (OSRD) during WW2 (source: Des savants aux chercheurs). His brother, Charles Marc Pomerat, was a zoologist and Rockefeller Foundation Traveling Fellow in 1937-1938 (source: American Men of Science), during which he worked in Buenos Aires with Nobel Prize-winning physiologist, Bernardo Houssay (source: FBH diary, 1937). As OSRD wound down after WW2, Gerard was recruited by Weaver as a Natural Sciences officer to help revitalize postwar European science. Gerard put the French he had picked up from his parents to good use. As with Loomis, Gerard was not a brilliant scientific mind in his own right, but his background and life experiences helped him to engage with scientists and drive Natural Sciences funding activities.
Trustees & Oversight
While Natural Sciences officers chose specific grants to recommend for funding, final decisions were made by the Rockefeller Foundation trustees, and not by the officers or by Weaver.
Rockefeller Foundation trustees, drawn from the leadership of government and industry, rarely had scientific expertise (Simon Flexner, Weaver’s nemesis, was a notable exception). John Foster Dulles was a typical Foundation trustee. A partner at the white shoe law firm, Sullivan and Cromwell, Dulles served on the Rockefeller Foundation board from 1935 to 1952, and then left to become Secretary of State. Trustees Henry Allen Moe and Raymond Fosdick similarly possessed legal and/or political experience (The Story of the Rockefeller Foundation).
Prior to the late 1920s, the Rockefeller Foundation primarily funded specific social and public health initiatives, which the trustees were well-placed to evaluate. But even after the Foundation’s grant-making focus shifted in the 1920s to scientific research, the trustees’ ideological and economic positions continued to influence Natural Sciences funding policies, sometimes going so far as to impact specific grant-making decisions. As such, trustee approval was always top of mind for Weaver’s program officers (The Molecular Vision of Life: Caltech, the Rockefeller Foundation, and the Rise of the New Biology, p10).
Deep involvement by the trustees had some advantages; a significant number of them held positions in university administration (The Molecular Vision of Life: Caltech, the Rockefeller Foundation, and the Rise of the New Biology, p6). Harold W. Dodds, for instance, was Princeton President from 1933 to 1957 and a Rockefeller Foundation trustee from 1936 to 1955, while Ernest M. Hopkins was Dartmouth President from 1916 to 1945 and a trustee from 1928 to 1942. Such overlaps in responsibility unquestionably assisted Weaver’s program officers in their efforts to triangulate toward scientific excellence.
That triangulation frequently involved independent, third party assessments, as well. In a sense, program officers conducted a sort of “rolling peer review” of their grantees, and focused much more on holistically evaluating scientists rather than any specific publications. In cases of unequivocally negative feedback, officers did not hesitate to pull funding, as they were always cognizant of the trustees’ watchful eyes.
For example, Natural Sciences funding for Linus Pauling’s immunochemistry research was largely cut in the early 1940s after program officer, Frank Blair Hanson, identified problems with Pauling’s work (FBH diary, 1943; FBH to Pauling, May 1943), which claimed to have resulted in the first ever in vitro manufacture of antibodies, to Pneumococcus polysaccharides (Pauling and Campbell, 1942).
Hanson solicited the opinions of immunologist Karl Landsteiner and bacteriologist Oswald Avery, while Miller consulted immunologist Michael Heidelberger. Although reluctant to openly disavow Pauling’s work in immunology, all scientists cast doubt on its reproducibility, given Pauling had not published details of controlled experiments (The Molecular Vision of Life: Caltech, the Rockefeller Foundation, and the Rise of the New Biology, p181-182).
Even a scientific giant such as Pauling, working in a field that was then central to the Natural Sciences research agenda, was not immune to the loss of Rockefeller Foundation funding.
From its grantmaking patterns, it is clear that the Natural Sciences funding style incentivized and enabled quick progress in specific areas of inquiry where opportunities to advance the scientific frontier had gone unfunded. This approach required that Weaver’s officers adopt an opinionated and ever-shifting focus. Unlike many other scientific research and funding institutions, program officers benefited from being able to simply present themselves to grant recipients as being from “the Rockefeller Foundation”—an appellation that required no further explanation. And by belying an explicit interest in any particular field of science, Weaver’s team retained optionality to shift its focus over the decades, as it did from the late 1930s (biochemistry) to the early 1940s (immunochemistry) to the late 1940s (phage biology) to the 1950s (nucleic acids).
This characteristic distinguishes the Natural Sciences Division from the government funding agencies that mushroomed in size in the second half of the 20th century.
Knowing that Natural Sciences’ support would not last forever, scientists were incentivized to produce rapid results that they could then wield to supplant Rockefeller dollars with funding from other benefactors. Indeed, by the early 1950s, more than half of Natural Sciences dollars were directed to its program in agriculture (which played a key role in the Green Revolution), rather than its program in experimental biology.
Changing focuses and long-term impacts are not exclusive. Weaver’s team sought to ensure that their grants enabled rapid progress and would later lead to independently sustainable centers of scientific excellence. The Rockefeller team preferentially selected scientists (such as Pauling) and institutions (such as Caltech) that were adept at obtaining outside sources of funding. Equally important, scientists who sought to bring their peers, especially junior colleagues, along were rewarded, as in the case of Delbrück’s phage group.
However, these strategies could be vulnerable to exploitation by charismatic personalities, who improperly commandeered third party funds. Pauling’s in vitro antibody manufacturing claims in 1942 were a good example of this failure mode. Natural Sciences officer, W. F. Loomis, was referring to this incident (and others like it) when he later remarked that Pauling had “gone off the deep end in some cases…he has no further worlds to conquer in straight science, so why not shoot at the moon…” (WFL diary, 1951)
Despite the preeminence of the Rockefeller Foundation in mid-century elite circles and the success of its Natural Sciences Division, science funding in America took an entirely different turn after WW2.
