If a philosopher were writing this book, we would begin by defining the terms discovery and invention (or perhaps dismissing them as useless concepts because they are so hard to define). Instead of beginning with definitions, I will offer examples illustrating discovery and invention. I will use the same examples to introduce most of the other concepts we will use throughout the book. Then in Chapter 2 we will take a more rigorous look at these terms, using the cognitive science literature. But the primary goal of this chapter is to give us a sense of the diverse range of activities to which labels like discovery and invention are applied.
The roads by which men arrive at their insights into celestial matters seem to me almost as worthy of wonder as the matters themselves (Kepler, quoted in Gentner et al., 1997, p. 403)
Kepler propped himself against the wall and watched the goatish dancers circling in a puddle of light from the tavern window, and all at once out of nowhere, out of everywhere, out of the fiddle music and the flickering light and the pounding of heels, the circling light and the Italian's drunken eye, there came to him the ragged fragment of a thought. False. What false? That principle. One of the whores was pawing him. Yes, he had it. The principle of uniform velocity is false. He found it very funny, and smiling turned aside and vomited absent-mindedly into a drain. (Banville, 1981, p. 72)
The above quotation comes from the novel Kepler by John Banville. It is a classic romantic account of discovery--the flash of insight that leads to Kepler's Second Law comes in the midst of a drunken revel. The false principle of uniform velocity refers to the widely-held assumptions that each planet orbited the Earth, or the Sun in the Copernican system, at a constant speed in a circular orbit. Kepler's Second Law states that if you draw an imaginary line between a planet and the sun, then look at the area swept out by that line at two equal intervals anywhere on the planet's orbit, the areas will be equal.
Banville's novel is based on Arthur Koestler's The Sleepwalkers (Koestler, 1963), in itself an inspiring, romantic account of Kepler's tortured path to his discoveries. Kepler developed an early model of the solar system in which the five Pythagorean perfect solids could be put in the five intervals between planetary orbits: in between the spheres of Saturn and Jupiter he placed a cube, between Jupiter and Mars a dodecahedron, and so on. This model gives us an insight into the view of the solar system Kepler had to transcend. We think of planets as having orbits through space, but before Kepler's time, they were thought to ride on giant spheres; therefore, the orbits had to be perfectly circular. Kepler's perfect solids were therefore inserted between these spheres.
This geometric relationship served Kepler as a mental model of the solar system. In the next chapter, I will discuss the psychological literature on mental models at length. For now, it will suffice to say that a mental model is a three-dimensional representation of a system that a scientist or inventor can manipulate in his or her imagination. Frequently, this sort of model is also sketched or prototyped. Kepler convinced Frederick, Duke of Wittemberg, to have his silversmiths create a drinking cup based on Kepler's nested spheres and geometric shapes; when the Duke agreed, Kepler created a paper model. Plans for the drinking cup expanded into a clockwork planetarium. In the end, it was never built (Koestler, 1963). But this hands-on experience is an important aspect of mental models, which are tactual. One of the themes of this book will be the way in which the hands and devices built with them serve as extensions of the mind.
Mental models differ from formal theoretical models in their incompleteness, their fuzziness; they represent the kind of system a discoverer hopes to find, or an inventor hopes to create. Even though the geometric model failed to fit the data and Kepler abandoned its literal form, it still survived as a mental model of what he was trying to achieve. Kepler later added the possibility of a correspondence between musical harmonies and planetary orbits; he explored quite a number of relationships and thought to the end that this approach held promise (Stephenson, 1994). Kepler was convinced there was an underlying harmony that governed the planetary orbits, and that it depended on the sun, which was the center of the solar system in more ways than one: it served "as the mathematical center in the description of celestial motions; as the central physical agency for assuring continued motion; and above all as the metaphysical center, the temple of the Deity" (Holton, 1973, p. 81).
Beginning in 1600, Kepler worked at the observatory of Tycho Brahe, first as Tycho's collaborator and then, when Tycho died after eighteen months, as Imperial Mathematicus. Tycho had the best observational data on the positions of the planets, data Kepler had to cajole out of him in little pieces until Brahe died. The most perverse of the planets was Mars. Kepler struggled for five years to fit four of Tycho's observations of Mars into a circular orbit. Then, when he finally succeeded, he managed to wrestle two more observations from Tycho, and these did not agree. The amount of error was only eight minutes of arc, but for Kepler it was enough to disconfirm his current orbital model: "he refused to accept an error of 8 minutes of arc because he believed Tycho's observations were a gift from God and hence deserved to be given utmost importance" (Job Kozhamthadam, 1994, p. 88).
Here again the Kepler case allows us to preview an issue that we will take up at greater length later. The philosopher Karl Popper argued that science advances not by embracing new truths, but by a ruthless willingness to discard old ideas which no longer fit new data (Popper, 1959). Much of the work of discarding is done as a group process: one scientist or group of scientists adheres strongly to an idea, another seeks to disprove it, and so the idea either holds up or is discarded. But successful discoverers and inventors have to do a certain amount of their own testing--have to be willing to abandon cherished hypotheses. In hindsight, this appears easy--why wouldn't Kepler simply throw out circular orbits. One has to realize that circularity was not just a hyopothesis in Kepler's time. Planetary orbits were governed a complex series of interconnected spheres (Margolis, 1993). Kepler's observations literally threatened to shatter the spheres.
Kepler had already thrown out uniform motion. Circular motion followed, but not before he arrived at his Second Law:
Since I was aware that there exists an infinite number of points on the orbit and accordingly an infinite number of distances [from the sun] the idea occurred to me that the sum of these distances is contained in the area of the orbit. For I remembered that in the same manner Archimedes too divided the area of a circle into an infinite number of triangles (Kepler quoted in Koestler, 1963, p. 329).
According to Koestler, Kepler knew that his assumptions about area and circular orbits were not quite right, but he claimed they canceled each other out, allowing him to propose the Second Law.
Now he returned to Mars' orbit; if it were circular, three observations should suffice to determine its path. But the path suggested by one set of three observations did not agree with the path suggested by another, indicating that the orbit was not a circle. He rejected the possibility that the observations were in error. An oval fit the orbit better, though even that was not perfect (Job Kozhamthadam, 1994).
For Kepler, observational reasons were never enough--there had to be an underlying model that explained the planetary orbits. Here he came up with another mental model based on an analogy with a ferry (Gentner, et al., 1997). The current supplies the main force, in a way analogous to the sun, but there were forces originating from the boat itself--the ferryman's rudder, the cord and pulley connection to the shore. Just as the clever ferryman could guide his in a circular path by using the rudder to take advantage of the currents, so the planets could move in circles while being swept by the power emanating from the sun.
But planets have no ferryman and no rudder. So Kepler evolved yet another analogy. He imagined the planetary orbit as a kind of 'magnetic river', with the poles of the planet alternately attracted to and repelled from the sun (Gentner et al., 1997; Job Kozhamthadam, 1994).
The point is, Kepler's evolving mental model of planetary motion had come to preclude the possibility of a circular orbit. If a planet is alternately attracted and repelled by the sun, then its orbit cannot be a circle. He settled on an oval, which did not perfectly fit the data, but gave results superior to a circle. He knew this was not entirely satisfactory, however, and spent another eighteen months wrestling before he realized that the orbit could be described by the equations governing an ellipse. The result was his First Law, discovered after his second.
Kepler published his two laws in 1609 in a work boldly entitled "A New Astronomy Based on Causation or a Physics of the Sky." The title reveals Kepler's other heresy. The laws or principles governing what we would now call the physics of the heavens were supposed to be totally different from those that operated on Earth. Kepler thought differently; as we have seen, his evolving mental model presumed not only a geometric regularity to the planetary orbits, but a physical connection between the planets and the sun: "so intense was Kepler's vision that the abstract and concrete merged." Here we find the key to the enigma of Kepler, the explanation for the apparent complexity and disorder in his writing and commitments. In one brilliant image, Kepler saw the three basic themes or cosmological models superimposed: "the universe as physical machine, the universe as mathematical harmony, and the universe as central theological order." (Holton, 1973, p. 86). Of particular note here is the combination of the abstract and the concrete into a powerful mental model that guided his effort.
The Third Law emerged from this mental model. "He had been searching for this Third Law, that is to say, for a correlation between a planet's period and its distance, since his youth. Without such a correlation, the universe would make no sense to him; it would be an arbitrary structure. If the sun had the power to govern the planet's motions, then that motion must somehow depend on their distance from the sun; but how? Kepler was the first who saw the problem--quite apart from the fact that he found the answer to it, after twenty-two years of labor. The reason why nobody before him had asked the question is that nobody had thought of cosmological problems in terms of actual physical forces." (Koestler, 1963, p. 395) Briefly put, the resultant law states that the cube of a planet's distance from the sun will be proportional to the square of its orbital period around the sun.
According to Job Kozhamthadam (Job Kozhamthadam, 1994, p. 8), Kepler "announced this law without providing any clear clue as to how he arrived at it." According to Koestler, Kepler discovered it by 'patient slogging'.
Recently, a group of researchers in Artificial Intelligence have created a computer program called BACON that, among other things, discovered Kepler's Third Law via the same sort of patient slogging--or what the program's authors call 'data-driven discovery' (Langley, 1987). Essentially, the program takes two columns of data, one containing the distance of a planet from the sun (D) and another its period of revolution (P), and applies a set of heuristics to this data.
A heuristic is a rule of thumb, a shortcut that one can use to reduce the size of the problem space when seeking a solution. Obviously, there are hundreds of possible relationships that could be used to link two columns of numbers; one needs either a mental model, or a set of heuristics, or both to reduce the possibilities to a limited solution space. In the next chapter, we will say more about the cognitive literature on heuristics.
The earliest version of BACON used three heuristics, which are shown in Figure 1.
Figure 1: BACON.1's Heuristics. Adapted from Michael E. Gorman, Simulating Science (1992) with the permission of the Indiana University Press.
Each of these heuristics was applied whenever its conditions for execution were met. As indicated in Figure 1, the second heuristic was applied first, resulting in the ratio D/P, then the third heuristic was applied twice to produce D2/P and D3/P. This last ratio is a constant. Voila! BACON had discovered Kepler's Third Law in a matter of seconds, leading Herbert Simon, one of the architects of BACON, to wonder why it took Kepler so long. Furthermore, four out of a sample of fourteen students, given the same two columns of numbers but no information about heuristics, made the same discovery (Qin, 1990). The solvers included a graduate student and an undergraduate in physics, and a graduate student and an undergraduate in chemical engineering. All the students were allowed to use calculators, and their processes were described at length. None of them knew the data had anything to do with Kepler's laws. The authors concluded that data driven discovery "was found to proceed in the same manner as many other problem-solving processes that have been studied and described. We believe that this result can be generalized to cover most, perhaps all, of the processes of scientific discovery" (Qin, 1990, p. 308) .
Here we have the first hint of how students can be turned into discoverers like Kepler--make them into good problem-solvers. Of course, making students into good problem-solvers is not trivial; we will talk more about this issue later in the book. But no special genius or magic is required for discovery.
The portrait of Kepler that emerges from historians and novelists resembles one of the mythical heroes described so eloquently by Joseph Campbell , involving several stages: a call to adventure, that takes the hero (or heroine) away from the ordinary world; a journey into the unknown, in which the hero is required to perform superhuman feats; and a return bearing a boon that benefits her tribe or, in some cases, the entire planet.
Like Arthur and his knights, Kepler begins with a vision of a Holy Grail, a model of the solar system that could be nested in a silver cup. But this is a fleeting vision; like the knight-errant, he has go on a long journey, with Brahe as both helper and tormentor and Mars as a kind of monster he has to battle. After twenty-two years of struggle, he returns with his three laws, which Newton uses to create a new model of the universe.
