Gerald Holton, Hasok Chang, Edward Jurkowitz. American Scientist. Volume 84, Issue 4. Jul/Aug 1996.
Even in the best of times, managing science has been compared to herding cats; it is not done well, but one is surprised to find it done at all. In these days of diminishing resources, the analogy seems even more striking. Setting priorities for research, choosing which projects are to be supported and which abandoned, triggers epic battles at the highest levels. It requires predicting which paths and which mixture of policies might best advance science and lead to fruitful technologies.
Yet, in such debates, little attention is given to one of the most fundamental questions: What can historical cases teach us about what it takes to make a scientific discovery? There are many popular ideas abroad, often based on oversimplified textbook accounts of famous discoveries and on charming anecdotes. They have little to do with the unruly complexity of the events themselves, and can only mislead science policymakers.
For this reason, the authors of this article welcomed an opportunity to thoroughly investigate an informative case-the discovery of high-temperature superconductivity-which, having occurred just 10 years ago, is recent enough to permit reconstructing its context. Our investigation, which included interviews with Karl Alex Muller and Johannes Georg Bednorz, the physicists who discovered the first high-temperature superconductors, throws light on a set of problems of intense current interest: How does “curiosity-driven,” or basic, science interact with “strategic” research and engineering? How important are both planning and serendipity in discovery? What laboratory culture makes success more likely? How deeply are the roots of crucial ideas and apparatus buried in the soil of history? How important is the practice of borrowing across traditions and disciplines? What role do the private style and presuppositions of the individual play in research?
Our study demonstrated that scientific innovation depends on a mixture of basic and applied research, on interdisciplinary borrowing, on an unforced pace of work and on personal motivations that lie beyond the reach of the administrator’s rule book. While many of these findings may be familiar to students of scientific creativity, our operational mode of analysis, which is roughly comparable to the methods of genealogical research, makes them more precise, testable and generally applicable. As such they may serve as an empirical complement to some of the untested assumptions that inform policy discussions, especially the anguished debates in Washington and in corporate boardrooms over the relative merits of applied and basic research.
A Brief History
Superconductivity-the loss of electrical resistance below a critical, or transition, temperature (Tc) characteristic of the material-was first discovered in mercury by the Dutch physicist Heike Kamerlingh Onnes in 1911. Mercury becomes superconducting at just 4.2 degrees above absolute zero (4.2 degrees Kelvin). Teams large and small worked for decades in the hope of finding electrical conductors with higher critical temperatures, which would be easier and cheaper to keep resistance-free. There beckoned the rewards of both new theories to explain the phenomenon and of practical applications to exploit it; among the latter was the possibility of enormous new efficiencies in the transmission and use of electricity
But nature, for a long time, yielded little hope for real progress. By 1973, fully 62 years after the discovery of the phenomenon of superconductivity, all efforts had stalled at a Tc of 23.3 Kelvin, the critical temperature of a niobiumgermanium compound (Nb3Ge). After years of frustrating failures to boost TC into a region where there were realistic prospects for commercial use, hightemperature superconductivity was no longer considered a promising area. Some theories held that no higher T, could be expected. Bernd Matthias, a highly respected Bell Laboratories physicist who, together with collaborators, had discovered hundreds of new superconductors, challenged his peers to give up “theoretically motivated” searches, or “all that is left in this field will be these scientific opium addicts, dreaming and reading one another’s absurdities in a blue haze” (quoted in Bromberg 1995).
All this changed practically overnight in 1986, with the publication of a set of papers by Karl Alex Muller and his former student Johannes Georg Bednorz, two investigators at the IBM Zurich Research Laboratory in Ruschlikon, Switzerland. Unlike most of the previously discovered superconductors, the new compound was a ceramic, a mixed oxide of barium, lanthanum, and copper
(La2CuO4, or lanthanum cuprate, doped with a small amount of barium). Not only did it have a remarkably high TC-in the neighborhood of 30 Kelvin-it was relatively easy to prepare by ceramic techniques and to modify by chemical substitution. Whereas ground-breaking discoveries often involve new technology, in this instance the means to create and to measure the phenomenon had been available for decades.
