Edwin Cohn, a temperamental and entrepreneurial protein chemist working at Harvard University in the early 1900s, is perhaps one of the most underrated translational scientists of all time.

In 1940, with the likelihood of America’s involvement in World War II steadily rising, the U.S. military approached Cohn about developing medical products from blood proteins to treat shock and blood loss in soldiers. Cohn’s team quickly invented methods to make blood albumin, which had a notable positive impact on soldiers’ survival from the earliest days of the American war effort. During the Normandy beach landings, many wounded soldiers were treated with Cohn’s albumin products. And, by the end of 1945, his Harvard team of scientists were so effective at turning lab discoveries into commercial-scale products that millions of Cohn’s blood products were used in all theaters of the war effort.

Cohn’s success is all the more remarkable today because, prior to the war, he rarely considered “applied” research, instead favoring theoretical work on the molecular properties of proteins. Ever the purist, Cohn was once described by James Conant, Harvard’s president, as “hopelessly high hat about all but ‘pure’ or ‘basic’ research.” In the first few months of the war, however, Cohn transformed his lab by introducing a pilot plant on Harvard’s campus and urging his team to grow their beaker-scale experiments from the bench all the way up to pilot-scale processes in 200L stainless steel tanks. Cohn’s team made vials of concentrated albumin solution that were more stable than plasma when stored in hot temperatures and, unlike dried plasma, could be immediately administered in dire situations without reconstitution.

The same team also invented several other products that proved useful for treating battlefield injuries, including gamma globulins to inoculate soldiers against diseases and fibrin film to minimize bleeding during brain surgeries.

Unfortunately, clinical results for many blood products made by Cohn’s team were inferior to other available treatment options, and perhaps that’s why his contributions to science have generally been forgotten. Human albumin administered to treat blood loss in soldiers was more shelf stable than, but clinically inferior to, both plasma and whole blood. In the decades following the war, more conventional vaccines were also developed for the same diseases which gamma globulin inoculated against — measles and Hepatitis A.

Still, Cohn’s work ought to be iconic amongst those interested in scientific progress and metascience. Before the war, his lab's work was characterized by one funder as, "painstaking, abstruse, and likely only slowly to come to widespread recognition for its essential importance." But in just a few short years, this same lab became one of the great translational R&D groups of all time. While Cohn’s methods are outdated, the wisdom of his approach is evergreen.

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Cohn’s story can serve two practical purposes for those interested in new science organizations. First, the case study of Cohn’s career should serve as a playbook for field strategists — people who design research targets, garner resources, and rally scientists to solve big problems. And second, the transformation of Cohn’s lab and its subsequent success highlight an exciting opportunity for research funders and entrepreneurial scientists.

For a well-chosen area of R&D, the story of Edwin Cohn shows what’s possible when you combine a pilot plant, funds, and vision to pursue a worthwhile problem. Circumstance found Edwin Cohn, and he made the most of his opportunity. Since many problems are too important to be left to chance, we would do well to enable more scientists to emulate Cohn’s approach to translating lab-scale success into industrial-scale impact.

Cohn the Purist

Cohn did not begin the war work that would later earn him national acclaim until his late 40s. Before that, he was not a man who thought seriously about how his research might later be applied. Instead, Cohn pursued science for the sake of understanding. His Harvard colleagues knew this about him; the Harvard President knew it; and even the head of the Rockefeller Foundation’s Natural Sciences Division knew it.

Cohn’s work consisted of "painstaking and abstruse" studies of proteins, protein components, and their properties under various conditions, according to Rockefeller Foundation staff. His lab was expert at honing fine-tuned processes to both isolate and analyze proteins, which were not yet thoroughly studied at the time. Prior to World War II, Cohn produced papers with obscure titles such as, "On the Swelling of Protein Colloids," "The Molecular Weights of Proteins in Phenol," and even "The Isoelectric Points of the Proteins in Certain Vegetable Juices."

In fact, before 1939, Cohn made just two noteworthy detours from his team’s fundamental investigations. The first detour came during World War I, when Cohn was asked to study the physical chemistry of bread-making. America was experiencing wheat shortages, so the government sought to find ways to make bread with various grain substitutes. Cohn’s second detour, however, was more noteworthy; for it marks the first time he began to show flashes of applied research genius.

In 1926, one of Cohn’s academic colleagues at Harvard Medical School discovered that patients suffering from pernicious anemia, a form of vitamin B12 deficiency, could be cured by eating liver. At the time, the U.S. mortality rate from vitamin B12 deficiencies was about 5 in 100,000. So with the effectiveness of the treatment proven, the next step was to isolate and purify the active agent in the liver curing the anemia. This would allow patients to consume a concentrate or injection of the substance instead of eating large amounts of liver daily. Cohn, known to be adept at distilling and purifying molecules for lab study, was asked to take up the task by his Harvard Medical School colleagues.

This was not a typical project for Cohn's team. As Cohn's biographer, Douglas Surgenor, once wrote, Cohn was known to have a "disdain for anything but pure scientific research." But several factors likely convinced him to take part, including the potential to save lives and garner prestige — friends and family have noted that Cohn cared quite a bit about the latter. Surgenor framed the situation as follows:

The successful isolation of the active principle in pernicious anemia would be an achievement fully as significant as the successful isolation of insulin from the pancreas by Banting and Best only five years before. Banting had won the Nobel Prize in Medicine in 1923 for that discovery and was knighted by the King of England.

In 1926, Cohn and a handful of young associates began to isolate and purify the curative molecule from livers. Within a few months, they developed a purified liver extract in which a 9 to 14-gram dose, given orally, could achieve results in ill patients similar to eating 200g to 400g of cooked liver. Over the next three years, Cohn and his team — several of whom would work with him through World War II as professors and technicians — dramatically increased both the purity and potency of these extracts.