If we adopt this perspective, students will need to become more than good problem-solvers to become discoverers; they will have to go on the kind of hero (or heroine's) journey discussed by Campbell.
The portrait that emerges from machine discovery is different. If a computer program can discover, then it diminishes the heroic, mythical stature of the human discoverer. It took poor old Kepler years to do what a machine does in seconds, and a science student with a calculator does in an hour or so--the data was right there, in a form anyone could recognize.
But what about finding the problem? Can we not give Kepler credit for realizing that there had to be a regular pattern of the form suggested by his third law? After all, he was not given two columns of numbers and asked to find the relationship. Qin & Simon counter that,
It is sometimes argued that the real problem of scientific discovery is not to find laws in the data, but to define the problem and to discover the relevant data. But it has just been seen that defining the problem and discovering the data were not Kepler's primary contribution. He inherited the problem of describing the heavens parsimoniously from a long line of predecessors, and the data, as explained above, were mainly inherited from Brahe and Copernicus. His merit was that he converted the data into a form that revealed the geometry of the heavens and laid the foundation for Newton's inertial and gravitational explanation. From a scientific standpoint, his attempts to provide "physical" explanations for his empirically derived laws are now only historical curiosities (Qin, 1990, p. 306).
One of the questions raised by this book will be whether beliefs like Kepler's faith in a geometrical relationship between the sun and the planetary orbits are central to discovery, or whether they are epiphenomenal. To put it in other terms, was Kepler's mental model simply irrelevant, perhaps even a distraction? Was his discovery really just about number-crunching and curve-fitting?
Qin & Simon pose Kepler's problem as 'describing the heavens parsimoniously'. That is, of course, too broad a statement to narrow the problem space significantly. Instead, Kepler created a new problem: how to discover a relationship based on geometric and/or musical harmonies between the sun, planetary distances, and periods of revolution.
No one else had put the problem in this form. Copernicus did locate the sun more centrally than the Earth but the actual center of the solar system was a point near the sun. Copernicus also believed in perfectly circular orbits with planets moving at uniform speeds. Brahe still believed in an Earth-centered solar system, with several planets circling the sun, which in turn circled the Earth. Kepler, in contrast, put the sun at the actual center of the solar system. This made his problem of 'describing the heavens parsimoniously' different from Copernicus', or Brahe's, or anyone else's at his time. As Simon himself said, "solving a problem simply means representing it so as to make the solution transparent" (Simon, 1981, p. 153).
BACON represents the problem as finding a relationship between two columns of data, using heuristics that dictate the relationship will resemble Kepler's third law. It could be programmed to search for a different kind of relationship. Collins (Collins, 1990) argued that discoveries like BACON's only work if one narrows the choices to Third Law or no law and if one has perfectly accurate data. Kepler's original data regarding Mercury did not fit his Third Law with complete precision (Stephenson, 1994) but he was convinced of the relationship on theoretical as well as empirical grounds and therefore did not abandon his new hypothesis. If one introduces the possibility of small errors into BACON's data, then it increases the probability that a program armed with more heuristics could discover other numerical relationships.
In Kepler's day, there was serious argument about whether scientific theories were primarily heuristic devices for describing the results of calculations or whether they corresponded to underlying realities. Cardinal Bellarmine, who eventually condemned Galileo, put it this way:
To say that the supposition that the earth moves and the sun stands still all the appearances are saved better than on the assumption of eccentrics and epicycles, is to say very well--there is no danger in that, and it is sufficient for the mathematician: but to wish to affirm that in reality the sun stands still in the center of the world, and that the earth is located in the third heaven and revolves with great velocity about the sun, is a thing in which there is much danger...(Job Kozhamthadam, 1994, p. 114)
This argument presaged the later debate between Max Planck and Ernst Mach, the former holding that theories did correspond to an underlying reality and the latter that they were merely useful human constructs, valuable for mathematical calculations and as a way of summarizing results (Matthews, 1994).
To put this issue in simpler terms, BACON does not know what it has discovered. It is BACON's creators who comprehend the significance of the discovery. So who is the real discoverer, human or machine? The answer is both are part of a system, or a network, to use the term preferred by sociologists (Law, 1987). Indeed, more sophisticated versions of their BACON system could serve as expert assistants to scientists searching for relationships among data. This is exactly the role played by sophisticated statistical packages like SPSS and SAS: they allow social scientists to explore data. But to make certain that relationships discovered are not chance alignments of numbers, some theory or model is necessary--even an imperfect one.
1. Discovery depends on finding a problem significant enough to be labeled an important achievement.
According to Keith Noll, a planetary scientist at the Space Teles cope Science Institute, "One of the hardest things about being a scientist is selecting a problem that's small enough for you to actually attack and pursue as a project yet big enough to add something significant to what's already known" (Sobel, 1996, p. 87). In Noll's case, he settled on the study of the four moons of Jupiter that were discovered in 1610 by Galileo. Since then, spacecraft and the Hubble have found many more moons. Noll brought a new instrument to their study--the Faint Object Spectrograph on the Hubble telescope; he among other things, he has found evidence of an oxygen atmosphere around Ganymede, one of the four.
Similarly, the astronomer Margarte Geller spent a year at Cambridge thinking about the problem of the universe's structure. Galaxies were thought to be distributed at random. The first survey, encompassing only a few hundred galaxies, had found a great empty area in the constellation Bootes, but even Geller thought that was probably an error. Geller decided there needed to be a survey that would reach deeper into the universe, searching for large patterns like the apparent void in Bootes. It was she who discovered the structure often referred to as 'the stick man': "The distribution of galaxies looked like a child's drawing of a somewhat bowlegged person. It's a whimsical name for a grand figure: the stickman extended 500 million light years across the universe. Its torso was composed of hundreds of galaxies, a massive congregation known to astronomers as the Como cluster. Its arms were two more sheets of galaxies streaming across the night sky" (Taubes, 1997, p. 54).
Like Kepler, Geller now had data that suggested one of the fundamental assumptions or dogmas about the structure of the universe was wrong. Unlike Kepler, she had generated the data herself. The solution to her riddle is still a work in progress; she is one of the astronomers leading projects that will map even more of the universe, in an effort to find a Keplerian pattern in the structure of galaxies.
In all three cases, Kepler's, Geller's and Noll's, improved instrumentation produced new data that led to discoveries. All three found a problem they could attack, given their background and equipment, and that would also make a real contribution to science. In Kepler's case the contribution was revolutionary. Thomas Kuhn has proposed that science evolves by going through periods of revolution, or crisis, in which the reigning paradigm or world-view goes through a dramatic shift (For more on Kuhn's view, see 2.1 below and Kuhn, 1962). Consider Kepler's discoveries. The reigning paradigm, or world view, was that planetary orbits were circular--even the Copernican solar system included them. Tycho's data constituted what Kuhn has called an anomaly--a result that does not coincide with the current paradigm. According to Kuhn, anomalies cause the period of crisis that leads to a revolution. Kepler was the only one who saw this anomaly; it certainly precipitated a crisis in his thinking! His three laws became part of a new paradigm; Newton used Kepler's laws in the creation of his theory of gravity (Kuhn, 1957).
2. Discovery depends on transforming that problem into a form that suggests a promising path to solution.
A key aspect of this is formulating or having a powerful mental model, one that sets up a creative tension between the ideal--what the discoverer expects or hopes will happen--and the real. Kepler began with his geometric solids; the failure of that model created a tension, a need to replace it with some other geometric order.
It would be premature to argue at this point that mental modeling is an essential part of this process of transformation. In physics, for example, some scientists seem to rely on it , while others have almost a horror of visualization, preferring purely mathematical transformations (Miller, 1989).
3. Discovery depends on finding good data.
Again, a powerful mental model can play an important role here, suggesting what data is relevant. But one also needs resources and connections to get at the data. Kepler had to maneuver to get his appointment to Brahe's observatory. Modern astronomers still have to compete for access to observatories, though the internet is making access to good astronomical data much less problematic.
4. Discovery depends on a combination of flexibility and stubbornness
In other words, a willingness to discard a hypothesis on the basis of negative evidence, while keeping what the philosopher Imre Lakatos (Lakatos, 1978) called the 'hard core' of a research program. No amount of negative evidence would have persuaded Kepler to shift the sun from the center of the solar system.
These generalizations, vague as they are, do suggest that discovery is not totally mysterious. Nor is it easily reduced to a set of algorithms, BACON notwithstanding. Unfortunately, at this point, we can offer only the most general advice on how to discover. Furthermore, our advice would be too dependent on a single scientist working on a particular kind of problem. To improve these generalizations and broaden the sample on which they are based, we will apply them to:
(1) Further examples of discovery: The rest of this chapter will include two cases of discovery that differ from Kepler's in important respects. The great Devonian controversy will provide us with an example of a discovery that emerged out of the interactions among competing research teams of geologists. Michael Faraday had to build the apparatus that generated his data; he could not collect his numbers from another source. In order to discover, Faraday had to invent.
(2) Invention: We will also explore whether generalizations about discovery can be applied to invention. Once again, we will begin with a case--the invention of the telephone. Alexander Graham Bell had to discover in order to invent. Since I have spent much of the last five years studying Bell and his competitors, this section will set up one of the cases we will come back to again and again.
(3) Recent research on the cognitive psychology of science and technology: Even the three cases cited above are an inadequate base upon which to make generalizations, particularly as all three are historical. Fortunately, the literature on cognitive psychology of science includes modern practitioners and students. It will also allow us to refine our tentative generalizations in the light of the latest research. Chapter 2 will focus on psychology of science, and Chapter 3 on invention .
All this talk about how discovery works does not, of course, answer the question of why. This book will only touch on what motivates discoverers and inventors. Certainly, fame and fortune are an important part of the puzzle. But Kepler gives us a hint of another motive:
Sagan in Silesia, in my own printing press, November 6, 1629: When the storm rages, and the state is threatened by shipwreck, we can do nothing more noble than to sink the anchor of our peaceful studies into the ground of eternity" (Kepler quoted in Koestler, 1963, p. 422)
Kepler lived during the time of the thirty years war. In 1611, his imperial patron Rudolph had to abdicate the throne of Bohemia; his favorite son died, followed shortly by his wife:
Numbed by the horrors committed by the soldiers, and the bloody fighting in the town; consumed by despair of the future and by an unquenchable longing for her lost darling...in melancholy despondency, the saddest of all states of mind, she gave up the ghost (Kepler, 1963, p. 381)
Kepler had just finished his Dioptrice, his major work on optics, so at this point he was experiencing the contrast between the eternal order he was discovering and the chaos of human affairs. Kepler was not a man who withdrew from the world; he did try to reconcile Calvinists with Catholics, but usually ended-up offending both.
So, one of the motives behind Kepler's discoveries was a desire to glimpse the eternal. Like the Arthurian knights, Kepler was on a quest for a Grail. Glimpsing the Grail did not guarantee temporal success--it was a spiritual goal, to be achieved by one who had risen above all ordinary desires. Einstein asked why some have chosen to enter the Temple of Science. The answer is not easy to give, and can certainly not apply uniformly. To begin with, I believe with Schopenhauer that one of the strangest motives that lead persons to art and science is flight from the everyday life, with its painful harshness and wretched dreariness, and from the fetters of one's own shifting desires. One who is more finely tempered is driven to escape from personal existence and to the world of objective observing and understanding. This motive can be compared with the longing that irresistibly pulls the town dweller away from his noisy, cramped quarters and toward the silent high mountains, where the eye ranges freely through the still, pure air and traces the calm contours that seem to be made for eternity.
With this negative image, there goes a positive one. Man seeks to form for himself, in whatever manner is suitable for him, a simplified and lucid image of the world, and so to overcome the world of experience by striving to replace it to some extent by this image. This is what the painter does, and the poet, the speculative philosopher, the natural scientist, each in his own way. Into this image and its formation, he places the center of gravity of his emotional life, in order to attain the peace and serenity that he cannot find within the narrow confines of swirling, personal experience (Holton, 1978, pp. 231-2).