The discovery became an academic and popular sensation, especially after Paul C. W Chu’s group at the University of Houston and Mao-Ken Wu’s team at the University of Alabama jointly announced in February 1987 that they had achieved superconductivity at about 90 Kelvin with materials related to the Bednorz-Muller compound, a temperature well within the range of the inexpensive coolant liquid nitrogen. Now high-school students could demonstrate the phenomenon. A climax of excitement was reached at the so-called “Woodstock of Physics,” a panel discussion on high-temperature superconductivity held at the American Physical Society’s annual meeting on March 18, 1987, in New York City Roughly 3,500 physicists crowded into the hotel where the meeting was held, some lingering so long after the session ended that they had to be ejected from the rooms by the hotel staff at 6 a.m. (Schechter 1989; Khurana 1987a; Robinson 1987).
Here was everything a physicist could wish for: a new class of materials with great potential for generating new theories and new technologies. Above all, the discoveries provided that most rare and most desired moment, a glimpse of vast unexplored scientific territory. Like Cortez’s men on the peak in Darien, the physicists at the meeting “look’d at each other with a wild surmise.” Or as a reporter put it: “One could have felt as if one were a part of a ceremonial gathering to affirm a new cult” (Kurana 1987a).
After the tumultuous emergence of high-temperature superconductivity even President Ronald Reagan hailed the “new age” of superconductivity as a welcome “revolution” having great promise for new products-Miller and Bednorz were awarded, with the maximum possible speed, the Nobel prize for physics for 1987. Their discovery unleashed the energies of dozens of teams, and laboratories all over the world rushed to synthesize other potential oxide superconductors. Indeed, it did not take long for the critical temperature to be raised to 125 Kelvin, and to even higher temperatures at high pressure. Today the record stands at 164 Kelvin, with isolated observations, often transient, being reported of critical temperatures well above 200 Kelvin (the freezing point of water is 273.16 K). The opium addicts’ blue haze has dissipated, and some physicists have even dared to hope again that room-temperature superconductors will eventually be found.
A First-Level Analysis
The main outlines of this discovery are well known, but our interviews and correspondence with Muller and Bednorz turned up essential details missing from other accounts. Here we set forth an account of the discovery of the first high-temperature superconductors as Miller and Bednorz experienced it, with particular attention to the resources, either intellectual or material, on which the discovery depended. Then, based on this narrative, we put forward a systematic analysis, a schema designed to help answer the more general question of what it takes to make a scientific advance.
Muller, who was born in Basel, Switzerland, in 1927, graduated from the Swiss Federal Institute of Technology (ETH) in Zurich in 1958. ETH was the home base of the physicist Wolfgang Pauli, who continued to teach there after winning the Nobel prize in 1945. Muller said of Pauli, “he formed and impressed me.” As we were to discover, the student had learned more than physics from his teacher. By 1963, Muller had joined the research staff of the IBM Zurich Research Laboratory, and in 1972 he was put in charge of the physics group there. In 1982 he was promoted to IBM Fellow, becoming one of a handful of distinguished scientists who were free to work on anything they pleased. He was to use that opportunity well.
Previously Muller had worked for almost 15 years on a series of problems in condensed-matter physics, many of which had links back to his doctoral research. His Ph.D. thesis, done under Georg Busch at the ETH, was on the identification of the electron paramagnetic resonance lines of iron ions, a subject quite unrelated to superconductivity. But as it happened, the material in which the iron ions were present as impurities was the then recently synthesized oxide strontium titanate (SrTiO3), and that fact, in a way nobody could have foreseen, would turn out to be Muller’s first step toward research on high-temperature superconductivity
Indeed, Muller’s use of strontium titanate was entirely accidental. Initially, he had set out to map the paramagnetic resonance spectrum of impurities in tin. When that worked out poorly, Muller explained to us, he went “by chance into Professor Heine Granicher’s office,” looking for crystals of other materials. Granicher offered Muller some samples, and among them was strontium titanate.