The following graph shows the team’s progress; constant tinkering to the extraction process eventually yielded massive decreases in the volume of extract needed to make a clinically viable dose. In 1929 and 1930, two medical doctors working with Cohn — George R. Minot and William P. Murphy — began to deliver these extracts to patients intravenously, further increasing their absorption and efficacy.

One contemporary researcher who wrote of the Cohn team's work observed:

They were able to eliminate proteins, fats, and carbohydrates from the raw beef liver without a noteworthy loss in activity. The purer fractions contained less phosphorous and a greater percentage of nitrogen.

Cohn’s team achieved this feat by honing skills they had already perfected in their studies on the physical chemistry of proteins. There are many steps involved in isolating proteins, and as many as six variables that could be finetuned at each step to improve the process. In other words, each step offered the opportunity for gradual improvements as well as mistakes. The following table represents an abbreviated list of steps used by Cohn's team to make just one version of the concentrated extract.

The Minot and Murphy medical studies, coupled with large-scale manufacturing of liver extracts by firms like Eli Lilly, proved so effective that within a few years, so few people in the Boston area had pernicious anemia that it became hard for researchers to find enough patients in which to conduct clinical experiments.

Despite its obvious success, Cohn viewed his work on pernicious anemia as a failure. His team never succeeded in isolating the active principle in its pure form. As a result, they never fully understood why the extract actually worked in patients. By the end of their studies, however, the team had learned enough to suspect that the active principle was not a protein, so Cohn decided to move on and the lab returned to its basic research efforts.

While Minot and Murphy shared the 1943 Nobel Prize in Medicine for their work on pernicious anemia, Cohn was not included.

Cohn the Field Strategist

Cohn is a fantastic example of what Renaissance Philanthropy CEO Tom Kalil calls a “field strategist;” those individuals who proactively catalyze under-explored areas of R&D, asking questions like “what are we not doing that we should be doing?” and coordinating efforts to pursue those problems.

Cohn made two major field strategy contributions during his career. The first was helping build the young field of protein chemistry into an established research field. The second was in organizing this group of chemists into a coordinated, well-funded system of applied researchers capable of quickly solving pressing problems for the war effort.

Oftentimes, the lever that makes a field strategist effective is an ability to distribute funding on behalf of some patron. Cohn never had that opportunity; at least not directly. Although he would often help raise money for labs doing complementary work, and was always pleading for backing to expand his own work, Cohn was foremost a researcher who organically became a field strategist by wielding his personality, ambition, and entrepreneurial energy.

Some field strategists — such as Salvador Luria, in the case of molecular biology — have a warm personality that draws individuals into a field. But that was not the case with Cohn, who had a penchant for success despite his interpersonal quirks.

Letters and notes from Harvard’s President, Cohn’s funders at the Rockefeller Foundation, and even his best friend all mention Cohn’s arrogance, mercurial nature, and inability to cooperate with colleagues as equals. Despite the salience of these negative qualities, Cohn reliably wooed talented researchers to his cause and raised a large amount of money to drive his agenda forward.

Cohn never missed an opportunity to recruit talented scientists, often going out of his way to poach people who were “between” research roles. He also had a stunning ability to look ahead and anticipate what sorts of talent his field would need to grow.

In the mid-1930s, for example, Cohn noticed that a talented MIT lecturer named Larry Oncley had accepted a lower academic position because, due to financial difficulties, he could not wait on a research fellowship. Oncley, a University of Wisconsin PhD, was not dissimilar to other Midwestern PhDs at the time; he was as much an instrumentalist, or a lab-instrument engineer, as a scientific researcher. This skillset, shared by Oncley and several others who later become key fixtures in Cohn’s laboratory, proved invaluable to wartime efforts when it became clear that many protein purification experiments would require extensive modification of instruments to work at scale.

But Cohn was mercurial and known to blow up at his lab staff for minor errors. Many scientists were scared to report poor results to him — with or without mistakes. Nonetheless, one visitor to the Harvard lab, A.C. Chibnall, noted in a letter to the Rockefeller Foundation's Warren Weaver — largely responsible for funding the field of molecular biology into existence — that he had never seen a group of researchers that size "in which all the people seem so happy and get on so well together."

Chibnall did not fully understand the technical aspects of Cohn’s work, but he left with a sense that their work was worthwhile. He felt that the entire team was on board with the "long programme that Cohn has mapped out for them during the next few years." Cohn was a natural leader. He could sell his long-term vision for the field to almost anyone.

All who worked in his area of protein chemistry — which in the years leading up to the war had grown to about 15 investigators, usually with small lab staffs of their own — seemed to defer to Cohn's de facto role as agenda-setter and orchestrator. He did not do this by insisting on putting his name on papers, however. Cohn cared about prestige, but not authorship. What motivated Cohn was exercising a level of influence and direction on the young field. And the center of the universe of protein chemistry, at the time, was Cohn's weekly lab meeting.

These meetings served as both a place for him to hold court, and for all participants to keep tabs on each other's work via frequent, brief presentations. Curious researchers from external laboratories often attended.

The meetings were great places for Cohn and others to see how one investigator’s work could complement another’s. And nobody helped more than Cohn. For all of Cohn's downsides — he once berated a staffer whose wife had died over the weekend for late work, never apologizing — he was not competitive. Or he was at least not competitive in the traditional way.

