In my recent post on the case study of the transistor, we saw that the research that led to its invention did not fall neatly into the categories of “basic” vs. “applied”, but in fact cycled rapidly between them.
An entire book—Pasteur’s Quadrant, by Donald Stokes—is dedicated to the thesis that “basic” vs. “applied” is a false dichotomy that is harming science funding.
The core idea of Pasteur’s Quadrant is that basic and applied research are not opposed, but orthogonal. Instead of a one-dimensional spectrum, with motion towards “basic” taking you further away from “applied”, and vice versa, he proposes a two-dimensional classification, with one axis being “inspired by the quest for fundamental understanding” and the other being “inspired by considerations of use”:
I find these phrases somewhat cumbersome, given their centrality to the thesis, so let’s call them “discovery” and “invention” for short.
In Stokes’s classification, research aiming at discovery, with no thought of invention—“pure basic research”—is characterized by Bohr’s search for a model to explain the atom, and hence labeled “Bohr’s quadrant”. The opposite, “pure applied research”, or invention with no attempt at discovery, is characterized by Edison and his lab, who tinkered endlessly to engineer products such as the light bulb, with little heed to theory: “Edison’s quadrant”. But, crucially for Stokes, there is research that combines discovery and invention, motivated by both at the same time. “Pasteur’s quadrant” is characterized by the career of the great scientist who gave us both the germ theory of disease and the first engineered vaccines.
Stokes traces the history of the basic-applied dichotomy back to ancient Greece, where they had different words for different types of knowledge: episteme for scientific knowledge, and techne for the practical arts. Long before the Baconian program, episteme was not seen as the basis of techne—nor was it, at the time. Mathematics, astronomy, and natural philosophy were ends in themselves, pursued for the pleasure of knowing, not with practical goals in mind. Plato formalized this by elevating conceptual knowledge to a higher realm, of which daily life was a mere imperfect reflection. His influence extended all the way to 19th-century Germany, where the modern research university was conceived, as a place for scientists to pursue scholarship in complete freedom. This model was ultimately exported to the United States in the late 1800s.
The modern American research funding paradigm was essentially established by Vannevar Bush at the end of World War II. During the war, government greatly increased funding for research, and great strides were made: radar, penicillin, malaria drugs, the proximity fuse, and of course the atomic bomb. As the war was ending, researchers wanted to keep their government funding, but also feared government micromanagement. How could they have both money and freedom?
Bush’s solution was the vision laid out in his famous report, “Science, The Endless Frontier” (written at President Roosevelt’s request). In the report, Bush said that “basic scientific research” would lead to all manner of practical benefits:
Advances in science when put to practical use mean more jobs, higher wages, shorter hours, more abundant crops, more leisure for recreation, for study, for learning how to live without the deadening drudgery which has been the burden of the common man for ages past. Advances in science will also bring higher standards of living, will lead to the prevention or cure of diseases, will promote conservation of our limited national resources, and will assure means of defense against aggression.
But, paradoxically, basic research is not and cannot be explicitly directed at those benefits:
Basic research is performed without thought of practical ends. … The scientist doing basic research may not be at all interested in the practical applications of his work, yet the further progress of industrial development would eventually stagnate if basic scientific research were long neglected.
Therefore, “freedom of inquiry must be preserved”:
Scientific progress on a broad front results from the free play of free intellects, working on subjects of their own choice, in the manner dictated by their curiosity for exploration of the unknown. …
And later:
… the primary obligation of the medical schools and universities is to continue the traditional function of such institutions, namely, to provide the individual worker with an opportunity for free, untrammeled study of nature, in the directions and by the methods suggested by his interests, curiosity, and imagination. The history of medical science teaches clearly the supreme importance of affording the prepared mind complete freedom for the exercise of initiative.
So in short, Bush’s message was: Invest in research with no thought of the return, and it will be returned many times over. Pump money into science, and it will trickle down to the economy. Give scientists absolute freedom to pursue their curiosity wherever it might lead, and it will ultimately lead to security and prosperity.
And he was not wrong. There is a large degree of truth in this message. But Stokes argues that Bush set up what I’ll call the “basic-applied dichotomy”, and that we need to overcome this and recognize the importance of Pasteur’s quadrant.
What’s the right way to categorize research?
I find Stokes’s two-by-two, if not quite compelling, then at least intriguing (and certainly better than the litany of prior approaches he outlines).
Naming the third quadrant after Pasteur is apt, because more than anyone else I know of, Pasteur’s career exemplifies the integration of science and engineering in a single mind. Tasked with improving the processes of French wine, beer, and vinegar makers, a mundane industrial engineering project aimed at iterative improvement, he showed the role of bacteria in fermentation, and discovered anaerobic metabolism—a breakthrough in microbiology. Decades later, when studying diseases of livestock, a purely scientific research project, a botched experimental setup gave him the clue that he followed to create the first engineered vaccine, a watershed invention in medicine. Clearly this was a man with the aptitude and the inclination to pursue both scientific knowledge and practical applications. And it was Pasteur who said, “There does not exist a category of science to which one can give the name applied science. There are sciences and the applications of science, bound together as the fruit of the tree which bears it.”