It was a fateful moment. Not only did strontium titanate help Muller to get his doctorate, it led him to study the crystallographic literature about the class of materials to which this compound belongs and set him on a road whose destination would become apparent only years later.
When he was made an IBM Fellow in 1982, Muller told us, he felt that since he had passed the age of 50, it was time for an entirely new challenge. Perhaps he remembered the advice of an old supervisor, H. Thiemann, whose byword had been: “One should look for the extraordinary.” In any case, Miller chose extraordinary conductivity as his next challenge.
At the time superconductivity was not a promising field of research. Not only had the incremental progress toward higher Tc apparently stalled, but IBM had abandoned the effort to produce a computer using Josephson junctions-electronic devices made of superconducting materials that can switch states faster than devices made of semiconductors-despite the enormous investments the company had made in this project.
Muller was aware of all of this. In 1978 he had spent an 18-month leave at IBM’s Thomas J. Watson Research Center in Yorktown Heights, New York. John Armstrong, the vice president in charge, wisely gave Muller discretion to pursue any subject he wished while he was there. That encouraged him to look into the troubled field of superconductivity, about which he then knew very little. As he put it, he started “from page one of Michael Tinkham’s book,” Introduction to Superconductivity. But thorough study turned up no theory that would lead beyond the usual materials to new substances and higher critical temperatures. Muller then “decided I just don’t talk to the theoreticians. They just held me back.”
After he returned to Zurich, Muller continued to work on superconductivity, first alone, and then from 1983 with Bednorz. Born in Neuenkirchen, Germany, in 1950, Bednorz was highly trained in crystallography, solid-state chemistry and physics. Muller and Granicher were supervising his Ph.D. thesis at the ETH; not surprisingly, Bednorz’s first experimental work was on the growth and characterization of strontium titanate.
Bednorz was an ideal partner for Muller. As Bednorz explained in their joint Nobel lecture, he had become interested in superconductivity in 1978, when he was invited by the IBM Zurich laboratory to improve the superconductive properties of strontium titanate single crystals. In this he quickly succeeded by adding trace amounts of niobium to the crystal. Yet the highest achievable TC was still only 1.2 Kelvin, so his IBM supervisor had lost interest, and Bednorz had returned to the institute to work on his thesis.
But the seeds of fascination with the field had been sown, and when Muller asked Bednorz in 1983 to join him in the search for a new superconductor, Bednorz accepted with such alacrity that it took Muller by surprise. Still, at the outset the two men spent a fruitless couple of years with nickel-based oxides. Right up to its culmination, their research was typically in the “little science” style, meaning on a relatively small budget. Bednorz later described it as a stage on a “long and thorny path.” Moreover, they worked in self-imposed isolation. Muller told us that they kept their early work completely to themselves, not informing even the IBM managers, in part because superconductivity research was not then a popular subject with management. This decision, made possible by Muller’s status as IBM Fellow, was also taken so that if they failed, they could quietly give the project “a burial in very restricted family circumstances, in order not to jeopardize Bednorz’s career.”
The breakthrough came when they decided to look for superconductors among copper-containing oxides, a class of materials fundamentally different from those that had been ransacked by the pioneers in the field, such as Matthias. During a literature search Bednorz happened on a 1985 paper by Claude Michel, L. Er-Rakho and Bernard Raveau of the Universite de Caen that described barium-doped lanthanum cuprate. But the authors were chemists and had concentrated on catalytic rather than superconducting properties.
The decision to investigate the oxides, which is a key turn in this story, “took every condensed-matter physicist by surprise” (Chakravarty 1994). Indeed one physicist recently confessed to us that when he and his colleagues had heard Muller “was searching for high T, in oxide, we thought he was crazy” Up to that time searches had concentrated on intermetallic compounds; ceramic oxides were generally thought to be insulators, not conductors, much less superconductors. But according to their joint Nobel prize lecture, the team’s “aim was primarily to show that oxides could do better in superconductivity than metals and alloys.”