Cohn even went out of his way to help researchers seeking to isolate the active principle from liver, a project he’d failed at, by sending his team’s extracts to their labs. Cohn helped others in ways outside the lab as well. He raised funds for other research teams, going out of his way to lobby for National Research Council Fellowships for researchers he thought would be useful to protein chemistry. He put in a good word for researchers with the Rockefeller Foundation and to firms he felt should sponsor some academic’s endeavors.

And Cohn was very good at fundraising. This partially came from his ability to sell a vision and partially from his vehement refusal to ever be satisfied with his budget. Cohn grew up in a wealthy family. A colleague who knew Cohn as an undergraduate wrote: “If he did not have the best of everything, he had the most expensive when his family did not know what was best, which was seldom.” Cohn expected no less for his laboratory.

In Oncley’s National Academy of Sciences memoir, former lab member Russell Doolittle reported admiringly:

Cohn was a powerful institutional figure who possessed what was apparently direct line reporting to the President of Harvard, James Conant, who was a chemist. Given this rare privilege, Cohn seemed always able to garner the generous funding that ensured progress would never be hampered by traditional academic bureaucracy.

The privilege of this direct-line reporting is demystified, however, when one reads President Conant's accounts of their relationship. In 1938, in the midst of one of Cohn’s insistent funding pushes, Conant wrote an amusing letter to a Harvard Dean detailing what it was like to deal with the chemist:

Get hold of Dr. E.J. Cohn and let him pour out his grief to you for several hours. (He is a very entertaining person, incidentally) … The question today is where does E.J.C. and his laboratory fit into the University? And more important, who is to finance it? E.J.C. feels it is my personal responsibility to go out and get funds for him because (1) I’m a chemist and (2) because my personal prejudices and actions have put him into the hole he now is in. From my point of view his work is good, but he can’t cooperate with his equals or superiors — he is hopelessly ‘high hat’ about all but ‘pure’ or ‘basic’ research. His budget is enormous … I’d like to have a committee between E.J.C. and myself. Why must a President of the University take on this man? … By listening and asking questions, you may steer him into a better mood and tell him the answer to a tough question, namely, how to keep him happy without making his support the first charge on my time and the University’s resources.

Warren Weaver, director of the Division of Natural Sciences at the Rockefeller Foundation, also funded Cohn and penned the following personal journal entry after an evening with him in 1939 (note that Weaver often wrote these entries in the third person):

C. [Cohn], who himself, apparently lives in a world of subtle and complicated intrigue, in which no one says just what he means, is forever reading deep an unintended significance in chance remarks of WW [Warren Weaver], later coming back with the proud report that he believes he correctly senses what WW meant when he earlier said something else. Thus C. now reports with considerable satisfaction that he believes he has figured out just what WW meant a year or so ago by certain wholly innocent and frank remarks concerning C.’s hope to get a supercentrifuge.

Despite such comments, Weaver seemed to like Cohn, in a way. He chose to make large block grants to Cohn's lab for nearly two decades. Weaver did this despite mixed reviews from Cohn’s peers. While all the scientists found Cohn's experimental work to be well-executed and thorough, several noted that Cohn's work lacked creativity and made only modest positive impact — Linus Pauling among them. Even A.C. Chibnall’s letter to Weaver, noting that he’d never seen a lab get along so well, also acknowledged that this harmony was particularly shocking given “the fact he appears to irritate a lot of people outside Harvard.”

But Weaver, the greatest life sciences funder of his era, apparently did not see this as an obstacle. Weaver understood how important field strategists were to the growth of young fields of science, understood the potential usefulness of proteins, and grasped Cohn’s natural talents as a field builder. While Weaver's journal entry note to himself poked fun at the "considerable length" with which Cohn bragged about his field strategy schemes, he clearly appreciated Cohn's field strategy excellence.

Weaver’s bet on Cohn would pay off faster than he ever imagined.

Drafting the Lab

In 1940, Cohn’s lab was drafted into the war effort. With the threat of American involvement in World War II looming, the government began to plan for conflict. In May 1940, the National Research Council held the first meeting of the Committee on Transfusions. This committee was made up of about ten people; half were prominent professors of medicine and the other half held positions in the Army and Navy Medical Corps.

During this meeting, representatives from the armed forces said they would favor the use of dried plasma over whole blood for treating wounded soldiers. Plasma — blood with the blood cells filtered out, a liquid largely consisting of water and proteins — was deemed comparable to whole blood in the treatment of shock in trauma patients by the committee. While this belief weakened over the course of the war, plasma had a distinct advantage over whole blood; namely, plasma could be dried, stored for months without refrigeration, and re-assembled for administration, whereas whole blood was only viable for about a week and required refrigeration. Dried plasma also didn’t need blood-type matching, meaning soldiers could be treated much faster.

But both approaches had flaws and would require the collection of blood from volunteers on an unprecedented scale. The Red Cross, then a general aid organization, was tasked with figuring the problem out. But many on the committee, including prominent Harvard Medical School researcher Walter Cannon, were not content to hold their breath on mass blood collection.

Fortunately, there was an alternative approach. Experimental results collected by University of Minnesota researchers suggested that bovine plasma might be well-received by humans with minimal serum sickness. While a great deal of research was still needed to determine the efficacy of the approach, one thing was clear: so many cows were killed each day in American slaughterhouses that stores of cow blood were essentially limitless. The committee decided that research should be conducted on developing and testing a bovine blood substitute for human plasma. Cannon, the chairman of the committee, asked Cohn to lead the effort.

In some ways, Cohn was a peculiar choice. He did not like applied research and, unlike the board, which primarily consisted of M.D. researchers, Cohn had no experience dealing with trauma victims in shock — or patients in general.