Vannevar Bush, who had led the wartime OSRD efforts to create atomic weapons through the Manhattan Project, sought to apply a similarly heavy-handed approach to the establishment of the postwar scientific order. In his famous July 1945 report to President Truman, “Science, The Endless Frontier,” Bush advocated for the creation of a new federal agency (the National Science Foundation) that would fund the creation of new scientific knowledge and the development of scientific talent—the very role that Weaver and his officers had been playing in the burgeoning field of molecular biology for the past decade.
A few months later, Weaver penned a New York Times editorial, forcefully refuting the foundational premise of Bush’s proposal—that top-down federal government funding should play a primary role in funding basic science research. Weaver drew a distinction between, on the one hand, successful, but temporary, efforts to apply basic science advances to wartime aims and, on the other hand, the process by which those underlying basic science advances were achieved in the first place. It was an ironic twist, given that Weaver had been similarly accused of attempting to exert top-down influence on basic science research, and to point it in a more societally relevant direction, by Simon Flexner just a decade earlier.
But Weaver’s pleas came too late—the wheels of government had already been resolutely set in motion. In subsequent decades, top-down funding for basic science research by the federal government came to dominate American academia, reaching heights of more than 70% of all dollars during the 1960s and 1970s. Although that percentage subsequently receded to 50%, contemporary science funding still largely occurs through NSF/NIH-style decentralized bureaucracies, rather than the shoe-leather methodology of Weaver and his band of Natural Sciences program officers.
As Weaver pointed out in his 1945 op-ed, industrialized science would be unlikely to rapidly yield nonlinear, basic science advances. Indeed, one of the biggest wins of government-funded life science research over the past half-century — the Human Genome Project — required 30 years (from 1990 to Jan 2022) of bureaucratic persistence to push forward a largely symbolic effort that has primarily produced indirect value through tool creation (low-cost sequencing, fluorescent dyes, and computer software for genomic analysis).
Shining a very bright spotlight on a centrally defined and heavily funded goal, without intrinsic urgency or deadlines, inevitably caused the Human Genome Project to be plagued by political infighting and schisms, such as Craig Venter’s attempts to privately sequence the human genome (The Genome War).
Although Venter’s efforts did push more scientists to adopt his efficient, shotgun sequencing approach, a less top-down Human Genome Project might well have fostered the intellectual freedom for alternate sequencing methods to be discovered, tested, and adopted in a less acrimonious manner.
A government-directed scientific accomplishment frequently compared to the Manhattan Project, Operation Warp Speed (OWS) was rapidly successful because it sought to achieve a clearly defined set of goals (testing, manufacturing, and distribution of COVID-19 vaccines at population scale) while operating under an extreme level of societally accepted urgency (a severe ongoing death toll from the COVID-19 pandemic).
Instead of making new basic science advances itself, OWS rightly focused on industrializing those advances (namely mRNA vaccine technology) that had been made in prior decades by a subset of the scientific community and which had faced intense skepticism and, thus, received limited financial support from the government (A Shot to Save the World).
Is there an opportunity to apply the principles that drove the Manhattan Project and OWS to far more initiatives that are a poor fit for government facilities, university research labs, or venture-backed startups?
The non-profit Convergent Research seems to think so—it’s convinced Schmidt Futures and the Astera Institute to fund a new type of entity, termed a Focused Research Organization (FRO). Each FRO is a scaled-down version of the Manhattan Project/OWS that receives $20-100M over a predetermined time period (usually ~5 years) to engineer a solution to a clearly defined, scientific challenge. The solutions generally take the shape of technique development or platform creation, producing public goods that can then be used by researchers (Unblock research bottlenecks with non-profit start-ups).
As Convergent, Arcadia, New Science, and others work to reshape science funding and innovation, they should remember that:
Natural Sciences’ principles for science funding were of their time.
The social environment of science and science funding at that time played a key role in the heuristics developed and followed by Weaver and his team.
The Rockefeller Foundation’s preeminent role in midcentury philanthropy opened doors all over the world for its program officers. This facilitated the intelligence gathering activities that drove funding decisions.
The scientific landscape has fundamentally changed since Weaver’s time.
Federal government funding now has an inexorable cultural influence on life sciences research and researchers (source: New Science's Report on the NIH).
New information and communication technologies enable far more seamless scientific communication and information dissemination.
A wide variety of private funders are exploring different science funding models.
Nonetheless, many of Natural Sciences’ principles were based on basic human psychology and incentive design.
Although the shape of contemporary science funding organizations will undoubtedly differ from the machine that Weaver created and oversaw, the opportunity to “create a new science of Man” presents itself in much the same way Weaver envisioned when he arrived at RF nearly a century ago.
About the Author
Samir Unni is an NYC-based technologist building products that help improve human health and our understanding of living systems. Follow him at https://twitter.com/SamirUnni.
Edited by Niko McCarty
Thanks to Sasha Targ and Alexey Guzey for reading a draft of this essay.
Cite this essay:
Unni, S. “Molecular Missionaries: How the Rockefeller Foundation revolutionized biology.” newscience.org. 2022 August. https://doi.org/10.56416/480pmz
Extraordinarily fascinating read!
Serendipitously, I just reached the section of The Wizard and The Prophet that discusses the Rockefeller Foundation's role in funding and directing the Mexican Agricultural Program. Landing upon this essay could not have been timed better.
Thanks for your immense research and writing.