Chapter 1
The Importance of Talking About Scientific Problems
[--- Unable To Translate Graphic ---]



As we near the end of a century whose philosophy has been profoundly influenced by the works of John Dewey and Karl Popper, it has become almost a common-place to say that knowledge is acquired through problem-solving, whether it be the struggles of a toddler to discover what lies behind a mirror or the smoothly coordinated efforts of an accelerator team to detect an omega-minus particle.
We no longer employ the metaphors of a wax tablet or empty bucket to describe the acquisition of information. Even Skinnerian conditioning requires the learner to be curious -- or at least engage in "exploratory behavior." A kitten who is passively moved around in a maze learns much less than its litter mate who iniates the same path. The Baconian/Lockean model of non-discriminating fact collecting is rarely endorsed these days except perhaps in the cautionary remarks of the foreman on an archeology dig who tells the crew not to throw anything away.
The metaphors of a lens or a searchlight are more congenial to our contemporary epistemologies, but unlike Descartes and Kant we do not believe that the concepts which shape our clearest thoughts and perceptions are immutable or beyond criticism. If even the basic principles of Euclidean geometry and Newtonian physics can be supplanted by scientific inquiry, what confidence can we have that any of our other fundamental principles are unrevisable?
So we view through a lens and we explore only selected areas of our universe -- despite the archeologist's advice. We cannot look at everything and, what is more unsettling, we cannot even inspect what we do focus on with a truly open mind. And the situation is complicated by the fact that we may even be forced to change our conceptual spectacles in the course of our investigation.
All of these features are nicely captured by thinking of inquiry as problem solving. The O.E.D. defines a problem as "a difficult or puzzling question..." This reminds us of the fact that scientific inquiry is challenging -- one cannot just deploy a bunch of conscientious data collectors. The O.E.D. defines solving variously as "loosening, dissolving, untying, unbinding, working out." This fits in well with our realization that the results of scientific problem-solving are not "final solutions." We "loosen or unbind" our difficulties; we "work out" a solution which "dissolves"our puzzlement or "unties"our conceptual knots. But our solutions may be temporary; often they are superficial and we look for a deeper, or finer-grained, or more comprehensive, or more elegant, or more accurate solution. A problem may have more than one solution, but typically the solutions are not all equally satisfactory.
I have said that it is a common-place that all knowledge acquisition, and the growth of scientific knowledge in particular, involves a process of problem solving. Given this, it is surprising how frequently expositors of knowledge neglect to spell out the problems which the doctrines they present are purported to solve!
Consider, for example, Russell's admirably lucid little book, The Problems of Philosophy. Russell is much better than most in stating the problems to which he will propose solutions. The book begins forthrightly enough: "Is there any knowledge in the world which is so certain that no reasonable man could doubt it?" (p.7) He then immediately goes on to show that this is a puzzling and difficult question. But in later sections of the book, some questions play more of a rhetorical role, as in "what is the nature of matter?" or "what is the value of philosophy?" Their main function appears to be to give Russell a chance to propound views on a variety of topics. In other chapters, such as the ones on intuitive knowledge and on idealism, discerning readers could probably construct for themselves the role of these ideas in the overall problem-situation, but Russell does not do it for them. Instead he merely says in the case of idealism, "the doctrine is so widely held, and so interesting in itself, that even the briefest survey of philosophy must give some account of it." (p. 37).
A nice example of the advantages of clearly stating the problem under discussion is provided by an essay of Popper's which is subtitled "My Solution of the Problem of Induction." Without now discussing the adequacy of his argument, his overall strategy is a good one. First, he distinguishes three problems of induction -- the common-sense problem and what he calls Hume's logical problem vs. Hume's psychological problem. He next criticizes the presuppositions of these problems and eventually replaces them with better formulated problems to which he then proposes solutions.
The procedure of disambiguating questions and scrutinizing their presuppositions is so obviously valuable that one wonders why it is not used more frequently. Recently my university has been exercized about "the" problem of computer literacy and "the" problem of values education. It often seems easier to debate the merits of proposals than to really analyze the problems we are supposedly solving!