And yet, in other respects, Cohn was a natural choice. In recent years, his lab had begun to work with blood proteins, albeit as a somewhat arbitrary protein source for fundamental investigations. While this material may have just been Cohn's newest intellectual pursuit, his genius and persistence in fundamental investigations had never been questioned. Most importantly, despite his purist leanings, he'd done exceptionally efficient work on the applied pernicious anemia problem.

Cohn answered the call.

From here, Cannon and the committee set the technical parameters of the challenge, noting that the final blood product from cows must:

• Simulate plasma proteins’s ability to control fluid balance
• Have appropriate molecular structure to be adequately retained
• Be a concentrated solution
• Withstand a range of battlefield temperatures
• Have a long shelf life
• Generally not harm the patient

Cohn set out to bring the full force of his laboratory and field strategist toolkit to bear on the problem. Given that some degree of serum sickness would likely be a clinical issue with non-human products, Cohn was tasked with isolating the single blood protein most suited to treating shock and restoring blood volume in wounded soldiers. The reasoning was that each additional bovine blood protein in the product might trigger additional allergic reactions, causing more severe serum sickness. If possible, the committee wanted to get the maximum clinical effects out of a single protein.

In Cohn’s estimation, the ideal protein would be bovine albumin. Albumin was largely responsible for restoring osmotic pressure in the blood and, conveniently, albumin is also the most abundant protein in plasma — both bovine and human.

A Prepared Mind

Prior to 1940, Cohn had always gone out of his way to ensure he was working with the best people and also, importantly, the best equipment.

In 1936, Cohn raised funds and assembled a team to build an ultracentrifuge; a machine capable of separating proteins of various sizes and shapes with extreme precision. Cohn had long been jealous of Theodor Svedberg's ultracentrifuge in Sweden, constructed in 1926. So when Cohn heard that the International Health Division of the Rockefeller Foundation was going to build one for itself in America, he lobbied for funds to build one for himself as well.

Cohn quickly convinced the Rockefeller Division to fund the ultracentrifuge and then worked with Harvard President Conant to build it. Conant appointed a six-man committee of Harvard's best life scientists to oversee the project. In an amusing turn of events, the six-man committee of Harvard's best life science researchers decided that they needed an MIT man to get the job done — the lecturer, Larry Oncley.

Oncley was put in charge of overseeing the design and construction of the machine, along with contractors. By the end of the project, Cohn had even found additional funding to offer the “expert instrument maker” brought on to work with Oncley a permanent position. The ultracentrifuge’s builder stayed with Cohn for decades.

In the latter half of 1940, Cohn’s team started work on the military’s blood project. Progress was smooth. After two decades of experience, the group was expert at finding ways to sediment and characterize new proteins. Methods developed over the years could often be applied toward this new challenge.

One of the most noteworthy of these was Cohn’s ethanol-water fractionation process. When the war project got underway, the lab had already developed a means by which they could successfully fractionate horse plasma — separating relatively pure protein components, one-by-one, away from the horse serum and each other. These “fractions” included component proteins such as albumin, gamma globulins, and fibrin. To separate each set of proteins from the horse blood, though, Cohn’s team had to carry out many tightly controlled steps based on dissimilar shapes, weights, and mobility; adding chemicals or solutions to enable further separation; or removing chemicals and solutions no longer useful.

Each step required the use of a variety of instruments and methods like the ultracentrifuge, Tiselius electrophoresis, salting out methods, and many other tricks of the trade. Developing, improving upon, and increasing the consistency of lengthy protein refining and testing processes was the Cohn team’s speciality. The lab’s horse serum method, in addition to providing useful experience with animal blood, was the “first study in which pH and temperature were controlled as variables” while separating proteins across a membrane with ammonium sulfate.

While innovative, Cohn did not believe that his team’s fractionation methods would work at an industrial scale. There were inefficiencies with the ammonium sulfate procedure that would cause major cost increases and time delays when ramped up to industrial scale. And, with America’s involvement in the war encroaching, any method that could not quickly enable the mass production of hundreds of thousands of doses was not worth exploring. The lab needed to find another way, and Cohn had a solution.

He believed key pieces of a separate process, which the lab had deployed to do fundamental studies on egg albumin years prior, could be combined with their horse fractionation procedure to yield a process fit for industrial scale. Instead of using ammonium sulfate dialysis procedures to separate albumin from plasma, Cohn’s lab would instead use an ethanol fractionation procedure. While ethanol had its downsides, Surgenor noted the clear upside: “ethanol is volatile and could be easily removed from proteins by drying from a frozen state.”

By December 1940, the group had developed an ethanol fractionation procedure that successfully fractionated the blood collected from a local Somerville slaughterhouse. The final step in the procedure, drying out the partially fractionated product to separate the albumin, was also well-suited to large-scale production.

Cohn and Conquest

Cohn's ability to manage technical talent, sell others on his vision, and fundraise was as sharp as ever. But he now sought a new metric of success: developing and shipping useful blood components for the U.S. war effort.

While his team continued to develop the process for fractionating bovine albumin — yields were still quite small — he instructed his MIT colleagues to begin developing the later steps of the ethanol fractionation process on horse albumin. Given the circumstances, waiting was impractical. Though American troops weren’t yet involved in the war, estimates suggest casualties were high — about 68,000 British troops during the Battle of France from May 10 to June 25, 1940. Cohn’s group could later substitute bovine albumin into their work when more fractionated product became available.

Beyond his own lab's efforts to increase the yield and purity of albumin, Cohn also set to work ensuring bovine albumin shortages would not be a concern for the rest of the war. His lab’s production scale was insufficient to provide the necessary research material or clinical trial material; at the lab’s bench top scale, Cohn’s team was only able to isolate albumin from two liters of plasma in a single run. These runs only yielded about two or three single-serve vials of albumin. To scale-up manufacturing, Cohn asked around and was put in touch with Victor Conquest, a bright technical executive at Armour Laboratories, a pharmaceutical manufacturer in Chicago.