The case of the transistor, too, defies simple categorization as “basic” or “applied” research. It was an inventive goal that required the inventors, multiple times, to make an excursion into scientific theory and to advance our understanding of matter, before returning once again to engineering. Nylon, created at DuPont, was a case of an invention that arose fortuitously out of research into polymer chemistry.
But I don’t think we can understand these examples simply by putting discovery and invention on orthogonal axes and declaring that there is a quadrant at their intersection. What I see in these examples is that any project or lab, at any point in time, has a goal which is either discovery or invention. But the researchers were able to quickly pivot from one to the other, either from necessity or from opportunity.
So Pasteur’s fermentation work is a case of an inventive goal (improved processes) that turned into a more important scientific goal (understanding anaerobic metabolism). His vaccine work was the reverse: a scientific goal (understanding livestock diseases) that turned into a very valuable practical goal. The transistor work was a case of an inventive goal that required scientific goals for its completion. (The logical fourth possibility, a scientific discovery goal that required invention, could perhaps be represented by an innovative experiment such as the Michelson-Morley attempt to detect the ether, for which Michelson invented an interferometer.)
“Pasteur’s quadrant”, as described by Stokes, seems to be a type of research which is simultaneously motivated by discovery and invention. But what’s interesting about these examples is the rapid, flexible cycling back and forth between them.
If this mode of research is important, what are the implications for how research is funded, organized and managed?
First, we must have people, projects, and labs that can do both science and invention.
To have people who can do both, they should be trained in both. More importantly, there must be a role that embraces both. This affects evaluation, compensation, promotions, and overall career paths. Further, the role should be recognized by society. This encompasses everything from students learning about it as a career option, to accolades for the top achievers.
To have projects and labs that do both, they need to be set up, funded, and evaluated with this mode of research in mind. They need the freedom to pivot quickly between science and invention as the need or opportunity arises.
In particular, I think we need ambitious programs of invention that are willing to push the frontiers of knowledge—that is, to do science—in order to succeed. Such projects may need broad goals and loose timeframes (see again the transistor case). Who does this today? Corporate research labs don’t seem to be this ambitious anymore, and startups generally don’t have this kind of funding and aren’t able to take on this kind of risk.
We also need scientific research done by people who are capable of seizing the opportunity for invention when it comes along. Who does this now? At least some of this is done in university labs, but in between the invention and the market is a process of “technology transfer” with a reputation for being cumbersome and inefficient.
Arguably, we should have some of our best scientists occasionally tackle purely practical engineering problems, to shake up their research and expose them to fortuitous insights. Does this happen today? Perhaps through consulting with industry?
These are some of my preliminary conclusions from considering these case studies and from reading Pasteur’s Quadrant.
Pasteur’s quadrant
Link post
In my recent post on the case study of the transistor, we saw that the research that led to its invention did not fall neatly into the categories of “basic” vs. “applied”, but in fact cycled rapidly between them.
An entire book—Pasteur’s Quadrant, by Donald Stokes—is dedicated to the thesis that “basic” vs. “applied” is a false dichotomy that is harming science funding.
The core idea of Pasteur’s Quadrant is that basic and applied research are not opposed, but orthogonal. Instead of a one-dimensional spectrum, with motion towards “basic” taking you further away from “applied”, and vice versa, he proposes a two-dimensional classification, with one axis being “inspired by the quest for fundamental understanding” and the other being “inspired by considerations of use”:
I find these phrases somewhat cumbersome, given their centrality to the thesis, so let’s call them “discovery” and “invention” for short.
In Stokes’s classification, research aiming at discovery, with no thought of invention—“pure basic research”—is characterized by Bohr’s search for a model to explain the atom, and hence labeled “Bohr’s quadrant”. The opposite, “pure applied research”, or invention with no attempt at discovery, is characterized by Edison and his lab, who tinkered endlessly to engineer products such as the light bulb, with little heed to theory: “Edison’s quadrant”. But, crucially for Stokes, there is research that combines discovery and invention, motivated by both at the same time. “Pasteur’s quadrant” is characterized by the career of the great scientist who gave us both the germ theory of disease and the first engineered vaccines.
Stokes traces the history of the basic-applied dichotomy back to ancient Greece, where they had different words for different types of knowledge: episteme for scientific knowledge, and techne for the practical arts. Long before the Baconian program, episteme was not seen as the basis of techne—nor was it, at the time. Mathematics, astronomy, and natural philosophy were ends in themselves, pursued for the pleasure of knowing, not with practical goals in mind. Plato formalized this by elevating conceptual knowledge to a higher realm, of which daily life was a mere imperfect reflection. His influence extended all the way to 19th-century Germany, where the modern research university was conceived, as a place for scientists to pursue scholarship in complete freedom. This model was ultimately exported to the United States in the late 1800s.