For Einstein , the Grail is 'a simplified and lucid image of the world'. Scientists often portray themselves as disinterested pursuers of truth for its own sake. Kepler was drawn to Einstein's 'silent mountains'--but he was also motivated by a desire to surpass Brahe and Copernicus. Recognition is the coin of science (Barnes, 1985) and part of this glory is attained by passing one's peers. Scientists know discovery is the road to recognition, and inventors hope their new technologies will lead to fortune--witness the bitter battles over priority and patent rights.
Kepler's accounts of his discoveries were usually in the form of a narrative, following the twists and turns of his thought processes, pausing for a burst of rapture when he thought he had made a discovery. This form of writing made it very difficult for Newton and others to find the three laws of planetary motion in Kepler's work.
In contrast, Newton transformed a narrative account of his experiments on optics into a more logical, inductive account in order to publish it in the Transactions of the Royal Society in 1672. In 1666, he organized fifty experiments with a prism in a kind of exploratory format, with one experiment suggesting another. Newton's first draft of an article on this topic, submitted to the Transactions , rigorously followed BACON's maxim: "What the sciences stand in need of is a form of induction which shall analyze experience and take it to pieces, and by a due process of exclusion and rejection lead to an inevitable conclusion" (Newton quoted in Bazerman, 1988, p. 91). Newton wrote his article as if he had followed this method while he was conducting his experiments, carefully articulating, testing and rejecting hypotheses until he arrived at the only possible explanation.
In fact, had he written a Keplerian narrative of the research, the order in which the experiments were conducted and the reasons for moving from one to another would have been different. The inductive format allowed Newton to organize the experiments into a logical chain visible only in hindsight. Bazerman is careful to point out that this reorganization might not be a deliberate strategy; Newton's memory of experiments done six years earlier may have been gradually transformed to correspond with how, in hindsight, he felt the research ought to have been done, a common cognitive phenomenon (Neisser, 1982). But it is likely that the act of writing at least catalyzed this transformation.
Newton's article ended with an invention: the reflecting telescope, which he claimed to derive from his discovery that different colors were refracted differentially when they passed from one medium to another. Actually, such a derivation was unnecessary, since Cassegrain independently made the same invention. Furthermore, at least part of Newton's derivation was in error, though his invention was sound. Here we see the beginning of one of the classic myths: the best inventions are derived from scientific discoveries.
Bazerman goes on to describe the letters Newton wrote, strengthening his argument in response to criticisms. This led to a new style in the first book of his Opticks, which Bazerman calls a 'juggernaut of persuasion'. Newton's experiments now play a supporting role in an axiomatic framework. The audience's questions and doubts are anticipated and dealt with, so that no alternate interpretation seems possible. As Bazerman (Bazerman, 1988, p. 124) says, "in Book I of the Opticks, Newton powerfully grabs hold of our reason and experiences until we have seen exactly what he wants us to have seen, in both the concrete and cognitive senses of the word."
Although Bazerman is more concerned with the persuasive elements of Newton's discourse, it is clear that these revisions led Newton to a more coherent, theoretical understanding of his own discovery. Writing can also spark discovery. One of the best examples comes from Larry Holmes' work on Antoine Lavoisier and Hans Krebs. Holmes argued that "it is from finely detailed case studies of the investigations of highly creative scientists that we are most likely to reach eventually a clearer understanding of the general nature of creative imagination in science" (Holmes, 1985, xvii). He conducted a detailed study of the Antoine Lavoisier's work in (what we would now call) organic chemistry over a twenty-years period. One of the major insights to emerge from this work is that the act of writing is itself part of the discovery process.
The extent to which Lavoisier developed his thought while writing his memoirs suggests a function for scientific papers that is not often emphasized. Scientific papers are characterized in many different ways: as reports of completed research, as announcements of discoveries, as vehicles for knowledge claims, as the end products of a process of "inscription," as the prime manifestation of the "context of justification," and as the necessary prerequisite for recognition as a practicing scientist. It has become commonplace to point out that as historical accounts of the discoveries they report, published scientific papers are misleading. For the actual pathway of thought and experiment they substitute the best combination of argument and evidence that the author can muster to justify the conclusions he has already reached. When, however, we have been able through laboratory records to approximate more closely the real historical course, we can perceive the relation between that course and its representation in the published paper in a more positive light. Although a scientific paper is everything that is implied in the above labels, it is, or at least for Lavoisier it was, far more. He was not merely contriving idealized or distorted versions of investigations, of which true versions already existed. He was transforming open-ended clusters of ideas and operations into organized, bounded investigative units. Not until he had chosen what to include and to exclude, clarified, linked together the parts, and rationalized what he had done did a coherent, completed investigation exist. Sometimes, as we have seen, he very nearly created an investigation on paper by bringing together experiments that had formerly been part of other investigations. Producing his scientific papers was, in short, not a matter of reporting accurately or inaccurately on something he had previously done, but an integral part of the creative process (Holmes, 1985, p. 488).
For example, Holmes traced changes in Lavoisier's thinking across several drafts of a manuscript he eventually presented to the Academy of Sciences in May of 1777. In the early drafts, he hypothesized that the portion of the air absorbed in respiration (what we now call Oxygen) gives a red color to the blood, just as this same portion of air gave a red color to metals with which it combined (producing what we now call rust). Laviosier wrote happily, "I believe that the theory of respiration has now been established" (Lavoisier quoted in Holmes, 1987, p. 223).
By the next draft, he was already tempering this conclusion and in subsequent drafts he scribbled and worked over an alternative hypothesis: that this new kind of air (which he called dephlogisticated air and we now call Oxygen) was converted to fixed air in the lungs. It was this hypothesis that became one of his most important discoveries. Holmes is careful to note that "We cannot always tell whether a thought that led him to modify a passage, recast an argument, or develop an alternative interpretation occurred while he was still engaged in writing what he subsequently altered, or immediately afterward, or after some interval during which he occupied himself with something else; but the timing is, I believe, less significant than the fact that the new developments were consequences of the effort to express ideas and marshal supporting information on paper" (Holmes, 1987, p. 225).
Holmes also conducted a detailed study of Hans Krebs' discovery of how urea is synthesized from ammonia and carbon dioxide, a closed circle of reactions referred to as the ornithine cycle. When Krebs began the experiments that led to this discovery, he was not proceeding according to the hypothetico-deductive method. After finishing medical training in 1925, he worked as a research assistant for the distinguished biochemist Otto Warburg, who "had developed methods for measuring, with sensitive manometers, the rates of respiration of thin slices of tissue places in a fluid medium" (Holmes, 1989, p. 60). In 1931, Krebs began his own research program and looked for problems he could solve with his new tools. Within nine months, he had discovered the ornithine cycle, a process that has been emulated by a computer program called KEKADA (Kulkarni, 1988). While BACON focused on discovery processes occur after data has already been gathered, KEKADA attempted to simulate the process by which Krebs generated new data. The program could not actually conduct an experiment, but it could propose one, and the experimenter could provide the result.
KEKADA was programmed with a wide range of heuristics. Some of the heuristics were ones Krebs himself mentioned, including "a standard biochemical strategy: if a given compound exerts some particular action, check whether derivatives of that compound have similar actions" (Kulkarni, 1988, p. 146). Most were inferred from Holmes' detailed accounts of his processes. Kulkarni & Simon arranged these heuristics in a hierarchy, from those that were general and could be used across a wide variety of problem domains and those that were restricted to biochemistry. They also classified them into nine types, including 'problem choosers', 'experiment-proposers', expectation-setters' and 'hypothesis-modifiers'. The two classifications of heuristic were potentially independent, but in fact, the problem choosers identified by Kulkarni and Simon were all general and the hypothesis-modifiers were mostly domain-specific.
The 'standard biochemical strategy' noted by Krebs was classified as domain-specific, and a modified version of it was included in a hypothesis-generating heuristic:
If a surprising outcome occurs involving A as one of the reactants, then hypothesize that there is a class of substances containing A (or its derivatives) that will produce the same outcome (Kulkarni, 1988, p. 156).
An example of a general or weak heuristic from the problem generator category is:
If the outcome of an experiment violates expectations for it, then make the study of this puzzling phenomenon a task and add it to the agenda (Kulkarni, 1988, p. 153).
This problem generator can trigger the hypothesis generator noted above. KEKADA was also equipped with background knowledge about a variety of substances and their expected reactions. On each cycle, the conditions of each of KEKADA's heuristics were matched against working memory. When a heuristic was selected and ran, it altered the contents of working memory, and another cycle began. Kulkarni & Simon also distinguished between those heuristics that determined the next hypothesis and those that determined the next experiment. Both of the heuristics noted as examples above searched the hypothesis space. These experiment proposers include a variety of specific heuristics to follow up on the class of substances containing A, depending on KEKADA's specific hypotheses about how the reaction works. For example, if A and B react to form C , then the experiment proposer suggests experiments on A and B separately and in combination. The results of these experiments would be supplied by the programmer.
One of the most interesting features of KEKADA is its capacity to follow-up on surprises generated by violations of the expectations it started with. The initial experiment with Ornithine produced a surprising amount of urea; Krebs dropped everything else to pursue this surprise. If BACON had been equipped with this capability, it might have been possible to have it start with circular orbits, then propose additional observations when its expectations were violated.
KEKADA clearly models more aspects of discovery than BACON, and illustrates the potential for heuristic-based analyses of scientific discovery. However, the program does not simulate two key aspects of Krebs' discovery: his acquisition and use of a tissue-slicing technique that became his 'secret weapon' (Kulkarni, 1988) and the role of writing. While discussing his 1932 paper reporting the discovery of the ornithine cycle, Krebs remarked that,
I spent a lot of time on writing, but usually while the work was still going on. And I find in general only when I try to write it up, then do I find the gaps. I cannot complete a piece of work and then sit down and write the paper (Holmes, 1987, p. 226).
Let us see how our four generalizations about discovery fare after this brief consideration of the cases of Lavoisier and Krebs.
1. Discovery depends on finding problem significant enough to be labeled an important achievement.
Lavoisier and Krebs both began with problems that were considered significant by major practitioners in their fields.
2. Discovery depends on transforming that problem into a form that suggests a promising path to solution.
Lavoisier had his own unique way of framing the problem in terms of "conceptual structures that were novel, deep and persistent, in the context of the state of the fields he entered" (Holmes, 1989, p. 63). Krebs was less conceptual and more empirically opportunistic--he followed surprising results. In the course of explaining them, he did have to formulate and test novel hypotheses. But the Krebs case suggests that a scientist who possesses good methodological techniques and problem-solving heuristics may be able to create opportunities for data-driven problem transformations.
Interestingly, both Lavoisier and Krebs at points held contradictory views of an important problem. At one stage, Lavoisier entertained both the idea that respiration worked (a) by absorbing one of two parts of air or (b) by removing 'fire matter' (heat) from the air. When exploring this new ornithine effect, Krebs had to grapple with the fact that ornithine seemed to be both catalyst and product of the reaction. Similarly, Kepler seemed to maintain for a time both the view that orbits had to be perfect circles and that they could not be circular. Holmes argues that, "in moving from an existing conceptual framework to a new one, scientists often cannot make a single leap from one coherent mental framework to another. They may have to endure, for extended periods of time, deep fissures within their mental worlds" (Holmes, 1989, p. 53).
