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On any new problem, of course, inductive inference is not as simple and certain as deduction, because it involves reaching out into the unknown. Steps 1 and 2 require intellectual inventions, which must be cleverly chosen so that hypothesis, experiment, outcome, and exclusion will be related in a rigorous syllogism; and the question of how to generate such inventions is one which has been extensively discussed elsewhere (2, 3). What the formal schema reminds us to do is to try to make these inventions, to take the next step, to proceed to the next fork, without dawdling or getting tied up in irrelevancies.

It is clear why this makes for rapid and powerful progress. For exploring the unknown, there is no faster method; this is the minimum sequence of steps. Any conclusion that is not an exclusion is insecure and must be rechecked. Any delay in recycling to the next set of hypotheses is only a delay. Strong inference, and the logical tree it generates, are to inductive reasoning what the syllogism is to deductive reasoning in that it offers a regular method for reaching firm inductive conclusions one after the other as rapidly as possible.

"But what is so novel about this?" someone will say. This is the method of science and always has been, why give it a special name? The reason is that many of us have almost forgotten it. Science is now an everyday business. Equipment, calculations, lectures become ends in themselves. How many of us write down our alternatives and crucial experiments every day, focusing on the exclusion of a hypothesis? We may write our scientific papers so that it looks as if we had steps 1, 2, and 3 in mind all along. But in between, we do busywork. We become "method- oriented" rather than "problem-oriented." We say we prefer to "feel our way" toward generalizations. We fail to teach our students how to sharpen up their inductive inferences. And we do not realize the added power that the regular and explicit use of alternative hypothesis and sharp exclusion could give us at every step of our research.

At the 1958 Conference on Biophysics, at Boulder, there was a dramatic confrontation between the two points of view. Leo Szilard said: "The problems of how enzymes are induced, of how proteins are synthesized, of how antibodies are formed, are closer to solution than is generally believed. If you do stupid experiments, and finish one a year, it can take 50 years. But if you stop doing experiments for a little while and think how proteins can possibly be synthesized, there are only about 5 different ways, not 50! And it will take only a few experiments to distinguish these."

  

One of the young men added: "It is essentially the old question: How small and elegant an experiment can you perform?"

  

These comments upset a number of those present. An electron microscopist said. "Gentlemen, this is off the track. This is philosophy of science."

  

Szilard retorted. "I was not quarreling with third-rate scientists: I was quarreling with first-rate scientists."

A distinguished cell biologist rose and said, "No two cells give the same properties. Biology is the science of heterogeneous systems." And he added privately. "You know there are scientists, and there are people in science who are just working with these over-simplified model systems - DNA chains and in vitro systems - who are not doing science at all. We need their auxiliary work: they build apparatus, they make minor studies, but they are not scientists."

  

To which Cy Levinthal replied: "Well, there are two kinds of biologists, those who are looking to see if there is one thing that can be understood and those who keep saying it is very complicated and that nothing can be understood. . . . You must study the simplest system you think has the properties you are interested in."

Any criticism or challenge to consider changing our methods strikes of course at all our ego-defenses. But in this case the analytical method offers the possibility of such great increases in effectiveness that it is unfortunate that it cannot be regarded more often as a challenge to learning rather than as challenge to combat. Many of the recent triumphs in molecular biology have in fact been achieved on just such "oversimplified model systems," very much along the analytical lines laid down in the 1958 discussion. They have not fallen to the kind of men who justify themselves by saying "No two cells are alike," regardless of how true that may ultimately be. The triumphs are in fact triumphs of a new way of thinking.

the emphasis on strong inference

is also partly due to the nature of the fields themselves. Biology, with its vast informational detail and complexity, is a "high-information" field, where years and decades can easily be wasted on the usual type of "low-information" observations or experiments if one does not think carefully in advance about what the most important and conclusive experiments would be. And in high-energy physics, both the "information flux" of particles from the new accelerators and the million-dollar costs of operation have forced a similar analytical approach. It pays to have a top-notch group debate every experiment ahead of time; and the habit spreads throughout the field.

Historically, I think, there have been two main contributions to the development of a satisfactory strong-inference method. The first is that of Francis Bacon (13). He wanted a "surer method" of "finding out nature" than either the logic-chopping or all-inclusive theories of the time or the laudable but crude attempts to make inductions "by simple enumeration." He did not merely urge experiments as some suppose, he showed the fruitfulness of interconnecting theory and experiment so that the one checked the other. Of the many inductive procedures he suggested, the most important, I think, was the conditional inductive tree, which proceeded from alternative hypothesis (possible "causes," as he calls them), through crucial experiments ("Instances of the Fingerpost"), to exclusion of some alternatives and adoption of what is left ("establishing axioms"). His Instances of the Fingerpost are explicitly at the forks in the logical tree, the term being borrowed "from the fingerposts which are set up where roads part, to indicate the several directions."

ere was a method that could separate off the empty theories!