They had several reasons for striking out in this new direction. Some oxides, including strontium titanate, had previously been found to be superconductors of the traditional sort, although with Tc’s no higher than 14 Kelvin, they ranked well below the niobium compounds. As Muller and Bednorz later noted, they were also reasoning from the then-standard theory for superconductivity-the BCS theory, named after physicists John Bardeen, Leon Cooper and Robert Schriefferand the Jahn-Teller theorem devised by physicists H. A. Jahn and Edward Teller. This is one of the interesting ironies of the story, because it is now thought that the BCS theory has only limited applicability to high-temperature superconductivity and that the Jahn-Teller effect has little to do with establishing superconductivity in the high-temperature superconductors. Yet because these theories were components in Muller and Bednorz’s motivation, they merit a brief summary.
According to the BCS theory, superconductivity arises from the interaction of phonons, or vibrations of the atomic lattice, and electrons. In most metals, phonons scatter individual electrons. Under certain conditions, however, the interaction between phonons and electrons causes some electrons to couple together to form what are called Cooper pairs. At sufficiently low temperatures, these electrons move as a coherent group through the solid. Because thermally excited phonons are too weak to disrupt the entire group, the flow of electrons persists indefinitely, making the material a superconductor. Muller and Bednorz expected oxides with mixed valence states to exhibit particularly strong electron-phonon coupling. Barium-doped lanthanum cuprate met this criterion.
They also thought a material that exhibited a strong Jahn-Teller effect would be a good candidate. Some solids are so constituted that as an electron moves through them, positively charged ions (atomic nuclei with their inner-shell electrons) markedly shift toward the electron, and negatively charged ions shift away from it. The electron is accompanied by a cloud of phonons that result from this deformation of the atomic lattice. Together the electron and the phonons are called a polaron, an entity whose effective mass depends on the displacement of the ions. This mechanism appeared to allow for the persistence of the superconducting state at higher temperatures, whereas the normal BCS mechanism implied that the superconducting state would not, in general, persist at higher temperatures.
Miiller had read a paper by KarlHeinz Hock and H. Nickisch of the Technische Hochschule in Darmstadt, Germany, and H. Thomas of the Universitat Basel in Switzerland (Hock, Nickisch and Thomas 1983) that led him to think that a material that met the Jahn-Teller criterion and was metallic at high temperatures might have an unusually high Tc The lanthanum cuprate met those criteria as well.
But, as Muller told us, there was another crucial factor: the attraction that he in particular felt toward that substance because it had a perovskite-type structure. This structure had special meaning for Muller; he said he had an “atavistic type of feeling that it might work for superconductivity.” When he and Bednorz came to deliver their joint Nobel lecture, they gave it the significant title, “Perovskite-type OxidesThe New Approach to High-Tc Superconductivity.”
Perovskites, named in 1830 in honor of the Russian amateur geologist Lev Aleksevitch von Perovski, are a class of ceramics that have a particular atomic arrangement. In their ideal form perovskites, which can be described by the general formula ABX3, consist of cubes that are decorated with three elements. The A cation (positively charged ion) lies at the center of each cube, the B cations occupy all eight corners and the X anions (negatively charged ions) lie at the midpoints of the cube’s 12 edges. The cubic structure has particular appeal because, of the seven possible crystal systems, it is the one with the highest degree of symmetry.
As we saw, Muller and Bednorz had each devoted their graduate research largely to the perovskite strontium titanate. Muller later wrote that “the perovskite structure determined, even dominated, my scientific efforts for many years” (Muller 1988). Indeed, in Muller’s extensive bibliography, perovskites recur in widely varying studies, ranging from paramagnetic resonance to sound attenuation and heat capacity, from structural phase transitions to photochromism. For example, Muller gave special attention to perovskites in a decade-long investigation of the manner in which the Jahn-Teller effect can lead to structural phase transitions (Thomas and Muller 1972).