Cohn pitched Conquest on his idea to build a pilot-scale industrial factory to scale up his labs’ bovine albumin fractionation process. Cohn also explained that he had no funds available to pay Armour; Cohn himself would not receive National Research Council funds until early 1941. Conquest was convinced, likely because he assumed Armour would be the natural choice to receive the military contract if the NRC decided to scale up Cohn’s work for the war effort. Still, this was an impressive feat by Cohn given that many government contractors throughout the war would refuse to take leaps of faith even after receiving word from government contracting officials. Cohn, with no authority or funds whatsoever, had convinced Conquest. Armour immediately began assembling the pilot plant.

The first Armour scientist assigned to lead the project quit because of “difficulties working with Cohn.” But a new senior scientist was later put in place who found Cohn less unbearable. An extremely productive working relationship ensued. As Surgenor summarized:

Under these amicable circumstances, the Armour scientific endeavor became for all intents and purposes an arm of [Cohn’s] Department of Physical Chemistry in pursuing the development of bovine albumin and human albumin.

With the bovine albumin project moving forward, Cohn set his sights on a problem that the NRC had not asked him to pursue but which he thought important: human albumin.

With bovine albumin, even if the physical chemistry and manufacturing problems were solved, Cohn knew clinical complications might derail the project. As he saw it, the appropriate approach was for his lab to simultaneously pursue both lines of work — bovine and human albumin — until one was approved for treatment in American soldiers. To make sure this happened, Cohn secured a meeting with a high-level Navy and Red Cross official in December 1940.

To the meeting, Cohn brought a copy of that month's Journal of the American Chemical Society, containing his team's new paper on the ethanol-fractionation of bovine albumin. He also brought a vial of bovine albumin for the high-ranking officials to pass around. Cohn, selling two competing research ideas at once, stressed how useful the bovine product could be for the armed services while cautioning against relying solely on the product. As Surgenor, the biographer, recalls:

[Cohn was showing the vial and] stressing how much depended on completely freeing bovine albumin from immunological reactivity, something that had never been done before. Under the circumstances, he advised [the Navy’s] Stephenson that it would be a mistake to delay keeping open the option of meeting the needs of the armed services with products from human blood.

Stephenson was apparently convinced. He recommended to the Navy Surgeon General that they commit to funding both research threads.

In April 1940, Cohn attended his first meeting of the NRC Subcommittee on Blood Substitutes. The makeup of the committee was similar to the previously mentioned umbrella NRC Committee on Transfusions — prominent doctors from medical schools, as well as representatives of the armed forces and the American Red Cross. Cohn was the only non-medical researcher invited, and he made a big impression. At this meeting, after passing around his vial of albumin, Cohn surprised many by announcing that scientists from Armour Laboratories had already begun training at his lab in Boston and assembling a pilot plant to his specifications.

Only nine months after Cohn's lab had been drafted into the war effort, his research group had published a paper describing a much more scalable approach to blood fractionation and, without any funds, had convinced a pharmaceutical firm to construct a pilot plant and send its staff to Cohn's lab for training.

And that was just the start. Cohn was rapidly learning. He had come to understand the bottlenecks of this applied work and wanted to restructure his lab accordingly. By the end of April, the NRC had granted Cohn’s lab $6,500 and arranged for an additional $5,000 grant from the American College of Physicians. Cohn was not going to use these funds to do more of the same. Instead, he was going to build a pilot plant of his own at Harvard to fractionate human plasma.

Pilot Plants

Cohn's construction of a pilot plant at Harvard drastically changed the environment in which science was done in his department. The new environment was more aptly suited to the team’s new priorities. His team of chemists no longer fractionated proteins merely to understand how they behaved, but now sought to manufacture them at scales sufficient to treat clinical issues in the battlefield. With the construction of the pilot plant, Cohn built a scientific environment at Harvard that mimicked commercial pharmaceutical factories in one fell swoop.

Surgenor, who was a close colleague and collaborator of Cohn’s for years, framed the upsides of the Harvard Pilot Plant in much the same way Cohn would have. He explained:

Pilot plants are small production plants. They enable production of products on an intermediate scale between ‘bench top’ experiments performed in the research laboratory and large-scale industrial production. In order to safely and expeditiously to scale up chemical processes to the pharmaceutical production level, experience must be gained at the pilot plant stage. Pilot plants use tanks instead of beakers and work with other large processing equipment. Pilot plants often provide valuable insights into how increases in scale of operations can affect a chemical process. Increases in scale of processing often introduce unforeseen effects. For example, the time it takes to carry out certain steps, such as the addition of reagents, or the centrifugation of large volumes of suspensions of protein precipitates, may increase inordinately, due to the differing characteristics of the larger equipment that must be used. Furthermore, the dynamics of temperature control differ when the volume to be cooled is sharply increased. During the pilot plant stage, the Harvard scientists could identify and overcome the pitfalls that could be expected to arise during the transfer of new technology to the pharmaceutical industry.

No longer would Cohn’s colleagues fiddle with processes for months or years at bench-top work stations only to learn they would not work at industrial-scale. Now, if a chemist on Cohn’s team achieved promising results at their bench, they were expected to immediately seek out someone like Oncley in the pilot plant to test and develop the new process on pilot-scale equipment.