3. Discovery depends on finding good data.
Because Laviosier and Krebs were both experimenters, they had to manufacture or invent the data they used. Lavoisier had to choose his experiments more carefully than Krebs, and showed a greater tendency to dismiss anomalous results as errors. Much of this difference may be accounted for simply by the fact that Krebs worked in an age of bigger science, where laboratories had more sophisticated equipment and there was a greater opportunity to carry out multiple experiments. Therefore, Krebs was able to create new data more rapidly than Lavoisier, and may also have felt more secure about eliminating sources of error (Holmes, 1989).
This generalization ought to be modified, then:
3. Discovery depends on finding or inventing good data.
Invention as used here does not mean creating fake data; rather, it reminds us that experimental scientists have to manipulate nature, and that manipulation depends on technologies and techniques that need to be invented.
4. Discovery depends on a combination of flexibility and stubbornness.
Lavoisier modified his theories based on experimental data, but "Lavoisier did not give in easily when his results appeared not to fit his expectations. He regularly guessed at possible sources of error and made whatever corrections he thought reasonable to bring the results more closely in line with his theoretical needs" (Holmes, 1989, p. 58).
Krebs displayed great flexibility in following surprising results. It is less clear where stubbornness plays a role in his work. Perhaps his case suggests a modification of our generalization:
4. Discovery depends on a combination of flexibility and stubbornness, depending both on the individual scientist's cognitive style and on the nature of the problem.
Style and problem interact, here, because scientists often choose problems that suit their styles. As a result of Holmes' work on both Lavoisier and Krebs, we will have to add a fifth generalization:
5. The act of writing is part of the discovery process.
For Lavoisier and Krebs, writing was critical to formulating their discoveries. Even Kepler's narratives doubtless helped him clarify his thinking.
James Gleick, in his biography of Richard Feynman, reports an exchange between a historian, Charles Weiner, and Feynman concerning Feynman's scientific notes. Feynman claimed that he "actually did the work on the paper." Weiner countered that the work must have been done in his head, with the record appearing on the paper. Feynman responded, "No, it's not a record, not really. It'sworking. You have to work on paper..." (Gleick, 1992, p. 409).
We don't know to what extent re-shaping his arguments for publication affected Feynman's understanding of his discoveries. Gleick notes that "he wrote in astonishing volume as he worked--long trains of thought, almost suitable to serve immediately as lecture notes." Furthermore, these lecture notes were often published. It would be interesting to know more about Feynman's process of revision as he turned notes into lectures.
At any rate, the Feynman example provides further support for the idea that writing plays a central role in discovery. As with the previous generalization about stubbornness, individual scientists differ in their writing style--for some, major conceptual changes can be seen in the notes, others in draft manuscripts, still others in both.
Like Kepler's discovery of the planetary laws, Michael Faraday's discovery of electromagnetic fields played a key role in a scientific revolution. Oddly enough, it was a revolution that countered an important feature of the Newtonian synthesis. Gravity was a force that acted in a straight line and was transmitted instantaneously over the space between bodies; this phenomenon was referred to as 'action at a distance'. Kepler would have been horrified by the idea; he thought in terms of a real force emanating from the sun, contacting the planets like light and sweeping them around their orbits.
Newton's gravity became one model for how forces might operate in other domains. By the late eighteenth century, it was clear that the attraction and repulsion of electrical charges followed an inverse square law. Perhaps electricity was another instance of action at a distance.
This viewpoint had its critics, among them Michael Faraday, who rejected both the primacy of matter and the notion that electricity operated 'at a distance'. The examples of Faraday's problem-solving processes described in this section are distilled from detailed, fine-grained cognitive studies by Tweney (Tweney, 1989a) and Gooding (Gooding, 1990a). "For him [Faraday], fields of force were the primary reality, and 'matter' a secondary or derived phenomenon. To understand his creative life, then, we must acknowledge his position as a revolutionary, as someone who demonstrates the practicality of a world view completely different from the prevailing one, and who does this, not by metaphysical argument, but by a series of compelling experimental demonstrations of such conceptual force that they could not be ignored" (Tweney, 1989a, pp. 94-5).
In 1816, Faraday saw electricity, magnetism and gravity as properties of matter; they accounted for cohesion and affinity, were responsible for attraction and repulsion and the same forces accounted for both chemical and physical phenomena (Tweney, 1985). Faraday's evolving mental model contained within it the possibility that the three forces could be unified (Nersessian, 1984).
Faraday was not an armchair speculator, however. His motto was, "il faut savoir de MANIPULER' (Tweney, 1985, p. 196). In 1820, Hans Christian Oersted showed that when a current passes through a wire, it acts as if it were a magnet. Furthermore, the force was directed transversely, at right angles to the wire--a major difference from gravitational force, which was directed radially. To understand what Oersted had discovered, Faraday repeated his experiments, varying conditions to explore the phenomenon. In the course of this research, he discovered that current through a wire could make a magnetic needle circle around it. In order confirm and demonstrate this discovery, Faraday invented the first electromagnetic motor.
David Gooding has reproduced this process in exquisite detail, replicating many of Faraday's experimental manipulations. Gooding believes that Faraday progressed via "a convergence of successive material arrangements (the apparatus) and successive construals (or tentative models) of the manipulation of the apparatus, and its outcomes" (Gooding, 1990b, p. 187). A construal corresponds roughly to what I am calling a mental model. Gooding's point is that, for Faraday, ideas, physical manipulations and objects are closely linked.
To find out how this linkage occurs, let us look more closely at what Faraday did. On September 3, 1821, Faraday began by exploring how magnetized needles behaved in the presence of strong currents. Humphry Davy, Faraday's mentor, and others predicted that a wire could be made to revolve or 'rotate'. To explore this possibility, Faraday built a new apparatus, consisting of a wire put through a cork which floated in water. The wire made contact with globules of Mercury at both ends; hence, he now had a wire that could rotate. He observed that the magnets thrust the wire form side to side: lateral motion, instead of rotation (Gooding, 1990a, p. 128). Then he bent the wire and discovered that repeated applications of the poles of the magnets produced a circular motion, if he looked down from above on the bent wire.
This account sounds simple and straightforward, as discoveries always do, after the fact. Gooding has shown how difficult it is to reproduce Faraday's result and how dependent it was on his construals (Gooding, 1990a).
At the end of the day, Faraday proposed building a new apparatus in which a magnet would be stuck upright in wax in a cup of mercury and a piece of wire allowed to circle around it when a current was applied. Faraday eventually produced a model of this experiment that could be shipped to other scientists so that they could replicate Faraday's results, given careful instructions on what to do.
Figure 2: Faraday's demonstration apparatus, which he sent to other scientists. All one had to do was add mercury and hook up a battery, and the wire would rotate. Reprinted with Permission of the Indiana University Press from Gorman (1992) Simulating Science , Fig 7-1, p. 143.
In effect, Faraday had created what W. Bernard Carlson and I call a 'mechanical representation'. We created this term because we noted that inventors seemed to have sets of familiar moves or operations that were embodied in specific components. For example, Edison took a drum cylinder from his phonograph and used it to rotate the film on the first motion picture camera (Carlson, 1990). According to Jenkins (Jenkins, 1984, p. 153), "Any creative technologists possesses a mental set of stock solutions from which he draws in addressing problems." This drum cylinder was part of Edison's repertoire of stock solutions: when faced with a new problem, he drew on them.
These familiar mechanical moves are representations because they can be run in the imagination as well as on the bench top. Not only can we manipulate the physical world, we can form mental representations based on our manipulations and run these representations in our imaginations. As Gooding says, "These mechanical representations can be retained in memory; moreover, they are so well understood that their use will be consistent and the implications of their properties for other components of a device can readily be worked out" (Gooding, 1990b).
For Faraday, the motor shown in Figure 2 served as a mechanical representation, even though his goal was understanding the phenomenon discovered by Oersted rather than inventing a new technological system. Any theoretical account of induction would have to incorporate the behavior of this device. Faraday shipped it to others to in order to persuade them to incorporate his mechanical representation into their thinking.
Latour (Latour, 1987) discusses the role of a strategy called 'black boxing' in the development of technoscience (he uses this term to refer to the fact that the boundary between science and technology is fuzzy at best). Once a device or an experiment or a finding is black-boxed, it is treated as an unquestionable fact: no one needs to look inside that particular black box again. Gooding does not discuss whether Faraday's demonstration motor became a black box for others, but mechanical representations can evolve into shared certainties, used by multiple inventors and scientists to embody knowledge and procedures.
In my analysis of Kepler's discovery processes, I remarked on the delicate balance between stubborn adherence to a hypothesis and willingness to abandon or alter it in the face of negative evidence. In an 1818 lecture, Faraday argued that 'mental inertia', by which he meant stubborn adherence to one's ideas, was both a blessing and a curse. A certain amount of such inertia saves one from discarding promising ideas prematurely, but an excess prevents one from recognizing when an idea or approach no longer works.
On August 29, 1831, Faraday found that a transient current was generated in one coil of wire wound around an iron ring when a battery was connected to, or disconnected from, a second coil wound around the same ring. This experiment did not appear 'out of the blue'. Faraday was engaged in a variety of experiments directed at transient effects. Faraday's electromagnetic experiments were part of a larger 'network of enterprises', a term coined by Howard Gruber (Gruber, 1981) to explain the way in which Darwin's diverse research interests connected, and also the motivations for his work. Darwin's work on topics like barnacles and pigeon breeding facilitated the development of his theory of evolution. Similarly, Faraday's efforts to take a variety of transient effects and make them visible were all part of his network of enterprises.
Faraday's first attempts to find electromagnetic induction can be seen in his notebook as early as 1822 where he outlined an experiment surprisingly similar to ones he would conduct in 1831. Why the delay? The answer, according to Tweney (Tweney, 1989b), is that in 1822 Faraday did not realize the magnetic induction effect could be transient. Whereas by 1831, he had developed heuristics for making transient effects visible. He had also read recently about new ways of obtaining powerful effects using large horseshoe-shaped electromagnets (Tweney, 1985). So on August 29th, 1831, when Faraday connected a coil to a battery and observed a brief deflection of the needle, this was more than a chance or 'serendipitous' discovery. He was returning to an old idea with a new mental model that highlighted the importance of transient effects and new heuristics for producing them.
In his 1831 experiments, Faraday followed the same pattern as in his 1821 experiments that led to the motor kit: he began with construals and exploratory experiments, then moved to hypotheses and demonstrations. He showed the same combination of stubbornness and flexibility that characterized Kepler. From August 29 to October 28, he attempted to use both electromagnets and permanent magnets to induce a current. Overall, he obtained positive results only 40% of the time. The bulk of the negative results came with the permanent magnet. At this point, he exhibited an appropriate mental inertia--he did not discard his hypothesis concerning magnetic induction in the face of a few negative results. Like any good experimenter, Faraday was aware of the possibility of noise or error in results, especially given that he was trying to obtain a transient effect.
On October 28, he switched to a more powerful electromagnet at a colleague's house and the proportion of positive results rose to 80%. Now he was beyond the exploratory phase and on to reliable demonstrations. Faraday gradually evolved a sophisticated mental model of the lines of force that were generated by a magnetic or an electrical current; these ideas culminated in his concept of fields of force, which were given mathematical expression by Maxwell (Nersessian, 1984).
With this brief coverage of Faraday, let us turn to the generalizations we have carried over from past cases.
1. Discovery depends on finding a problem significant enough to be labeled an important achievement.
Faraday certainly selected one of the most important 'cutting-edge' problems of his time: how magnetism could be used to induce electricity.
2. Discovery depends on transforming that problem into a form that suggests a promising path to solution.
James Clerk Maxwell referred to Faraday as a "mathematician of a very high order" (Gooding, 1994, p. 4), even though Faraday rarely used equations. But Faraday did use what he called a 'rough geometrical method', a kind of mental modeling. We saw an example of this above in his work on electromagnetic rotations that led to a prototype motor. The same kind of careful, rigorous mental modeling led gradually to his mature idea of fields, or lines of force. Gooding describes Faraday's method as follows:
(i) represent particular behaviours of magnets, illuminated lines of induction, diamagnets, crystals and light rays in terms of patterns; (ii) use changes in pattern or arrangement to guide the development of structural models of the interactions of forces; (iii) try these by running them in the imagination or by simulated and real experiments; (iv) explore limiting cases by real- and thought-experimentation that invokes practical knowledge of the geometry and topology of lines of force (Gooding, 1994, p. 22).