  

Bacon, said the inductive method could be learned by anybody, just like learning to "draw a straighter line or more perfect circle . . . with the help of a ruler or a pair of compasses." "My way of discovering sciences goes far to level men's wit and leaves but little to individual excellence, because it performs everything by the surest rules and demonstrations." Even occasional mistakes would not be fatal. "Truth will sooner come out from error than from confusion."

Nevertheless there is a difficulty with this method. As Bacon emphasizes, it is necessary to make "exclusions." He says, "The induction which is to be available for the discovery and demonstration of sciences and arts, must analyze nature by proper rejections and exclusions, and then, after a sufficient number of negatives come to a conclusion on the affirmative instances." "[To man] it is granted only to proceed at first by negatives, and at last to end in affirmatives after exclusion has been exhausted."

  

Or, as the philosopher Karl Popper says today there is no such thing as proof in science - because some later alternative explanation may be as good or better - so that science advances only by disproofs. There is no point in making hypotheses that are not falsifiable because such hypotheses do not say anything, "it must be possible for all empirical scientific system to be refuted by experience" (14).

The difficulty is that disproof is a hard doctrine. If you have a hypothesis and I have another hypothesis, evidently one of them must be eliminated. The scientist seems to have no choice but to be either soft-headed or disputatious. Perhaps this is why so many tend to resist the strong analytical approach and why some great scientists are so disputatious.

Fortunately, it seems to me, this difficulty can be removed by the use of a second great intellectual invention, the "method of multiple hypotheses," which is what was needed to round out the Baconian scheme. This is a method that was put forward by T.C. Chamberlin (15), a geologist at Chicago at the turn of the century, who is best known for his contribution to the Chamberlain-Moulton hypothesis of the origin of the solar system.

Chamberlin says our trouble is that when we make a single hypothesis, we become attached to it.

  

"The moment one has offered an original explanation for a phenomenon which seems satisfactory, that moment affection for his intellectual child springs into existence, and as the explanation grows into a definite theory his parental affections cluster about his offspring and it grows more and more dear to him. . . . There springs up also unwittingly a pressing of the theory to make it fit the facts and a pressing of the facts to make them fit the theory..."

  

"To avoid this grave danger, the method of multiple working hypotheses is urged. It differs from the simple working hypothesis in that it distributes the effort and divides the affections. . . . Each hypothesis suggests its own criteria, its own method of proof, its own method of developing the truth, and if a group of hypotheses encompass the subject on all sides, the total outcome of means and of methods is full and rich."

The conflict and exclusion of alternatives that is necessary to sharp inductive inference has been all too often a conflict between men, each with his single Ruling Theory. But whenever each man begins to have multiple working hypotheses, it becomes purely a conflict between ideas. It becomes much easier then for each of us to aim every day at conclusive disproofs - at strong inference - without either reluctance or combativeness. In fact, when there are multiple hypotheses, which are not anyone's "personal property," and when there are crucial experiments to test them, the daily life in the laboratory takes on an interest and excitement it never had, and the students can hardly wait to get to work to see how the detective story will come out. It seems to me that this is the reason for the development of those distinctive habits of mind and the "complex thought" that Chamberlin described, the reason for the sharpness, the excitement, the zeal, the teamwork - yes, even international teamwork - in molecular biology and high- energy physics today. What else could be so effective?

Unfortunately, I think, there are other other areas of science today that are sick by comparison, because they have forgotten the necessity for alternative hypotheses and disproof. Each man has only one branch - or none - on the logical tree, and it twists at random without ever coming to the need for a crucial decision at any point. We can see from the external symptoms that there is something scientifically wrong. The Frozen Method, The Eternal Surveyor, The Never Finished, The Great Man With a Single Hypothcsis, The Little Club of Dependents, The Vendetta, The All-Encompassing Theory Which Can Never Be Falsified.

a "theory" of this sort is not a theory at all, because it does not exclude anything. It predicts everything, and therefore does not predict anything. It becomes simply a verbal formula which the graduate student repeats and believes because the professor has said it so often. This is not science, but faith; not theory, but theology. Whether it is hand-waving or number-waving, or equation-waving, a theory is not a theory unless it can be disproved. That is, unless it can be falsified by some possible experimental outcome.

the work methods of a number of scientists have been testimony to the power of strong inference. Is success not due in many cases to systematic use of Bacon's "surest rules and demonstrations" as much as to rare and unattainable intellectual power? Faraday's famous diary (16), or Fermi's notebooks (3, 17), show how these men believed in the effectiveness of daily steps in applying formal inductive methods to one problem after another.