As Muller emphasized, perovskites “always worked” for him. This highly symmetric structure became for him a thematic guide, quite different from and supplementary to the elements traditionally considered central to the logic of scientific research. We recognize that Muller, in this tendency, joins many other scientists who found themselves being led by thematic commitments, at least during the early, rather private stages of their projects. Einstein, for example, had a predilection for symmetry, continuity and classical causality, whereas Heisenberg embraced discontinuity and abandoned classical causality In Muller’s case the thematic influence on the scientific imagination was just as compelling, as we shall see.
After reading the French paper about barium-doped lanthanum cuprate, Bednorz and Muller prepared the compound and showed that it became superconducting at a temperature of about 30 Kelvin, a Tc substantially above that of any previous material. They also confirmed that the sample exhibited another important indicator of superconductivity, the Meissner effect: When a superconductor in a magnetic field is cooled to the temperature at which it loses resistance, all or part of the magnetic flux within the material is expelled. Still, Bednorz and Muller initially found that their reports were “met by a skeptical audience” (Bednorz and Miller 1987b). But soon the confirmations came pouring in, and research groups grew explosively the world over.
A Second-Level Analysis
For a serious study of what it took to make this discovery and what lessons it implies, we must press on beyond this sketch of events to a deeper level, where the resources that history had prepared for the success of the team lie hidden. A complete analysis would take into account in more detail the personal research trajectories of Miller and Bednorz, evaluate the influences of encounters with other researchers, and thoroughly explore the educational systems through which they passed, as well as the universities and corporate institutions that employed them. Here we concentrate on the vast treasury of intellectual and material resources that these two scientists were able to exploit. On the basis of this case history, we then generalize, proposing a structured description of how new scientific work is rooted in and nourished by previous achievements, some from the distant past.
It is often said that scientific work is “based on” earlier work, or that earlier work “gave rise to” later work; there is also much talk of “traditions,” “influences” and “connections.” These notions, we believe, must be made more precise to be useful. In particular, we seek to operationalize them, that is, to define them in terms of identifiable and repeatable operations.
By resources we mean mathematical techniques, physical laws, analytical instruments, factual information and the like. Although an investigator may well create some such resources on the spot, more frequently they are derived from previous work done by others. Indeed the most important relation between scientific research efforts is that of adapting, assimilating, transforming-or in general “borrowing”whether consciously or not.
Such borrowing leaves identifiable traces, just as one can discern one’s ancestors’ traits in one’s own makeup. To pursue this suggestive metaphor, it should in principle be possible to reveal many “generations” of “ancestors” that lie behind a scientific work. In short, “influence” can be operationalized by attempting to tease out the genealogy of a work by looking for documentable facts that are equivalent to a line of inheritance.
One way to locate the resources that were used in a given piece of scientific work is to trace the citations to publications or to private communications it contains. To be sure, citations cannot be used blindly, because they may be merely pro forma, intended to acknowledge the existence of related projects in the same field, or to serve other, largely social purposes. A second problem is that not all important resources are explicitly cited. Many resources will be considered generally known and silently assumed. The scientific genealogist, therefore, must rely on his or her own scientific and historical background knowledge to find implicit citations in the target paper or in the ancestral papers. Finally any genealogical exercise is open-ended; how far back to trace the connections is a pragmatic decision. We have found that it is not necessary to go back farther than three or four “generations” to test interesting hypotheses about scientific innovation.
A genealogical analysis of Bednorz and Muller’s main scientific publications announcing the discovery of high-temperature superconductivity shows the need to distinguish among the various types of resources on which the team drew. They made use of at least four sets of resources: initial, motivating theoretical framework and ideas (schema); experimental techniques and material resources (production); means of gathering and analyzing data (observation); and theoretical concepts for interpreting the results (interpretation).
Analysis of the original five papers that comprised the announcement of their breakthrough quickly reveals a number of silent resources that Muller and Bednorz put to use. For example, among the tools for observation were several standard techniques no longer referred to explicitly in research reports: x-ray powder diffraction for analyzing the structure of the sample and various electrical resistance thermometers, among others. Similarly the theoretical resources needed to interpret the experimental results included some long considered commonplace and whose original sources were not cited, such as the criteria for identifying superconductivity: zero electrical resistance and the Meissner effect.