As Maxwell noted, Faraday provided "a method of building up an exact mental image of the thing we are reasoning about" (Gooding, 1994, p. 21). Kepler provided us with an example of a scientist who translated the results of his own mental modeling into equations. In Faraday's case, the equations were developed by James Clerk Maxwell, whose mathematical discovery played a critical role in the development of Einstein's theory of special relativity. An account of the interplay of visualization and formal mathematics in these discoveries lies beyond the scope of this book (Nersessian, 1984). It will suffice to say that Faraday 's lines of force did play an important role in one of Kuhn's great scientific revolutions: the shift from a Newtonian to an Einsteinian world view.
3. Discovery depends on finding or inventing good data.
Faraday's invention of the first electromagnetic motor suggests the way in which he created mechanical representations in order to discover.
4. Discovery depends on a combination of flexibility and stubbornness, depending both on the individual scientist's cognitive style and on how she or he represents the problem.
Faraday's lecture on mental inertia suggests the way in which he reflected on the problem of flexibility and stubbornness. Late in his career, Faraday began another investigation that indicates the way in which he was careful to maintain just the right balance. He still adhered to the idea that the three main forces were all manifestations of a single, underlying force. He had demonstrated the intimate relationship between electricity and magnetism. Now he sought to demonstrate gravitational induction. To accomplish this, he dropped electrical coils down through cylindrical 'shot towers' to see if movement through an electrical field would induce an electric current in the coil. Initially, results confirmed his expectations--a current was produced. But true to his own advice, Faraday looked carefully for evidence that could disconfirm his explanation. The shot towers, it turned out, contained small amounts of magnetic material; therefore, the effect was simply another example of magnetic induction. But Faraday never abandoned his gravitational hypothesis, because he also knew the effect he was looking for could be very weak--perhaps he needed a far longer tower with much more gravitational mass.
5. The act of writing is part of the discovery process.
Lavoisier and Krebs revised and re-organized ideas that became discoveries in the course of writing them up for publication. Faraday's similar space of re-organization and revision seems to have been his notebooks: "he left us records of about 30,000 experiments, both successful and unsuccessful, as well as a large number of speculative idea books, bibliographies, indexes, scrap-books, etc., etc." (Tweney, 1991, p. 301). Faraday's notebook served as:
1) An external memory aid. Here the goal was to faithfully record results and ideas in a form that facilitated retrieval. Faraday experimented with a number of such schemes. He began with a static alphabetical index, but it was hard to add appropriate categories as the material grows, so he adopted a scheme of John Locke's, in which each entry is indexed by its first letter and first vowel. He also experimented with numbering schemes. Faraday spent a great deal of time organizing his external memory.
2) A space for speculation and exploration. Faraday also kept idea books, that were not dated and were full of blank spaces, for use in recording additional ideas on the same theme. Sometimes entries were crossed out. Faraday also used loose slips that contained a brief description followed by numbers corresponding to a diary entry. Tweney speculated that Faraday was using these to create an equivalent of a modern database.
Is Faraday a hero, in the Campbellian sense? He was certainly treated as a hero by his contemporaries; as the Duke of Somerset wrote to Charles Babbage in 1835, "the story of Faraday is just one that is sure to make a great noise. There is something romantic and quite affecting in such a conjunction of poverty and passion for science...he comes out as the Hero of chemistry" (Schaffer, 1994, p. 41).
Like Kepler, Faraday had a religious faith that the universe was orderly and comprehensible. Faraday belonged to a group of Christians who referred to themselves as Sandemanians. But whereas Kepler believed in a mathematical harmony, Faraday believed the 'book of nature' was comprehensible to anyone who had the patience to read it slowly and carefully--higher mathematics were unnecessary:
Since the Sandemanians accept that the Bible is written in a plain style we would expect them to attribute similar characteristics to nature. Indeed, Faraday assumed that nature possesses an inner coherence and simplicity. For example, he accepted that nature was governed by a set of God-given causal laws. These laws were not merely the result of God speaking his will at the creation, they were also the work of a wise Creator who, avoiding unnecessary complexity, constructed the world on simple, plain principles. Faraday's belief in the indestructibility of force--all phenomenal forces being manifestations of a more basic conserved force--can likewise be interpreted as an instance of this more general principle of simplicity (Cantor, 1985, p. 73).
Faraday's struggle to read this book therefore does not seem like a struggle, only the result of patient, careful experimentation. Genius is supposed to come in sparks, leaps and insights--it is a product of imagination, not mere manipulation. But Faraday illustrates that scientific revolutions can come from intimate, experimental contact with Nature--genius is in the hands and their products as well as in propositions and equations.
One of the scientists in C. P. Snow"s novel The Masters (Snow, 1951) talks about how intoxicating it is to make Nature 'sit up and beg'. Faraday was such a scientist. However, in the case of a truly great experimenter, one might also argue that nature is making the scientist 'sit up and beg': the two are locked in an intimate dance. Faraday is a hero because he did not just read the book of nature--he wrote a part of it by slowly and carefully exploring the relationships between forces. This characteristic of Faraday's is captured by the computer program created to emulate his discovery processes.
Like Kepler and Krebs, Faraday has inspired computational research. In this case, instead of writing a program that emulates Kepler, (Gooding & Addis, 1990, Gooding & Addis, 1993) created a new computer tool called CLARITY which allows users to create diagrams that represent programs in a functional database called FAITH. CLARITY converts these diagrams into FAITH programs.
Instead of relying on computer scientists to model cases of discovery, CLARITY makes programming tools available to scholars like Gooding, who are studying science. As Gooding and Addis note, "CLARITY diagrams make hypotheses about inference and learning processes accessible; they can be discussed and criticized more readily than computer code and are therefore open to revision and experimentation in ways that most code-based modeling is not" (Gooding & Addis, 1993, p. 8).
For example, Gooding can use Clarity to generate graphs of Faraday's cognitive processes like the simple one shown in Figure 3. In this simple graph, we see Faraday begin with a goal, to make the wire move continuously, then decide to build an apparauts with which he will try to make the wire move. Triangles are used to dentoe goals, circles to represent mental outcomes and squares to represent physcial ones., including observations.
Figure 3: A problem behavior graph depicting the beginning of the experiments that led to Faraday's electromagnetic motor. Adapted from (Gooding, 1990, p. 180).
This simplified diagram does not do justice to the complexity of Gooding's scheme, which allows him to characterize hierarchies of goals by the way he shades the arrows and show embodied cognition by superimposing circles and squares. Gooding was able to graph whole sequences of Faraday's experiments in this manner (Gooding, 1990).
CLARITY could allow other scholars to do the same, and also permit them to see the assumptions underlying the graph. One could even draw CLARITY diagrams while interviewing a scientist, and run them to see if the results corresponded to elements of the actual discovery process. Such graphs would facilitate for more rigorous comparison of the cognitive processes of different discoverers.
CLARITY can be viewed as a compromise between top-down, algorithmic models like BACON and KEKADA that specify processes in terms of rules and bottom-up approaches typified by connectionist systems that learn from examples (Waltz, 1988). The functional approach allows one to create top-down models of discovery processes, but also to build them from the bottom up, looking closely at the fine-grained activities of the scientist.
An intelligent reader might ask at this point, "Who cares about all these computational simulations?" The central problem of cognitive science is that it is impossible to directly observe the mind in action. Therefore, one approach is to build a model of the mind, run it, and see if, given the same inputs as a discoverer, it produces the same outputs. Indeed, most cognitive scientists have accepted that any theory of human mental functioning should be expressed as a computer program of some sort (see Gorman, 1992 for a counter-argument). The danger is that more time will be spend building discovery programs than studying discoverers and further, that the languages and concepts of those doing the studying will be very different from those doing the modeling. CLARITY shows promise of being a computer tool that will encourage collaboration between modelers and scholars who do not have a computational background. So far, CLARITY has been tested only on Faraday, who was already the object of extensive study. To prove its promise, CLARITY needs to be tried on other cases.
In particular, the program's creators recognize that they need to come up with a "multi-agent model of the interactions of individuals and groups of practitioners, particularly the dynamics of consensus-seeking and of controversy in science" (Gooding & Addis, 1993, p. 99). In other words, Gooding and Addis recognize that discovery is a social process. Hitherto, we have talked mostly about the mind of the individual discoverer. Before we turn to a closer look at the literature on the psychology of discovery, let us cover at least one case that clearly illustrates how discovery involves multiple 'agents'.
The MacArthur Foundation's 'genius' awards embody the classic Campbellian myth: the way to make great, positive changes in the world is to locate individual heroes, give them a million dollars, and let them be creative. In contrast, the Nobel Prizes are frequently awarded to more than one person; these awards seem based on the idea that discovery can be a collective effort.
For example, Watson and Crick shared the Nobel prize for the discovery of the double helix structure of DNA. But as even Watson's entertaining, irreverent account of their discovery showed, they relied heavily on the work of others who were close on their tails (Watson, 1968) and there were other good candidates for inclusion in the award (Portugal & Cohen, 1977).
Similarly, Banting and MacLeod were both awarded the Nobel Prize for the discovery of insulin--and each promptly selected another colleague to share the award. Furthermore, the major paper announcing the discovery actually had seven authors (Bliss, 1982).
The negotiations among scientists about who deserves credit are frequently acrimonious; each of the original recipients of the insulin award thought the other did not deserve it, and the battle continued long afterwards. To find out more about the nature of the negotiations that lead to and follow up on a discovery, we once again need a case that has been studied in sufficient detail.
This controversy concerns the discovery of what we now call the Devonian period in geological history. The name comes from Devon, in England, where the strata that came to typify the Devonian sequence were first identified. This discovery grew out of an often acrimonious set of negotiations among at least ten major participants (Rudwick, 1985). In the interests of simplification, we will stick to a few main characters and a sub-set of the full story.
Roderick Murchison was a gentleman who had taken up geology because it afforded him a respectable hobby that could be combined with the pleasure he took in hunting. His mentor was another gentleman geologist, Adam Sedgwick, a respected president of the prestigious Geological Society. Murchison succeeded him in that post.
One of the controversies in the geology of the 1830s concerned the relative importance of two methods for dating strata: fossils and rock types. Murchison, who did his fieldwork in the Yorkshire, became impressed with the heuristic value of using fossils to date strata.
In contrast, Henry De la Beche, secretary of the Geological Society under Murchison in 1831, tended to favor rocks over fossils. As of 1831, younger and more recent strata were relatively well understood, but below the Carboniferous group was a large, undifferentiated area known as the Greywacke, the upper part of which was an area of "Transition limestone". Between the two was an area known as the "Old Red Sandstone".
In 1831 Murchison had an Eureka insight when he found a place where the Transition passed conformably into the Old Red. Actually, the Eureka was a myth; Murchison and at least one other geologist had observed this phenomenon before. Successful discoverers are also good at myth-making.
By 1834, Murchison had developed a hypothesis: that the Old Red Sandstone was divided into three parts, the middle of which had fish, but no plants; below that, the Transition also had sea fossils, but most of the Greywacke below had none. This hypothesis had economic implications in the search for coal, which--if Murchison were right--had to exist above the Old Red.
What appeared obvious in one area of England might look entirely different in another. When De la Beche did a survey in Devonshire in 1834, he found evidence to accord with his presuppositions--that fossil plants existed throughout the Greywacke, and therefore coal could be found in Greywacke as well.