Beyond more effectively translating processes to pharmaceutical plants, there were other practical upsides to the Harvard Pilot Plant. Developing processes at the pilot scale supplied more than enough human albumin for clinical trials, for example. With the Harvard Pilot Plant — capable of processing 40L batches of plasma in a single run, 20 times more than what was possible in the lab — new clinical trial stages could proceed with no unnecessary delays. In addition, pharmaceutical staff from manufacturing firms could get hands-on training at the plant before their own production plants were even finished.

During the war, while one key pharmaceutical employee might be overseeing the production of his firm’s plant, another would go to Boston and work eight-hour shifts with Cohn’s staff. Beyond simply learning the methods of fractionation and analysis from Oncley and others, Surgenor recalled the full level of immersion of these trainees, writing:

A visitor to the pilot plant in the late evening might encounter a senior pharmaceutical firm manager clad in arctic clothing emerging from the cold room pushing an empty glass-lined Pfaudler tank out the door to be washed.

In 1941, with the integration of the pilot plant into the department’s processes, many of the department’s researchers took on more specialized roles. Oncley, a Wisconsin PhD who always had a great mind for instrumentation, became the Director of the Ultracentrifuge Laboratory. The arrival and rapid promotion of Lawrence Strong, another technically-adept Midwesterner with a PhD, demonstrates how valued hands-on skillsets became in the growing industrial R&D lab. Surgenor recounts:

On Strong's arrival, Cohn was designing a glass device for use in the equilibration of plasma ... Cohn was not a glass blower, while Strong was a capable glass blower. He quietly stepped in and blew the device that Cohn sketched. With this ‘hands-on’ encounter as a beginning, Strong, a quiet and thoughtful Quaker, was, before long, playing a key role in Cohn's developing organization. Although titles were seldom used in the laboratory, Cohn and Strong held titles as Director and Associate Director of the Harvard Pilot Plant, respectively, for the duration of the war.

The extended universe of researchers surrounding Cohn took on a more formal structure during the war, but beyond that things operated similarly to how they had previously. The field was still managed via his weekly lab meeting — even though the headcount of Cohn’s own Harvard operation grew to over 40 during the war. Cohn also continued sending materials to all researchers whose minds and hands could provide something useful to the endeavor. And he still had a strong hand in directing the investigators’ work in his own department, even though he rarely added his name to any of their papers.

In June 1941, a member of Cohn's team discovered an accidental blessing in a sample of bovine albumin that had crystallized in the cold room. Crystallization would allow for much purer bovine albumin, which was essential given that clinical tests on early bovine batches showed signs of serum sickness. The team, which had historically been effective at crystallizing other proteins, was able to reliably produce crystallized bovine albumin in the pilot plant by the end of the year. As Surgenor framed this success, "No crystallized protein had ever been prepared on such large scale."

Cohn’s team was equally adept at working with both bovine and human albumin. The military would later opt for human albumin, however, once it became clear that the Red Cross was able to collect large amounts of donations — thirteen million units in total during the war. Within two months of receiving funds from the NRC and American College of Physicians, Cohn’s team had fractionated its first batch of pilot plant human albumin. The team worked so rapidly that, by December 7th of 1941 — the day the Japanese attacked American troops at Pearl Harbor — human albumin had shown enough promise to be tested in the field.

As Admiral McIntire reported of Pearl Harbor, "It was burns, burns, and more burns." The fluid loss from battlefield burns can lead to severe shock. An NRC Chairman phoned Cohn and insisted he send all vials on hand to Pearl Harbor. The 29 available vials that Cohn sent were administered to seven of the most severe burn cases the on-site doctor could find. All the treated soldiers got better. Surgenor described one case as follows:

One patient was unconscious and in critical condition, leading an attending physician to question the advisability of giving him albumin. He was given a quantity of albumin equivalent to more than a liter of plasma in the morning and by afternoon he was delirious but talking. The following morning he was given more albumin. On the third morning the edema had disappeared and the patient was able to eat breakfast.

Pleased with the results, the NRC approved Cohn’s human albumin for military use in January 1942.

By the end of the war, approximately two million of the 13 million blood donations procured by the Armed forces were used to make human albumin. Another 10 million units were used to make plasma kits. That is two million units of a blood substitute that, practically speaking, did not exist in early 1940. The albumin process was ready for industrial-scale production as soon as the Army was ready to begin ramping up production for war.

While the albumin was not as clinically desirable as plasma and not nearly as clinically useful as whole blood, it surely saved many lives. The product was more stable than dried plasma. And unlike dried plasma kits, which had to be reconstituted with water even in the most dangerous of circumstances, the liquid albumin solution could be administered to wounded soldiers straight-away in dangerous situations.

Cohn’s albumin kits were also one-sixth as heavy and one-fifth as large as the plasma kits. In a war of logistics, this shipping and storage convenience had a clinical quality all its own in many cases. For example, Surgenor recounted the case of a group of corpsmen who lost all their plasma when their landing boat was sunk off the beaches of Normandy. The soldiers stuffed their pockets with the small packages of albumin and administered it to many seriously wounded men, most of whom lived to be evacuated to ships and receive further medical care.

Human albumin did not prove as useful in peacetime, however, as plasma or whole blood. Perhaps that is why so few today know about Cohn’s work.

Even so, we should not disregard the lessons we can learn from Edwin Cohn. Cohn was a protein chemist who did everything possible to rapidly translate his methods so that doctors could determine their efficacy, industry could manufacture his products easily, and the powers that be could allocate material as they saw fit. Cohn’s expert integration of his pilot plant into his lab’s work demonstrates just how productive his approach can be in areas where research insights are great, but the manufacturability and efficiency of methods seem major bottlenecks.