Figure 7 shows that each resource can be connected either to one of the twodozen publications explicitly referred to in the Bednorz-Muller papers or to a publication implicitly cited in their papers. For example, the passing reference to the Meissner effect implicitly refers to the 1933 publication describing the effect by German physicists Walther Meissner and Robert Ochsenfeld. Similarly, the platinum thermometers the teams used imply reference to an 1887 publication by Hugh L. Callendar of the Cavendish Laboratory in Cambridge that ushered in the resistance thermometer as a practical means of measuring temperature.
It doesn’t take long for the BednorzMiller work to reveal a broad and intricate system of ancestors. Our search revealed many cross references among early resources and also quickly took us back to work done a century or more ago. Unwittingly but documentably the stage for the 1986 discovery was set by scientists, many long in their graves. For instance, the apparatus commonly used to liquefy helium today stems from a liquefier developed by the MIT engineer Samuel C. Collins in 1947, whose predecessor was the Russian physicist Pyotr Kapitza’s 1934 liquefier, which in turn made use of two principles of cooling first laid out by British physicists William Thomson (Lord Kelvin) and James P. Joule in the 1850s and by the French chemists Nicolas Clement and Charles-Bernard Desormes in 1819.
Obviously, this network must be extended to yet earlier generations. Moreover, if one focused on any one node-say the BCS theory of superconductivity-it would reveal a broad and intricate network of its own. That, of course, is the point: In an operationally meaningful sense we begin to perceive “what it took” to discover high-temperature superconductivity. We can generalize that any significant advance relies on a large but identifiable set of earlier contributions. Some may be famous and profound, many more are much less significant in themselves. But all have served, almost always unwittingly, to prepare for the emergence of the new scientific or technological achievement.
The Private Dimension
As we have noted, tracing the genealogy of a scientific discovery through the published literature does not uncover every factor of relevance to it. Perhaps the most intriguing needed addition is the private dimension of scientific discovery. Because of the tradition of formality in science writing, this aspect of discovery rarely survives in the published record. But we were lucky. When we asked Muller to elaborate on his remark that the perovskite structure “always worked” for him, he obliged us by sharing in some detail an aspect of his motivation that would ordinarily be kept private.
His unlikely choice of a perovskite in his search for high-temperature superconductors was guided not just by the force of (well-rewarded) habit. As he put it: “I was always dragged back to this symbol.” He first became fascinated with this highly symmetrical structure in 1952, when he was working on his doctorate. Wolfgang Pauli, who as we have mentioned was one of Muller’s professors at ETH, had just published an essay on the influence of archetypal conceptions in the work of the astronomer Johannes Kepler in a book coauthored with psychoanalyst Carl Jung (Pauli 1952). Much impressed by that essay, Muller started to read Kepler avidly, thus encountering Kepler’s deep commitment to the guidance of three-dimensional structures of high symmetry-the five Platonic solids-in his work on planetary motion.
Muller continued, “If you are familiar with Jung’s terminology, the perovskite structure was for me, and still is, a symbol of-it’s a bit highfetched-but of holiness. It’s a mandala, a self-centric symbol which determined me…. I dreamt about this perovskite symbol while getting my Ph.D. And more interesting about this is also that this perovskite was not just sitting on a table, but was held in the hand of Wolfgang Pauli, who was my teacher.” At the time, Muller had divulged this aspect of his inspiration only to friends and to Pauli’s last assistant, Charles P. Enz. He has since discussed it in an introspective essay (Muller 1988) illustrated with the Dharmaraja mandala.