Murchison and De la Beche had been sparring in letters already, but now the controversy broke into the open at a meeting of the Geological Society in December of 1834. Essentially, Murchison focused on fossils--if De la Beche had found Carboniferous fossils, then he had Carboniferous strata. De la Beche, who had actually studied the rocks, felt they looked like Greywacke. Indeed, he wrote a letter to another geologist in which he depicted himself confronting Murchison and his colleagues and, pointing to his nose, announcing, "This, Gentlemen, is my Nose," to which they responded:
My dear fellow--your account of yourself generally may be very well, but as we have classed you, before we saw you, among men without noses, you cannot possibly have a nose (Rudwick, 1985, p. 104).
De la Beche initially won Sedgwick's support, in part on the grounds that Murchison had found no distinctive Greywacke fossils and therefore his case hung on the absence of fossils, rather than on the presence of a distinct variety. Murchison then back-tracked a bit, claiming there were distinct fossil plants in the Old Red, although they were too poorly preserved for clear identification.
In 1835, Murchison, working in his Welsh Borderland area, labeled his Transition strata Silurian and confirmed that they contained no plant fossils. He also found a place where De la Beche had mistakenly applied the label Greywacke to Carboniferous coal-bearing strata. This piece of evidence was crucial in converting De la Beche's chief backer, Sedgwick, into a supporter of Murchison's view. While Murchison was discovering the Silurian system, Sedgwick was discovering the even older Cambrian system. Murchison referred to these groups of strata as systems because he was convinced that they were general and could be found anywhere in the world where erosion, eruption or other local disruptions had not erased them.
In July of 1836, Murchison and Sedgwick 'invaded' De la Beche's home ground, North Devon. They had hoped to find evidence of a discontinuity from the Carboniferous coal-bearing strata to the older Greywacke, caused by the way the strata were folded and had eroded. Instead, they found support for De la Beche's claim that there was a gradual transition. Despite the puzzling lack of an obvious discontinuity, they hypothesized a great trough of Carboniferous coal measures in the center of North Devon, which made an abrupt, unconformable transition to Silurian on the north side and Cambrian on the south.
In August of 1836, they presented their findings at a meeting of the British Association in Bristol. By the time of the meeting, Murchison had added a fourth band, or system, of strata, which he labeled 'Devonian'; on his map, these Devonian strata appeared between the Silurian and Cambrian systems north of the great Carboniferous trough in Devon. Sedgwick re-labeled these strata 'Upper Cambrian'. At this point, Murchison and Sedgwick obviously felt there was something different about this transition from Silurian to Cambrian, but they weren't sure what. Figure 4 compares De la Beche's hypothesis to Sedgwick and Murchison's.
Figure 4: Competing hypotheses about the structure of the same geological strata. A corresponds to De la Beche's view, B to Sedgwick and Murchison's. Reprinted with the permission of the University of Chicago Press from (Rudwick, Fig. 7.6, p. 164).
De la Beche was given an opportunity to respond at the meeting. "I was taken most deucedly in the flank, my ammunition being in my magazines, and my guns dismantled, expecting nothing but peace, I made my retreat in the best manner I could" (Rudwick, 1985, p. 166). He conceded the plausibility of the Murchison-Sedgwick re-interpretation of the north Devon strata, but argued that there was nowhere any evidence of the unconformity that should have been observed. Later, he objected to this 'slapdash' introduction of new systems into Devon by geologists who had not studied the rock as carefully as he had. He was the one professional geologist in this group, hired to do the survey--his job was on the line, as well as his reputation.
Then a local geologist in Devon discovered plant fossils in strata Murchison and Sedgwick had labeled Lower Silurian. Murchison had claimed there would be no plant fossils this far down. He resolved this apparent anomaly by re-classifying these Silurian strata as Old Red Sandstone. Sedgwick laughed-off this interpretation and chided Murchison for relying too heavily on fossils. Though both authors agreed that De la Beche's hypothesis was wrong--and by this time, even De la Beche agreed it needed modification--they could no longer agree on all the details of their own hypothesis. The sticky problem of the missing unconformity remained unresolved.
Fossils from the strata in contention showed strong parallels with the Carboniferous but with some additional, new fossils, none of which were from the Silurian. Nor did these fossils seem characteristic of the few that had been found in the Old Red. These fossils were found by Austen, one of the large group of talented amateur geologists who entered the controversy, and were identified by fossil specialists in London. In other words, a broadening network of actors was playing a role in this controversy, which was featured prominently in William Whewell's Presidential address to the Geological Society in February of 1838.
That summer, Sedgwick read a paper which focused primarily on his Cambrian system, which had few fossils, therefore making a correlation across regions particularly difficult. Sedgwick conceded that there was no unconformity in North Devon, which meant post-Cambrian and post-Silurian strata had to go down much farther than either he or Murchison had proposed previously. Sedgwick still claimed that the bulk of the strata of Devon were upper Cambrian, but only in one location in Cornwall was he absolutely sure, and from that location he derived a few fossils characteristic of the Cambrian. In a subsequent field trip, he found these characteristic fossils in other places he had identified as Cambrian, but also ones characteristic of later periods.
Shortly afterwards, Murchison published his magnum opus on the Silurian System; towards the end, he speculated that the Old Red Sandstone might be a system like the Silurian, which could be found all over the globe. As yet there were no characteristic fossils. No coincidence, De la Beche published the report of his survey shortly afterwards, and criticized the idea that local arrangements of geological strata represented systems valid globally. Furthermore, fossils were as local as strata, in the sense that a species that flourished at one time in England might flourish under the same conditions centuries or even epochs later in another part of the world. For De la Beche, the fact that species characteristic of the Carboniferous appeared in rocks he labeled Greywacke did not mean these were more recent strata; it simply meant that these species had flourished at different times in different places.
Murchison had paved the way for a solution to the Devonian problem with his suggestion that the Old Red might be a system. Perhaps the questionable strata in Devonshire belonged to the Old Red. However, this new hypothesis meant making three major concessions to De la Beche:
1) There was no unconformity below the Carboniferous in Devon; instead, Carboniferous passed conformably into Old Red.
2) The fossils in the proposed Old Red in Devon were not identical to those found in the Old Red elsewhere, which meant that Murchison would have to agree that fossil evidence was not totally reliable, that there were important local variations which could make using the fossil record problematic.
3) De la Beche had even hinted that there might be Old Red sandstone in Devon, although his overall interpretation of their place and role differed from Murchison's.
Finally, there was another problem. Sedgwick objected to this Old Red idea because it corresponded to strata he had labeled Cambrian--the amount of Cambrian in England was shrinking, and with it the possibility of finding more than a handful of distinctive fossils so it could be extended world-wide, like the Silurian.
Murchison persuaded Sedgwick to adopt this new hypothesis and the two published a paper written by Murchison in the Philosophical Magazine. Instead of conceding his debt to De la Beche, Murchison attacked him for using parts of their re-analysis of Devon without giving him credit--and then appropriated some of De la Beche's views as if they had been his own! Specifically, Murchison pointed-out that he and Sedgwick had discovered the coal- measures trough in central Devon, but also claimed they noticed how it passed conformably into strata below, giving De la Beche no credit for this discovery.
Then Murchison made a classic rhetorical move. He gave the widely-recognized fossil specialist William Lonsdale credit for realizing that "the South Devon rocks would be found to occupy an intermediate place between the carboniferous and Silurian systems" (Rudwick, 1985, p. 283). Indeed, Murchison chastised himself for not reaching the obvious solution sooner, and claimed he had relied too heavily on the character of the rocks and not enough on the fossils! This was a total rewrite of the actual history of the controversy to make it appear that the solution had been obvious all along and that it was really proposed by an authority outside of the controversy. The end of the article proposed a new Devonian system equivalent to the Old Red Sandstone that lay between Carboniferous and Silurian. Murchison conveniently glossed over many of the remaining difficulties, including the fact that there were no clear Silurian strata under the new Devonian system in Devon, nor did the new system have any truly characteristic fossils. The article was a brilliant polemic.
Murchison canvassed members of the Geological Society shortly afterwards, and happily concluded that if De la Beche attempted an angry rejoinder, "we have enough powder and shot in our tumbrils to sink him" (Rudwick, 1985, p. 287). Murchison eventually apologized for some of his more pointed remarks, but made no concessions regarding the new system, which he now traced to an even more respected elder, the fossil specialist William Smith. Murchison had now placed himself firmly 'on the shoulders of giants', to adopt Newton's felicitous phrase. He conveniently ignored the contributions of lesser, Devon geologists like Robert Austen who provided much of the fossil evidence.
The leading participants began to reach a consensus on this new point of view--even De la Beche conceded that the Devonian hypothesis had merit, especially as he felt the new synthesis vindicated some of his earlier views. But consensus was by no means universal, and could only be achieved by looking for the Devonian elsewhere. Murchison and Sedgwick traveled to the continent, where they were assisted by able European colleagues. "In the course of their long expedition, Murchison had turned most of the ancient Greywacke of the Rhineland into Devonian, only to find himself forced by the fossil evidence to turn much of it back into Silurian, leaving his confidence in the Devonian precarious if not collapsed. Sedgwick has seen his potential Cambrian annexed by the Devonian but later at least partially restored. He had totally lost confidence in the Devonian interpretation, of which he had been the nominal co-author only six months earlier. But whatever their differences, it would have been clear to both geologists that their best hope of resolving the Devonian problem, after almost five years of controversy, lay packed inside the boxes they had been sending back to London" (Rudwick, 1985, p. 329).
The newly discovered Devonian system was now on its deathbed--Sedgwick renounced it, Murchison had doubts, and others would soon follow. But Lonsdale and the other fossil experts showed that there was indeed a unique, intermediate group of fossils--that some of what Murchison and Sedgwick thought was Silurian was in fact Devonian. The difficulty was that there were Silurian fossils in the Devonian strata, in addition to other new fossils that promised to be characteristic of this system. Even with this evidence, Murchison had to work hard to persuade others. He took the campaign to Russia, where he found further evidence of the three systems and found evidence for a fourth, the Permian system.
Who discovered the Devonian? Clearly Murchison became its champion, the one who really persuaded others that it was a system--indeed, the one most responsible for the widespread adoption of the idea of a geological system. But if one asks who first found the evidence that pointed towards a new set of strata in Devon, then the picture becomes more complex: Lonsdale, Austen, Sedgwick and even De la Beche can be said to share part of the glory. In particular, after Lonsdale's fossil analysis resurrected the Devonian, geologists moved quickly to give him credit for discovering the system. Murchison and Sedgwick had to mount a counterattack to salvage their own claims, showing that not just fossils but field evidence played an essential role in establishing the Devonian.
The point is, the Devonian emerged out of a complex set of negotiations involving a number of actors. In contrast, the Silurian was more clearly a Murchison discovery and the Cambrian more clearly attributable to Sedgwick.
The three discoveries discussed so far have been modeled or simulated on a computer. No one has done this with the Devonian case, but Paul Thagard (Thagard, 1988) has simulated the resolution of a number of other controversies, including the oxygen/phlogiston debate and the controversy over whether a comet caused the extinction of the dinosaurs (Thagard, 1990). He used a connectionist algorithm in which a theoretical position is represented as a network of connections among hypotheses and pieces of evidence. A connectionist model of Murchison's Devonian hypothesis, as he presented it in the Philosophical Magazine, might include positive connections to the hypothesis that there were global geological systems, to evidence to the conformable passages in the Devon strata and to some of the fossils, but negative links to other fossil evidence and to the fact that there were no Silurian fossils. De la Beche's Greywacke alternative would have positive links to the conformable strata, but negative links to fossils and to the idea of global systems. If we ran a Thagard-type program, Murchison's hypothesis would doubtless win.