Expositions of science are also very uneven in their emphasis on problems. Some books plunge directly into didactic subject matter. For example, Sears and Zemansky's popular text starts off as follows: "Mechanics is the branch of physics and engineering which deals with the interrelations of force, matter, and motion. We shall begin with a study of forces" (p. 1). In this text the behavior of falling bodies is merely presented as a "common example of motion under (nearly) constant acceleration" (p. 55). In Holton's historically and methologically oriented introductory text, on the other hand, we are informed of Galileo's problem- situation and the student learns about the Law of Falling Bodies and Kepler's Laws before Newtonian mechanics is presented.
Sometimes there is a perfunctory attempt to intrigue the student. My old introductory chemistry text waxed poetic in the first paragraph: "In autumn flowers wither in a single night...the hills are also changing...Constant change seems to be an inevitable law of nature." But then the problem of understanding change is shelved completely as the authors turn to the distinction between physical and chemical changes and the laws of conservation of matter and energy.
By contrast, Coulson's advanced monograph, Valence, lays out the problems it is addressing quite explicitly: Why do molecules form at all? Why do atoms aggregate in discrete numbers (the phenomenon of "saturation of valence")? Why do compounds have fixed geometries? (pp. 1-2) It is immediately made clear that any adequate theory of the chemical bond should provide answers to these questions.
Now it could be argued that it is not surprising that science books neglect problems. The story might go as follows: "Granted science grows through problem-solving. But once a clear gain is made, why bother the reader with the cognitive puzzlement which preceeded it? The discovery stands on its own. The historical circumstances of its origin may be used to motivate the student (cf. the Holton text). Or in the case of a research monograph like Coulson's where the readers are presumably already puzzled about valence, it may be convenient to start with an articulation of the problem situation. But in general there's nothing undesirable with presenting the facts/theories in a systematic, linear fashion."
One problem which this book will have to wrestle with is whether problems indeed are like scaffolding which can be discarded once a cognitive edifice is constructed. I will argue that they are not so disposable. Problem analysis helps us both in understanding and in criticizing a scientific doctrine. However, we will see that the problems emphasized for these purposes need not always be the ones which were most important in the actual historical development of the doctrine. But let us postpone the delicate and controversial issues of "rational reconstruction" (Lakatos) and "objective vs. subjective problem situations" (Popper) until the body of the book.
Let us now continue this preliminary sales pitch for the advantages of taking seriously the cliche' of science as problem solving. Much ink has been spilt on the purported distinction between the "nomothetic" and "idiographic" sciences. [Nomo - means "law," as in astronomy, laws of the stars, Idio - means .] It is claimed that certain lines of inquiry, say physics, concentrate on the search for more and more profound general laws while students of culture, by contrast, seek to give ever finer and more extensive descriptions of the unique properties of specific systems. This dichotomy results in all sorts of further issues: Are both activities "scientific"? Are their findings of comparable explanatory and predictive power? If not, what's "wrong" with the idiographic sciences? Does the "fault" lie in the vagaries of their subject matter or in the inadequate training of the practitioners?
The debate is multi-faceted but may be crudely summarized as follows: If one holds a unity-of-science position, then idiographic studies come out looking like second-rate or immature sciences. If one celebrates variety, then idiographic studies are seen as valid, but it is difficult to say exactly what differences in the nature of the objects studied leads to the differing standards for explanation, etc. One recent move by the unity-of-science camp is to deny that any disciplines seriously look for or make conjectures about universal laws. (See Giere.)
On this view, scientists work out detailed models and then see where they apply. For example, if geologists can develop a plate techtonics model of Continental Drift for our planet they don't really mind whether it's useful elsewhere in the solar system. Newtonian mechanics happened to have numerous applications, so the story goes, but we will not always be so lucky. If our model of the rise and fall of the Roman Empire doesn't apply smoothly to the Ottoman Empire or the British Empire, well then we just have to propose a wider variety of models of empires!
I am not at all sympathetic to this balkanizing tendency in philosophy of science. First of all, it obviously falsifies history -- Newton wasn't kidding when he spoke of his universal law of gravitation or titled Book III of the Principia "System of the World." And Skinner hoped to account for all learning, animal and human. Secondly, it suggests a facile pluralistic methodology which would deny the importance of the current search for a unified field theory, or the 19th Century chemists' attempts to give a unified theory of organic and inorganic compounds, or Galileo's problem of reconciling the terrestrial vs. celestial laws of motion in the science of his time.