To the historian this is familiar ground. Scientists from Kepler to Kekule, from Newton to Crick and Watson, were guided in the early stages of scientific research by a visually powerful, highly symmetric geometrical design. In faithfulness to Muller’s self-report, our genealogy should include a new type of resource, “personal thematic presuppositions,” and with it a new line of inheritance, reaching back first to Pauli and Jung and then to the works of Johannes Kepler four centuries earlier. This added intellectual resource played as big a role in motivating the 1986 discovery as any of the other resources we have mentioned. Other personal thematic presuppositions of various sorts are found to be essential motivators in major advances throughout the history of science. Some Testable Hypotheses What can we learn about scientific discovery in general from this genealogical analysis of a particular advance? We offer four hypotheses that may be found to hold generally for modern science. Although students of scientific discoveries will not find them surprising, we would contend that our genealogical method of analysis has allowed these hypotheses to be put in a more testable, and therefore more useful, form.
Borrowing of resources routinely takes place between different traditions within a conventionally defined discipline. For instance, among the theoretical ancestors of the Bednorz-Muller work are ideas from thermodynamics, statistical mechanics, the old quantum theory, quantum mechanics and quantum field theory. Even when a given work superficially appears to be the result of a narrow line of research, it is likely to have a deep and broad ancestry. When scientists borrow from different subfields, these can blend together or be transformed in an alchemical process that turns them into gold. One may also note that the unpredictable way scientists reach back to earlier research in a different part of the discipline suggests it would be futile to attempt to “rationalize” or “direct” this process but argues for making a scientific education as wide-ranging as possible.
Borrowing of resources also routinely occurs across traditional boundaries between disciplines. The Bednorz-Muller work borrowed directly or indirectly from a wide variety of disciplines, each with its own professional societies and journals. They included physical chemistry, material science, crystallography, metallurgy, electronics and low-temperature techniques. This feature, most obvious in experimental projects but also found in theoretical ones, has, we suggest, become more and more characteristic of modern scientific work.
Basic research borrows resources from applied research, and applied research borrows resources from basic research. A good example of this symmetrical exchange is Bednorz and Muller’s use of a SQUID (superconducting quantum interference device) to measure changes in magnetic fields. The initial pursuit of superconductivity can be regarded as basic, or “curiosity-driven.” So can Brian Josephson’s prediction that superconducting currents can tunnel across an insulating film. But then the Josephson effect led to the production of SQUIDs, making possible exquisitely sensitive magnetic susceptometers, whose development is considered a piece of applied work. The susceptometers, however, proved useful in further basic research into superconductivity, including Bednorz and Muller’s. In short, to use a metaphor from physics, the exchange of energy between pure and applied research resembles the exchange of energy between a pair of coupled pendulums. Such feedback effects can be observed even within discipline-oriented research lines.
Our findings emphasize the great importance for scientific research of unintended interactions or applications. Most borrowed resources had been developed by others in research with a goal quite different from that of the eventual borrower. Moreover, the research of the borrower also often ends up somewhere other than the intended destination; for example, Onnes’s initial discovery of superconductivity was based on ideas of Kelvin’s, which predicted “exactly the opposite of what was found eventually” (Meijer 1994). As we have noted, Bednorz and Muller discovered high-temperature superconductivity by studying a compound that had been synthesized and researched by others for unrelated purposes. Nor could the team have predicted that now, a decade after their discovery there are over a hundred high-temperature superconductors as well as a growing set of industrially promising applications motors, transformers, thin films and power cables some of them already on a production basis. Moreover, all of this has transpired in the continued absence of any consensus about the mechanism of high-temperature superconductivity.
The Miller-Bednorz story, replete with unpredictable turns of events and rife with unintentionality, has yet another twist. As we noted, the perovskite structure inspired Mi.ller and Bednorz to gamble on investigating the oxides in the first place. Their barium cuprate compound contained well-separated planes of copper and oxygen atoms, and these layers turned out to be a universal property of high-temperature superconductors. Moreover, these layers exist because the compound is not, after all, a true perovskite; because of the way its unit cells stack, it has orthorhombic rather than cubic symmetry. As Muller said to us in this connection, although Kepler tried to decompose planetary orbits into perfect circles, he was led to ellipses instead-but thereby helped prepare for Newton’s Principia.