But note that we set up the links in this connectionist simulation from Murchison's perspective. If we took De la Beche as the primary viewpoint, any links to a universal system would be negative because he was suspicious of this idea, and links to fossil evidence would be at best neutral. As Thagard admits, one can set up a connectionist simulation so any side in a controversy wins, depending on whose perspective one takes.
The real value of Thagard's simulation is that it could allow one to experiment with what evidence might change a participant's point of view, if they were evaluating the evidence rationally. For example, what would a simulation built from Murchison's perspective do if one added a negative link between the Devonian hypothesis and the first geological evidence from the Continent, which suggested there were no Devonian strata? Would this be enough to cause the weights for the Devonian hypothesis to fall below a critical threshold? Could one also add in a negative weight for the defection of his main collaborator, Sedgwick, and see how that affected the result? All the weighting would be somewhat arbitrary, of course, but the point would be to play with the various connections and combinations, as a means of getting new hypotheses about the resolution of the controversy. Unfortunately, instead of seeing his connectionist simulation as a tool for play and exploration like Gooding and Addis' expert system, Thagard has argued that his simulation proves the correctness of his own philosophical position regarding the resolution of controversies (Gorman, 1989(a)). The point is, you could create a simulation from another perspective and show that worked as well--but it would work differently, and that is where the fun begins.
There is still no multi-agent simulation that will allow us to create different agents with different agendas, run the simulation, and gain a new perspective on how the different actors in the controversy might have interacted under different circumstances.
Is Murchison the hero in this controversy? If so, he is a different kind of hero than the 'disinterested pursuer of truth' that has been our guiding heroic metaphor to date. Murchison is more like a general, with his frequent references to campaigns and artillery. His goal is to defeat De la Beche and then conquer the world with his and Sedgwick's geological systems. De la Beche also uses military analogies to describe his reversals in the battles.
Contrast this competitive picture of the motives for doing science with the following, "If someone, for example, Charles Darwin, becomes fascinated by science, the work itself draws him on; if he works hard it is because the task is hard and he is engrossed in it... If he seems ascetic, it is because no jewel is more beautiful than the atom, no luxury cruise more fascinating than a voyage of discovery. The simple idea of task involvement provides the basis of understanding the organization of purpose of the working scientist" (Gruber, 1989, p. 250).
The exciting and frustrating thing about human beings is that, unlike billiard balls, we have multiple motives. It is no contradiction to seek a scientific truth in order to flatten an opponent. Indeed, this sort of competition may be critical to the advancement of science. Murchison alone could not have discovered the Devonian system. He needed to recruit allies, fight opponents and in the course of this, alter his own views to accommodate those of others, all the while denying any significant change in his position.
Could a multi-agent computational simulation have achieved the same result without these 'hot' motives? In the next chapter, we will consider a simulation with human beings that might help answer this.
Let us see how the Devonian case affects our generalizations about discovery.
1. Discovery depends on finding a problem significant enough to be labeled an important achievement.
The problem of the geology of Devon was certainly of local significance. Murchison deserves some credit for turning it into a problem of global significance by claiming that systems should be universal. A discoverer can play an important role in establishing the significance of a problem. Therefore, this generalization should be modified:
1. Discovery depends on establishing that a problem is significant enough to be labeled an important achievement.
If there is already a consensus that a problem is important, then a scientist needs to establish that her/his work is relevant to the problem.
Sometimes others establish this relevance post-hoc and even post-mortem. Consider the case of Gregor Mendel. According to the heroic myth, his 1865 paper on cross-breeding of traits in peas across successive generations was so revolutionary no one understood it at the time. In fact, it was well-received because, as Sir Ronald Fisher pointed out,
Each generation found in Mendel's paper only what it expected to find: in the first period, a repetition of the hybridization results commonly reported, in the second, a discovery in inheritance supposedly difficult to reconcile with continuous evolution. Each generation, therefore, ignored what did not conform to its own expectations (Brannigan, 1981, p. 102).
Indeed, others in the mid 1800s had found results similar to Mendel's. In fact, Fisher argued that Mendel's ratios were too perfect, suggesting that he knew what results he ought to get, and that influenced his classification of the peas. The mantle of discoverer was awarded to Mendel by a later generation; Gregory Bateson and others established him as champion of the view that inheritance depended on combinations of dominant and recessive genes. Mendel certainly raises these issues in his paper, but it is not clear that even he saw their full significance for the evolutionary debates raging at the time (Brannigan, 1981).
The first of the 're-discoverers' made a move similar to Murchison, who attributed the discovery of the Devonian to Lonsdale. Similarly, Hugo DeVries cited Mendel in a 1900 paper as an after-thought because DeVries immediately became involved in a priority dispute concerning the discovery of the laws of segregation and dominance. Correns, one of DeVries' competitors, realized he was going to lose the priority dispute and so neutralized that loss by speculating that DeVries owed his discovery to a close reading of Mendel's paper (Brannigan, 1981). Similarly, one might label Lonsdale the discoverer of the Devonian system only because Murchison established the significance of his fossil work and used his name to neutralize opponents.
2. Discovery depends on transforming that problem into a form that suggests a promising path to solution.
Murchison and others had to agree on the nature of the problem in North Devon before it could be solved. Was there really a problem at all? If so, what should be the role of fossils and rock types? Was one looking for a universal system or a local one? Whose expertise should weigh heaviest in debates? Problem creation and transformation often depend on intense negotiations among scientists. Again, the Mendel example is relevant--the significance of his work was transformed by other, later scientists.
3. Discovery depends on finding or inventing good data.
The Devonian case illustrates that what constitutes data is often the outcome of a process of negotiation. De la Beche's analysis of the rocks in Devon--as obvious to him as his nose--was dismissed by Murchison because he regarded the evidence from fossils as more important. But when it appeared everyone would take Murchison's rhetorical move seriously and label Lonsdale the discoverer, Murchison had to appeal to rocks to restore his own claim.
BACON was given the data that was produced by the long set of negotiations between Kepler, Brahe and others. Similarly, one could give a program--perhaps Thagard's--the picture of the data that emerged as a result of the controversy, and show that the program would reach the same conclusion as the participants. But the conclusion, at this point, would be embedded in the data.
Here generalizations two and three begin to merge. Transforming the problem transforms the data; transforming the data transforms the problem. So we could synthesize these two generalizations:
2. Discovery depends on transforming that problem into a form that suggests a promising path to solution, which includes locating and transforming the necessary data.
This is a much more controversial generalization than the previous one, as we will see in the next chapter, when we consider the cognitive literature on scientific problem-solving.
4. Discovery depends on a combination of flexibility and stubbornness, depending both on the individual scientist's cognitive style and on the nature of the problem.
The Devonian controversy shows how patterns of flexibility and stubbornness occur partly as a function of negotiations among participants in a controversy. Murchison appeared the most stubborn partly because when he changed his mind, he disguised the fact, as much as he could, to establish that his view was, and always had been superior to his rival De la Beche's. In contrast, De la Beche, who publicly made much greater concessions than Murchison, stuck to his view that there was a continuous series of conformable strata in Devon and in private, ridiculed Murchison. Sedgwick was perhaps the most flexible, beginning as an ally of De la Beche's, then shifting strongly to Murchison, gradually and reluctantly allowing the Devonian to supplant his Cambrian system in Devon.
One could argue that Sedgwick was the most secure of the three, in terms of his reputation, social position and employment. Murchison was out to make a name and carve out a new career, but had independent income. De la Beche's primary source of income was the survey, so he had to proceed in a way that antagonized as few geologists as possible.
So, this generalization places too much emphasis on the individual. We might re-word it as follows:
4. Discovery depends on a combination of flexibility and stubbornness, depending on the cognitive styles and career trajectories of the scientists involved and on how they represent the problem..
We could list a great many more factors in this generalization, but these few words will give the flavor. Whereas Faraday had to work hard to maintain the right balance between mental inertia and flexibility, it is possible in a controversy for some participants to adopt a more stubborn cognitive style, with flexibility emerging grudgingly out of competition. 'Career trajectories' can include relative eminence in the field, strategies for improving one's position and current or expected sources of funding. Problem representation can include theoretical commitments, like Sedgwick's desire to see his own Cambrian writ large--therefore, part of his problem in Devon became finding Cambrian fossils, which colored his perception of the strata.
5. The act of writing is part of the discovery process.
The act of writing in the Devonian controversy is an intimate part of the negotiations. Indeed, were it not for letters, there would be no detailed study of this controversy! Therefore, this controversy adds a type of writing to our list, which now includes letters--or e-mail in modern times--alongside notebooks and drafts of articles.
The four surviving generalizations suggest that discovery is not entirely mysterious, and that it can be taught, or at least encouraged. We hope to make them more precise by going more deeply into the relevant psychological and sociological literature in the next chapter.
These generalizations are also based primarily on a sample of 'classic', pre-twentieth century discoveries, although we have made occasional references to more recent discoveries. The kind of intense negotiations that went on in the Devonian case also characterized the discovery of the double-helix structure of DNA, though the pattern of negotiations was different. Our Murchison and Sedgwick in the DNA case are Watson and Crick, but whereas the former were gentlemen of science, Watson was a post-doc and Crick a Ph.D. student at the Cavendish laboratory. Furthermore, whereas Murchison and Sedgwick eventually took credit for discovering separate systems, Watson and Crick shared the credit for DNA. Still, both discoveries emphasize the importance of collaborative teams.
Watson and Crick took Linus Pauling's methods for finding the helical structure in a complex protein and applied them to the structure of DNA. Initially, they came up with a triple helical structure, but Maurice Wilkins and Rosalind Franklin quickly convinced them that this model was incorrect. Here Wilkins and Franklin played roles similar to figures like De la Beche and Austen in the great Devonian. Franklin, in particular, supplied a critical photograph that suggested the double-helical structure, and also important constraints the model had to satisfy. While Watson and Crick received the credit, one could argue that Franklin, Wilkins and others in the small scientific community focusing on this problem deserve some of the credit, just as the small community of geologists played a major role in discovering the Devonian period.
A quick skate through the list of four generalizations suggest that they could be applied to the discovery of the double helix, though we should remember that the primary source is the recollections of one of the discoverers and such recollections are not totally reliable (Ericsson & Simon, 1984).
1. Watson and Crick targeted a problem that was recognized as very important.
2. They transformed it into a form that suggested the path to solution and found or were given the appropriate data. According to Weisberg, the most significant problem transformation was the first one, suggested by Pauling: "There were thus several discontinuities in Watson and Crick's discovery: the change from three to two strands, the change in position of the backbones, and the change from parallel to antiparallel backbone chains. All of these discontinuities came about without restructuring; both alternatives existed as possibilities throughout the work because Watson and Crick had decided DNA was helical" (Weisberg, 1995, p. 60). However, if the other transformations or re-structurings were so trivial, one might ask why other researchers like Franklin, Pauling and Wilkins did not solve the problem. Watson and Crick had to do a great deal of physical modeling in an effort to find the correct sequence and structure, literally building the DNA sequence out of cardboard. This kind of modeling was favored by Pauling, but was anathema to Wilkins and Franklin.
The amount of transformation necessary to discovery varies from case to case. Consider an astronomical example: the location of the optical source of a pulsar. The transformation here was to recognize that the optical pulses recorded on an oscilloscope corresponded to a radio pulsar in the Crab Nebula. This is actually a significant transformation that would not be obvious to someone outside this area of astronomy, but was not a significant transformation for the astronomers involved. It was not a s trivial as a Baconian data-driven discovery, either--they had to check and re-check for artifacts and alternate explanations (Lynch, 1992).
3. Watson and Crick were both flexible and stubborn, sticking to their helical mental model but modifying the shape and arrangement of the structure as they found or were given new data.