The exceptional translational work of Cohn and his colleagues coincided with some of their best scientific work. The fractionation process continually improved, in no small part, as a result of the Cohn group’s willingness to do novel research with their large instruments. Cohn’s group eagerly folded in new ideas from colleagues in university labs and wrote regular letters sharing problems and possible solutions. The beautiful “interplay of ideas in this research” was clear to Cohn, who would have been the first to admit if his lab became a place of industry and not frontier research.

During the war, as was typical, Cohn still found a way for his ambitions to outstretch his now-massive budget. He was not content just researching human albumin. He wanted to find uses for the other component blood proteins that his team and the pharmaceutical firms were fractionating along the way, such as gamma globulin and fibrin.

However, the U.S. Government was reluctant to sponsor Cohn’s fishing expedition while a war was on. But, since a war was underway, Cohn figured they’d fund anything that showed promise to aid the war effort. As he saw it, he just needed to source money from elsewhere to prove the worth of these proteins. And he would get them. Cohn later bragged about these funds, calling them his “risk capital.” Cohn’s expert deployment of this risk capital alongside his war contracts allowed what might be his lab’s most exceptional period of basic research to coincide with its golden era of applied work.

“Risk Capital”

Cohn, one part acquisitive and one part visionary, decided war was the perfect time to go on a fishing expedition for new ideas. He began using his substantial basic research funds to explore any exciting research ideas not covered by military R&D funds.

In early 1942, a Rockefeller Foundation officer, aware of Cohn's war funding, wrote Cohn a letter indicating the foundation would be happy to hold in escrow the rest of Cohn's grant until after the war. Cohn quickly dissuaded the foundation officer from this course of action. An excerpt from Cohn’s letter reads:

No matter what proportion of our work is taken over by contracts with the OSRD [Office of Scientific Research and Development], there is always the new angle of the research to be investigated and at every level we have found it invaluable to be able to use our grant … for such investigations until such time as their value as an applied research could be investigated.

In the letter, Cohn cited the lab's work with gamma globulin — which later proved to successfully innoculate against measles and Hepatitis A — as "a very proper use to which to put your grant." The war funding enabled Cohn to operate a lab at a scale that was optimal for translation. With government contracts covering so much of Cohn’s fixed costs, he was able to stretch the Rockefeller Funds exceptionally far — much farther than in peacetime.

In the years leading up to the war, Cohn's budget was comparatively huge for a basic research group. He had about $25,000 in reliable, annual funds — with around $10,000 coming from Rockefeller and the rest from Harvard. But Cohn was also adept at raising one-off funding. One example is when he raised $30,000 to build the ultracentrifuge. In another case, he convinced corn-growing companies to grant him $60,000 to train their scientists in his lab. Taking these one-off raises into account, Cohn's yearly pre-war budget may have been in the $40,000 range. This was peanuts compared to his wartime budget.

By the end of the war, Cohn’s budget had soared. He had finally achieved a budget that fit the scale at which he thought. By 1945, his annual budget was $120,000 — $2.1 million today. That number does not include the handful of external labs that operated, more or less, as an extension of his own agenda — whose funds had also increased during the war.

Of the annual $120,000, Cohn was free to use $14,000 in Rockefeller funds as "risk capital.” On top of that $14,000 per year, Rockefeller had also given Cohn a one-time grant of $16,000 to use as needed to buy additional equipment. While $2.1 million might not sound like a lot today, it was enormous for a mid-century life sciences lab. To provide a frame of reference for Cohn’s $120,000 annual budget, at the time a tenured professor's salary was ~$4,000, and Cohn’s massively expensive ultracentrifuge cost only $30,000 to build.

With his mix of applied funds and risk capital, Cohn was able to work magic during the war. The Rockefeller Foundation President glowingly wrote in an annual report about how Cohn's research was "paying large dividends in human lives on our far-flung battlefields." Warren Weaver, pleasantly surprised that his bet on this peculiar man paid off, wrote the following of Cohn in the Rockefeller Foundation's 1943 Annual Report:

As late as 1938 The Rockefeller Foundation, making an appraisal for itself of this project, included in its statement the sentence: ‘The work has been painstaking, abstruse, and likely only slowly to come to widespread recognition for its essential importance.’

This laboratory and this patient effort thus constitute a dramatic illustration of the truth of John Dewey's remark: ‘It does not pay to tether one's thoughts to the post of usefulness with too short a rope.’ For when the war came and sudden emergencies arose, it developed that Dr. Cohn's laboratory was in possession of the knowledge and the techniques to solve a very practical and pressing problem.

Weaver also went on to praise the scope of Cohn's wartime research agenda, which Rockefeller’s risk capital enabled:

What started as an inquiry into the practicability of using animal plasma as a blood substitute for transfusion purposes, has developed into a program of ‘mining’ blood for its individual substances and for testing these concentrates for therapeutic and prophylactic use. Knowledge gained in a laboratory devoted wholly to problems of pure science has been turned quickly and effectively to meet immediate human needs.

Despite the lab’s massive success, after the war Cohn chose to follow the same trajectory that he had after his earlier success with pernicious anemia: he moved on. Even Cohn, who did not admit mistakes, came to deeply regret the decision.

Cohn’s Folly

In 1945, Cohn's Rockefeller Foundation grant was set to expire. It was time for Cohn, who had become a minor scientific celebrity as a result of his contributions to the war effort, to plan for his lab’s next chapter. So, the Rockefeller Foundation wrote Cohn's dean at Harvard, suggesting he and Cohn outline their plans for the future of the physical chemistry department. Dean Sydney Burwell wrote back to the Foundation with Cohn’s new plan to revert to attacking "fundamental problems." One excerpt reads:

These young men and their colleagues have accumulated a vast amount of knowledge during the extraordinary opportunity of the five years. They have seen during this period more material than they might expect to see in an ordinary lifetime. Important scientific assets are here and should be preserved by a proper transfer of the efforts of this group from the applied to the theoretical area. During the past five years it has been necessary to postpone fundamental work which was simply crying to be done …

The letter indicated that Cohn could get by on half his wartime budget — $70,000 per year. Harvard requested the Rockefeller Foundation fund $22,000 of the annual total.