Surveys, taxonomy, design of equipment, systematic measurements and tables, theoretical computations - all have their proper and honored place, provided they are parts of a chain of precise induction of how nature works. Unfortunately, all too often they become ends in themselves, mere time-serving from the point of view of real scientific advance, a hypertrophied methodology that justifies itself as a lore of respectability.

We speak piously of taking measurements and making small studies that will "add another brick to the temple of science." Most such bricks just lie around the brickyard (20). Tables of constraints have their place and value, but the study of one spectrum after another, if not frequently re-evaluated, may become a substitute for thinking, a sad waste of intelligence in a research laboratory, and a mistraining whose crippling effects may last a lifetime.

Beware of the man of one method or one instrument, either experimental or theoretical. He tends to become method-oriented rather than problem-oriented. The method-oriented man is shackled; the problem-oriented man is at least reaching freely toward that is most important. Strong inference redirects a man to problem-orientation, but it requires him to be willing repeatedly to put aside his last methods and teach himself new ones.

anyone who asks the question about scientific effectiveness will also conclude that much of the mathematizing in physics and chemistry today is irrelevant if not misleading.

  

The great value of mathematical formulation is that when an experiment agrees with a calculation to five decimal places, a great many alternative hypotheses are pretty well excluded (though the Bohr theory and the Schrödinger theory both predict exactly the same Rydberg constant!). But when the fit is only to two decimal places, or one, it may be a trap for the unwary; it may be no better than any rule-of-thumb extrapolation, and some other kind of qualitative exclusion might be more rigorous for testing the assumptions and more important to scientific understanding than the quantitative fit.

Today we preach that science is not science unless it is quantitative. We substitute correlations for causal studies, and physical equations for organic reasoning. Measurements and equations are supposed to sharpen thinking, but, in my observation, they more often tend to make the thinking noncausal and fuzzy. They tend to become the object of scientific manipulation instead of auxiliary tests of crucial inferences.

Many - perhaps most - of the great issues of science are qualitative, not quantitative, even in physics and chemistry. Equations and measurements are useful when and only when they are related to proof; but proof or disproof comes first and is in fact strongest when it is absolutely convincing without any quantitative measurement.

you can catch phenomena in a logical box or in a mathematical box. The logical box is coarse but strong. The mathematical box is fine-grained but flimsy. The mathematical box is a beautiful way of wrapping up a problem, but it will not hold the phenomena unless they have been caught in a logical box to begin with.

Of course it is easy - and all too common - for one scientist to call the others unscientific. My point is not that my particular conclusions here are necessarily correct, but that we have long needed some absolute standard of possible scientific effectiveness by which to measure how well we are succeeding in various areas - a standard that many could agree on and one that would be undistorted by the scientific pressures and fashions of the times and the vested interests and busywork that they develop. It is not public evaluation I am interested in so much as a private measure by which to compare one's own scientific performance with what it might be. I believe that strong inference provides this kind of standard of what the maximum possible scientific effectiveness could be - as well as a recipe for reaching it.

The strong-inference point of view is so resolutely critical of methods of work and values in science that any attempt to compare specific cases is likely to sound but smug and destructive. Mainly one should try to teach it by example and by exhorting to self-analysis and self-improvement only in general terms

one severe but useful private test - a touchstone of strong inference - that removes the necessity for third-person criticism, because it is a test that anyone can learn to carry with him for use as needed. It is our old friend the Baconian "exclusion," but I call it "The Question." Obviously it should be applied as much to one's own thinking as to others'. It consists of asking in your own mind, on hearing any scientific explanation or theory put forward, "But sir, what experiment could disprove your hypothesis?"; or, on hearing a scientific experiment described, "But sir, what hypothesis does your experiment disprove?"

It is not true that all science is equal; or that we cannot justly compare the effectiveness of scientists by any method other than a mutual-recommendation system. The man to watch, the man to put your money on, is not the man who wants to make "a survey" or a "more detailed study" but the man with the notebook, the man with the alternative hypotheses and the crucial experiments, the man who knows how to answer your Question of disproof and is already working on it.