4. It is not clear that writing played a major role in this discovery. Watson did jot down important ideas from time to time, though he did not keep a notebook. His breezy account of the discovery should be supplemented by a careful study of any written documents, including drafts of the research note announcing the discovery.
Communication, however, was extremely important. Watson and Crick were not only in constant conversation with each other, they were also in touch with Wilkins, Franklin and, through his son, with Pauling. They drew on the expertise of other scientists and laboratories as well. For example, Watson admitted that one of their greatest advantages was having the crystallographer Jerry Donohue in the office next door; it was Jerry who told Watson that information commonly available in chemical textbooks about guanine and thymine was wrong. This news eliminated the possibility that DNA was built on a 'like pairs with like' model; instead, adenine paired with thymine and guanine with cytosine.
Perhaps it would be better to broaden the generalization about writing to focus on communication, and keep writing as an important category:
5. Communication is part of discovery.
Important forms of communication include: A. Writing 1. Journal articles 2. Letters 3. Notebooks and rough sketches of ideas on scraps of paper B. Oral communication 1. Conference papers 2. Conversations
So, at least one twentieth century case-study has reinforced the relevance of the generalizations and helped us modify them. More and more excellent studies of twentieth century scientists are emerging; I encourage readers to try these generalizations on other cases. For example, Holton describes in elegant detail the way in which Einstein and Bohr transformed problems (Holton, 1973) and Galison takes us into the fine-grained negotiations involved in experimental physics (Galison, 1987).
The larger question is, can one make generalizations about discovery at all, or is each act of discovery entirely idiosyncratic? The problem with many studies of discovery is that they are framed in the language of the author, making comparisons difficult. Holton, Galison and Gruber use different frameworks and focus on different aspects of discovery. This is creative and may lead to a broader view of the phenomenon, but it makes comparison difficult.
In this chapter, I tried to pick discovery cases which were detailed and comprehensible enough to allow a reader to question the perspectives taken by those who studied them. The fact that each had inspired some kind of computational simulation gave us a basis for comparison. I cast these discoveries in my own framework, which I will discuss in more detail in the next chapter--in part so the reader will see my assumptions, and feel free to disagree with them.
What about failed discoveries? All of the above generalizations might characterize failures as well as successes. For example, Leverrier, who predicted the existence and position of Neptune, used the same techniques to predict the existence of a planet Vulcan between Mercury and the sun (Schaffer, 1994). Another astronomical case will provide us with a more detailed case of a discovery that wasn't.
In 1877, Schiaparelli discovered canali (channels) on the surface of Mars. Earlier observers had hinted at the existence of such features, but Schiaparelli's were sharper and more systematically arranged (Hoyt, 1976). Percival Lowell, a wealthy American astronomer who built his own observatory, turned Schiaparelli's channels into canals, and became their champion in a debate that lasted over a quarter of a century. He came up with a complex system of canals, which he claimed were built by an advanced civilization as the planet turned gradually into a desert. Lowell and Schiaparelli were not the only ones to see these canals; indeed, members of the British Astronomical Association reported seeing more than a hundred.
If this were a successful discovery, there would have been the usual argument about who deserved priority, Lowell or Schiaparelli. Instead, the blame for a false discovery was laid at Lowell's door.
Three problems eroded support for the canals:
1) Not all astronomers saw them. Lowell argued that he used superior observational techniques, including spending far more hours observing Mars than most other astronomers.
2) Experimental evidence with human participants. Several astronomers attempted to conduct crude experiments to find out whether the canals might be some sort of optical allusion. One of Lowell's own observatory group placed artificial planets at a distance of about a mile, studied them through a telescope and found that "some well known planetary appearances could, in part, be regarded as very doubtful..." (Hoyt, 1976, p. 160). He was fired for his pains. A British astronomer, E. Walter Maunder, asked school boys to copy pictures of Mars; they drew in canals, even though none were present. A similar experiment with French schoolboys yielded the opposite result, but even so, the British Astronomical Association concluded that those members who had claimed to see canals "really saw something very different from the straight lines they imagined they were looking at" (Hoyt, 1976, p. 160).
3) Improved astronomical equipment: Eventually, better telescopes and photographic equipment found no evidence of the canals--the last reported sighting came in 1924. By this time, Lowell had been dead for eight years.
Do our generalizations show evidence of a failed discovery in the making, in this case?
Generalization #1: Were the canali on Mars a major problem before Lowell?
Arguably not--like many discoverers, Lowell sought to establish the significance of what he had found. For example, he might, like Schiaparelli, simply have said he had seen mysterious lines on the face of Mars. Instead, he developed a theory concerning the presence of the lines that explained why they varied with the seasons and why on at least one occasion, new ones appeared.
Generalization #2: Did Lowell transform the data?
Certainly--in hindsight, it is obvious he created the data, and convinced others that they saw it, too. But he would have argued he was simply describing what was there. In other words, for Lowell, this was a data-driven discovery--the lines came first, and the theory followed. Of all the discoveries we have studied so far, Lowell's had the weakest grounding in prior theory. However, Alfred Wegener's theory of continental drift began with an observation about the way the shapes of the continents and the continental shelves fit together (LeGrand, 1988). Unlike Lowell, Wegener was able to refer to multiple lines of evidence in favor of his discovery: not only did the shapes of the continents match, but also the flora and fauna on either side, and continental drift could be used to explain patterns of global climate change.
Generalization #3: Did he maintain a balance between stubbornness and flexibility?
No--once he had established his theory and network of canals, he never altered it in the face of criticism. This stubbornness is often a hallmark of successful scientists (Mitroff, 1974). Wegener, for example, never abandoned continental drift, though he altered what the he philosopher Imre Lakatos (Lakatos, 1978) refers to as the corollary assumptions surrounding the hard core of a theory. For example, in response to criticisms from physicists, Wegener de-emphasized the portions of his hypothesis that attempted to explain how the drift occurred (LeGrand, 1988).
Generalization #4: Did writing play a role in his discovery?
Lowell wrote extensively about the canals, particularly for a general audience, including books, lectures and articles for Scientific American and Nature. He also published regular, detailed reports from his observatory and wrote lengthy letters to his critics, especially those who challenged his priority. Lowell's writing made the canals controversy and Mars itself a center of attention shortly after the turn of the century. It is harder to say what role these writings played in convincing the author himself. More detailed study of Lowell's notebooks and drafts is needed.
The Lowell example suggests that our generalizations do not clearly discriminate between successful and unsuccessful discoverers. Lowell's work was based less on theory and he was a bit more stubborn than most of the other discoverers we have studied. Basically, Lowell's problem was that the canals just weren't there. This kind of appeal to reality as the ultimate arbiter of scientific disputes is anathema to some sociologists of science, whose work we will discuss briefly at the beginning of the next chapter. But in terms of advice for future discoveries, the Lowell case suggests another generalization, one that we hinted at in the Faraday case:
6. Successful discoverers often pursue a network of related enterprises.
This is necessary so that if one potential discovery doesn't pan out, it is not fatal to the whole enterprise (Gruber, 1989). As noted above, Faraday was never able to translate gravity into electricity, but this was not fatal to his larger goal of demonstrating the unity of forces--his failure in one area was balanced by significant successes in others. Similarly, Lowell's persistent search for a 'Planet X' beyond Neptune was instrumental in the eventual discovery of Pluto (Hoyt, 1980). He patiently calculated and re-calculated the probable orbit of 'Planet X', and put the Lowell observatory to work searching for it at intervals between 1905-1916, but he died before it could be discovered. Still, the search for Planet X was one of the legacies he left the observatory. Clyde Tombaugh, who was hired by the observatory and given new equipment to search for Planet X, found Pluto at a position close to Lowell's predictions in 1930.
But was the discovery due to Lowell's calculations or to sheer persistence? The controversy raged for years. Pluto appeared to be much smaller than Lowell's Planet X--so small that it was doubtful it could have had calculable effects on the orbit of Uranus. In 1978, the discovery of Pluto's moon Charon confirmed that Pluto was tiny--a few thousandths of the Earth's mass--and therefore it was persistence and not theory that discovered Pluto.
This discovery suggests a seventh, not entirely tongue-in-cheek generalization:
7. Successful discoverers have to be lucky.
One can be persistent, have a mental model which prepares one to make a discovery and the best possible equipment, but still fail because there simply isn't anything to be discovered. Of course, even a failed search can generate lots of important information. Tombaugh continued to search for planets beyond Pluto, and he was able to determine that none existed above the 16th magnitude. This kind of negative information is very important. In the course of this search, he also discovered a wide range of interesting astronomical phenomena, including a new globular cluster and a cloud of some 1800 galaxies (Hoyt, 1980).
Obviously, one cannot teach students to be lucky, but one can remind them to be prepared to take advantage of surprises. The bit of mold that landed in Alexander Fleming's petri dish is the classic example--had he and Florey, Chain and others not diligently pursued this bit of serendipity, penicillin never would have been created (Macfarlane, 1984).
Similarly, Henri Becquerel put uranium salts, a copper cross and a photographic plate in a dark closet, awaiting a sunny day to test his idea that sunlight would make the phosphorescent uranium emit rays. But after several cloudy days, Becquerel developed the plate anyway, and found to his surprise that the image of the cross stood out on the plate. It was the Curies, Ernest Rutherford and others who eventually explained the phenomenon of radioactivity. Marie Curie, in particular, received two Nobel Prizes, one shared with Becquerel and her husband Pierre for the discovery of radioactivity and another on her own for the discovery and isolation of radium. Despite these accomplishments, she was never admitted to the French Academy of Sciences, which was at that time an all-male club. Marie Curie eventually paid with her life for her pioneering work, but her daughter carried on, earning her own Nobel Prize for the discovery of artificial radioactivity, which she shared with her husband, Frederic Joliot (Quinn, 1995).
Were Fleming and Becquerel lucky? Yes, but as Pasteur noted, "in the field of observation chance favors only the prepared mind" (quoted in Root-Bernstein1989, p. 87). They were both primed to take advantage of a surprise generated in the course of their research. We should also refer to prepared minds, in both of these cases--others took the initial discoveries and carried them forward to make penicillin and radium.
So, instead of making 'be lucky' a sixth generalization, let us recognize the importance of taking advantage of luck. This fits under generalizations four and seven: great scientists pursue a network of related enterprises and remain open to surprises that occur in the course of their research program.
Hopefully, this chapter has demolished the idea that process of discovery can be reduced to an algorithm. But hopefully we have also shown that it is not totally mysterious--that when one looks closely at cases of discovery, one can make generalizations about the process that would prove of value to students, managers and all those interested in how human beings have managed to find order in the universe.
Could these generalizations be made more rigorous? Might there be aspects of the discovery process that are more algorithmic? Could we give more specific advice to teachers and managers? In the next chapter, we plunge more deeply into the literature on cognitive psychology of science and, to a lesser extent, sociology of science in an effort to find out.
What about motivation? Earlier, we sketched a picture of the heroic scientist, motivated by a search for the grail--but also by a desire to stake out here or his claim to be the first to find it. Albert Szent-Gyorgi once cynically remarked that, "If any student comes to me and says he wants to be useful to mankind and to into research to alleviate human suffering, I advise him to go into charity instead. Research wants real egoists who seek their own pleasure and satisfaction, but find it in solving the puzzles of nature" (Szent-Gyorgi quoted in Holton, 1978, p. 235). Indeed, one could argue that even the hero who returns with the Grail can bring misery and suffering: witness Einstein's famous E=MC2, which made possible the development of atomic weapons (see Chapter 4 for more details).
Is it possible to seek the Grail of scientific knowledge while at the same time promoting one's own career and also trying to benefit others? We will consider these issues in greater depth in Chapters 4 and 5. For now, let us turn to the question of whether scientific methods could be used to gain a better understanding of the process by which scientific discoveries are made.
This page was last edited: Wednesday, July 14, 1999