Unity in Science
If the four hypotheses we developed are more generally confirmed, they will have the effect of providing support for the old assumption that there is some underlying unity in science, perhaps not of the Theory-of-Everything variety but of a different, operational kind.
A distinguished and vocal minority of scientists (including Philip W Anderson, who won a Nobel prize for his work on the theory of superconductivity) has asserted that we should not look for unifying theories emerging from the study of elementary particles, and that each area of science, such as biology or fluid dynamics, has its own laws, which cannot be derived from something more fundamental. Those arguments, whether right or wrong, do not touch our idea of unity, which is exemplified in the ceaseless borrowing connecting diverse traditions and disciplines. In principle, any two research efforts, however removed in time, subject or purpose, may turn out to be genealogically connected. And in the limit, the whole of natural science may be represented as one thickly linked continuum, which can be divided into distinct disciplines and traditions only in a more or less arbitrary way. However they may differ, the multitudinous projects of science share in and emerge from a common history.
Implications for Science Policy
This study has significant implications for science policy. It suggests, first of all, that far more attention should be paid to the history of actual advances. They demonstrate, in operational terms, that major accomplishments in science depend on healthy systems of education and research administration that nurture a mixture of basic, applied and instrument-oriented developments. The traditions and management styles of laboratories and their parent institutions can greatly advance or hinder research. At the Zurich laboratory Muller and Bednorz benefited from access to highly trained machine and glassblowing technicians, schooled in the traditions of excellence and craftsmanship that can be traced back to the guilds of previous centuries. Then too, it was probably not an accident that their discovery, which is basically an advance in the science of materials, occurred at a laboratory with a long-standing commitment to this science, most notably to the study of ferroelectricity
But the most striking feature of the culture at the Zurich laboratory was the willingness to give good people the freedom to pursue projects with long gestation periods. This was rewarded twice in quick succession. The year before Bednorz and Muller won the Nobel prize in physics, it had been awarded to Gerd Binnig and Heinrich Rohrer, also of the Zurich laboratory, for their patient development of the scanning tunneling microscope. The stories of the transistor and the laser also suggest that the chance of serendipitous encounters with key ideas is increased by permitting research to proceed at an unforced pace.
We recognize here the well-known phenomenon of the self-amplification of self-confident, successful, high-quality cultures. They exhibit what Robert K. Merton of Columbia University, who pioneered the modern sociology of science, has memorably termed the Matthew Effect (a reference to the text: “Unto every one that hath shall be given, and he shall have abundance…” Matthew 25:29).
It is equally important that the system of research administration encourage the flexibility that promotes borrowing within and across disciplines and between basic and applied research. The culture of the laboratory, including its financing, should allow both a natural, unforced pace of work and a degree of self-direction that allows researchers to draw on the personal sources of inspiration on which administrative rule books and traditional science texts are so silent.
But above all, our research suggests that the current debate about the relative merits of and support warranted for basic and mission-oriented research is oversimplified. Historical study of cases of successful modem research has repeatedly shown that the interplay between initially unrelated basic knowledge, technology and products is so intense that, far from being separate and distinct, they are all portions of a single, tightly woven fabric (Mort 1994; Ehrenreich 1995). Even research that narrowly targets a specific application sooner or later must rely on results from a wide spectrum of research areas. Thus it is still sometimes said that Irving Langmuir looked into blackened light bulbs and so created modern surface chemistry. But of course his achievement did not spring full-fledged from his brow. Its genealogy, if traced back as carefully as we have traced the genealogy of Bednorz and Muller’s discovery, would quickly reveal the crucial role of many types of research in earlier generations. If we wish to achieve noteworthy science, even if noteworthy is defined to mean only science with an economic payoff, the nation has no alternative but to support the seamless web of research. Acknowledgments We gladly acknowledge advice on early drafts received from J. Georg Bednorz, George Benedek, Henry Ehrenreich, Theodore H. Geballe, Marc A. Kastner, K. Alex Muller and Michael Tinkham. One of us (Holton) is also grateful for support of this study from the Andrew W. Mellon Foundation.