The modern American research funding paradigm was essentially established by Vannevar Bush at the end of World War II. During the war, government greatly increased funding for research, and great strides were made: radar, penicillin, malaria drugs, the proximity fuse, and of course the atomic bomb. As the war was ending, researchers wanted to keep their government funding, but also feared government micromanagement. How could they have both money and freedom?
Bush’s solution was the vision laid out in his famous report, “Science, The Endless Frontier” (written at President Roosevelt’s request). In the report, Bush said that “basic scientific research” would lead to all manner of practical benefits:
But, paradoxically, basic research is not and cannot be explicitly directed at those benefits:
Therefore, “freedom of inquiry must be preserved”:
And later:
So in short, Bush’s message was: Invest in research with no thought of the return, and it will be returned many times over. Pump money into science, and it will trickle down to the economy. Give scientists absolute freedom to pursue their curiosity wherever it might lead, and it will ultimately lead to security and prosperity.
And he was not wrong. There is a large degree of truth in this message. But Stokes argues that Bush set up what I’ll call the “basic-applied dichotomy”, and that we need to overcome this and recognize the importance of Pasteur’s quadrant.
What’s the right way to categorize research?
I find Stokes’s two-by-two, if not quite compelling, then at least intriguing (and certainly better than the litany of prior approaches he outlines).
Naming the third quadrant after Pasteur is apt, because more than anyone else I know of, Pasteur’s career exemplifies the integration of science and engineering in a single mind. Tasked with improving the processes of French wine, beer, and vinegar makers, a mundane industrial engineering project aimed at iterative improvement, he showed the role of bacteria in fermentation, and discovered anaerobic metabolism—a breakthrough in microbiology. Decades later, when studying diseases of livestock, a purely scientific research project, a botched experimental setup gave him the clue that he followed to create the first engineered vaccine, a watershed invention in medicine. Clearly this was a man with the aptitude and the inclination to pursue both scientific knowledge and practical applications. And it was Pasteur who said, “There does not exist a category of science to which one can give the name applied science. There are sciences and the applications of science, bound together as the fruit of the tree which bears it.”
The case of the transistor, too, defies simple categorization as “basic” or “applied” research. It was an inventive goal that required the inventors, multiple times, to make an excursion into scientific theory and to advance our understanding of matter, before returning once again to engineering. Nylon, created at DuPont, was a case of an invention that arose fortuitously out of research into polymer chemistry.
But I don’t think we can understand these examples simply by putting discovery and invention on orthogonal axes and declaring that there is a quadrant at their intersection. What I see in these examples is that any project or lab, at any point in time, has a goal which is either discovery or invention. But the researchers were able to quickly pivot from one to the other, either from necessity or from opportunity.
So Pasteur’s fermentation work is a case of an inventive goal (improved processes) that turned into a more important scientific goal (understanding anaerobic metabolism). His vaccine work was the reverse: a scientific goal (understanding livestock diseases) that turned into a very valuable practical goal. The transistor work was a case of an inventive goal that required scientific goals for its completion. (The logical fourth possibility, a scientific discovery goal that required invention, could perhaps be represented by an innovative experiment such as the Michelson-Morley attempt to detect the ether, for which Michelson invented an interferometer.)
“Pasteur’s quadrant”, as described by Stokes, seems to be a type of research which is simultaneously motivated by discovery and invention. But what’s interesting about these examples is the rapid, flexible cycling back and forth between them.
If this mode of research is important, what are the implications for how research is funded, organized and managed?
First, we must have people, projects, and labs that can do both science and invention.
To have people who can do both, they should be trained in both. More importantly, there must be a role that embraces both. This affects evaluation, compensation, promotions, and overall career paths. Further, the role should be recognized by society. This encompasses everything from students learning about it as a career option, to accolades for the top achievers.
To have projects and labs that do both, they need to be set up, funded, and evaluated with this mode of research in mind. They need the freedom to pivot quickly between science and invention as the need or opportunity arises.
In particular, I think we need ambitious programs of invention that are willing to push the frontiers of knowledge—that is, to do science—in order to succeed. Such projects may need broad goals and loose timeframes (see again the transistor case). Who does this today? Corporate research labs don’t seem to be this ambitious anymore, and startups generally don’t have this kind of funding and aren’t able to take on this kind of risk.
We also need scientific research done by people who are capable of seizing the opportunity for invention when it comes along. Who does this now? At least some of this is done in university labs, but in between the invention and the market is a process of “technology transfer” with a reputation for being cumbersome and inefficient.
Arguably, we should have some of our best scientists occasionally tackle purely practical engineering problems, to shake up their research and expose them to fortuitous insights. Does this happen today? Perhaps through consulting with industry?
These are some of my preliminary conclusions from considering these case studies and from reading Pasteur’s Quadrant.