Cohn, who may have become overly obsessed with all the problems he hadn’t been able to look into during the war, instead of focusing on all the useful questions war work brought to the lab, would go on to deem this decision a major mistake,¹ later writing:

This error in judgement has been a continuing embarrassment to the Administrators of the University and to myself, since the laboratory space which I assured President Conant would be adequate, has proven completely inadequate, and since the funds which I assured the Rockefeller Foundation would be adequate have also proven completely inadequate.

Cohn never had a “first-rate” creative mind. He was, rather, a pragmatist. His wide-ranging genius lies in coming up with processes to thoroughly answer questions, fundraising, field strategy, and management. As one colleague described Cohn, the manager:

Cohn is a tycoon. He runs his lab like General Motors. The kind of team work he demands often makes it impossible to tell with whom any scientific idea originates.

To one Rockefeller Foundation officer, one downside of Cohn, the manager, was that his lab was not the kind of place one could count on to find anything "sideways." Cohn’s lab was at its best when constrained by a goal, but with the freedom to thoroughly explore new avenues relevant to the goal at hand. In my FreakTakes essays on the golden eras of Bell Labs and GE Research, I’ve referred to this as a “long leash within a narrow fence.” Cohn thrived with certain freedoms, certain budget allowances, some constraints of practicality, and the funding and scale that came with those constraints.

Without the fence and funding levels that came with it, Cohn’s lab became a shell of its former dynamism. It still produced useful work, but would never be the same. One can only speculate on the results had Cohn led his lab in peacetime in the same way he did in wartime.

Edwin Cohn died in Boston in October 1953, right around the time his Rockefeller grant was set to expire. He was just 60 years old.

Lessons from Cohn

The story of Edwin Cohn is both a playbook for field strategists and a demonstration of the outsized impact a great pilot plant can have when applied to the right problem area.

Cohn’s laboratory shows, at least anecdotally, that even a “pure” academic lab can become a translational powerhouse under the right circumstances. These circumstances aren’t necessarily difficult to come by, either; Cohn’s lab contained many of the same people and methods before the war as after it, but the war-driven pilot plant and applied incentives created the circumstances for them to flourish.

Setting up pilot-scale facilities at academic universities could help accelerate progress toward solving many problems in biology and chemistry that are currently hamstrung by cost and manufacturing. Synthetic blood, for example, can be made in limited quantities in the laboratory but is exceedingly difficult to make at scale. The same is also true in materials research. Ben Reinhardt, founder of Speculative Technologies, has previously written about how carbon nanotubes, graphene power sources, aerogels, and lithium-ion battery anodes are all examples of laboratory novelties that have similarly failed to ratchet up.

There are many reasons why bench discoveries such as these struggle to find commercial success; slow iteration cycles, lackluster connections between academics and companies, inadequate funds, lack of engineering know-how useful in ramping up pilot labs, and the fact that many researchers are often incentivized to chase punchy headlines regardless of commercial viability, so they select R&D paths without adequate consideration for cost and scale. Ultimately, while these conditions do present formidable challenges, they could be resolved, in part, by introducing more Cohn-style workflows into the modern R&D ecosystem.

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Eric Gilliam recently joined Renaissance Philanthropy and is a Fellow at the Good Science Project. He writes operational histories on the FreakTakes Substack, exploring actionable takeaways from the 20th Century’s greatest R&D operations.

Cite: Gilliam, Eric. “Edwin Cohn and the Harvard Blood Factory.” Asimov Press (2024). DOI: 10.62211/94ut-12kj

Postscript: Eric is eager to hear about areas of R&D that could benefit from Cohn’s playbook. Please reach out to him with a description of a technical area you think could use a pilot plant, how expensive it would be to operate, who might be willing to fund it, and what the realistic and best-case scenarios would look like to make the pilot plant an efficient use of funds. He will eagerly assist those with compelling ideas. Feel free to email him (gilliam@renphil.org) or DM him on Twitter.

Further Reading

• Douglas Surgenor’s biography of Cohn
• Cohn’s chapter in Advances in Military Medicine, Volume 1
• Warren Weaver’s 1937, 1938, 1943, and 1945 Rockefeller Foundation Annual Report Natural Sciences sections, especially 1943.
• The entirety of Janeway and Colleagues’ Chemical, Clinical, and Immunological Studies on the Products of Human Plasma Fractionation series of papers, especially Part VII on Concentrated Human Serum Albumin
• John Edsall’s National Academy of Sciences memorial piece on Cohn
• John Edsall’s Memories of early days in protein science, 1926-1940
• Russel Doolittle’s National Academy of Sciences memorial piece on Oncley
• Charles Janeway and Oncley’s chapter in Advances in Military Medicine, Volume 1
• Angela Creager’s paper on Cohn and blood as a research material.
• W.B. Castle’s National Academy of Sciences memorial piece on Minot.
• James Phinney Baxter’s Scientists Against Time, Chapter 21

Footnote

1. Surgenor, Cohn’s biographer, emphasized the gravity of Cohn’s admittance given that "he rarely admitted making a mistake." This was, after all, the man who did not apologize after screaming at a colleague for late work the day after his wife had passed away.

This article was published on January 5th, 2025.