So I disagree with the attempt to replace our concepts of scientific theory or law with the concept of model. However, I think there is a way to give a less pejorative gloss on the nomothetic/idiographic hiatus, namely by carefully analyzing the problems which different studies are designed to solve. It's immediately obvious that the question "Who shot Kennedy?" requires an idographic investigation, while the query "What are the causes of xenophobia?" will receive a more general treatment.
Once we have shifted the discussion to problems, we can then ask critical questions about problem-choice. Why do certain fields focus on certain kinds of questions? Are they considered to be more cognitively important (if so, why) or are they chosen for practical reasons (if so, what)? Can we say something useful about the choices between "big" questions and "little" questions? Are there institutional pressures to go after short term projects as opposed to long-term inquiry? Once again it seems that switching the focus from scientific results to scientific problems will help us better understand scientific inquiry.
Looking at problem-choice within the scientific community will also help us clarify the proper (as well as inevitable!) role of values in science. In this book I will espouse the rather old-fashioned position that the appraisal of the verisimilitude of a claim should be independent of our wishes about how the world should be. But I will argue just as strongly that since life is short and inquiry long, not only are we permitted to let values of all sorts--epistemic, economic, ethical--influence our choice of research problems, we are obligated to be conscious and critical of the values which help determine our choices. One of the central aims of this book will be to provide a framework for the responsible evaluation of research questions.
I will not attempt to provide a sharp criterion according to which certain questions would be censored because they are too hot to handle, but I will argue that problems should be prioritized. My personal view is that scientists most often err by working on boring problems, ones which are of low cognitive value as well as of little public interest. Working on "dangerous" problems (and we will of course have to carefully analyze this concept!) is probably much less common than working on projects which have little value by any standard.
Organized science is the primary institution dedicated to knowledge acquisition in our society, while the educational establishment is the agency charged with the job of efficient and systematic knowledge transmission with children being the main target audience. (The possible contributions of libraries, magazines, and newspapers are generally thought to be secondary - even for adults. Television is seen as being very effective, but the information conveyed is thought to be of low quality in a variety of respects.) Philosophers of education and educational theorists have often adopted the convenient assumption that the process by which a child learns somehow mimics the process by which scientists (the plural is deliberate) acquire knowledge -- a sort of epistemological version of ontogeny recapitulating phylogeny. Parallels have been drawn on various levels. Dewey emphasizes the methodological similarities: Both children and scientists start with puzzling situations and resolve their doubts by a process based on trial and error. Piaget and his followers also see resemblances in the temporal order in which basic concepts are acquired. Children struggle to attain the everyday concepts of causality and conservation which apply to colliding billiard balls and the transfer of lemonade, while our scientific ancestors had to struggle to articulate conservation laws and causal analyses which would apply to more complicated phenomena such as heat, electricity, and nuclear reactions.
I will argue that although children do learn by problem solving and that they can also learn to improve their methods of inquiry, there are absolutely crucial differences between working on a problem, the solution of which resides in the back of the book or the head of the teacher, and investigating a scientific question whose answer has no clear hallmark of correctness and which may even turn out to be unanswerable. We do children a disservice to make them think otherwise. On the other hand, it would be too frustrating to set problems for children where they frequently fail. It will turn out that the problem of how a problem-solving approach can best be used in a classroom (or even in a one-on-one tutorial situation) is a very complicated one. I will propose some rather modest guidelines which will at least make the activity less hypocritical. * * *
The general outline of the book is as follows. First, we ask: What kinds of problems are characteristic of scientific inquiry and exactly what role do they play in science?
To get some preliminary answers to these questions, we will look at some classic accounts of the development of science which view science as problem solving, especially the theories of Popper, Kuhn, Lakatos, and Laudan: My primary purpose will not be to evaluate these philosophies of science in their entirety. Whole books have already been written on the issue of whether Popper is right about induction or Kuhn is right about Gestalt switches. Instead I will rather opportunistically forage through their works in order to extract their views on the nature of scientific problems and their role in scientific inquiry.
Having surveyed the rich variety of scientific problems, we can then ask: What is the formal structure(s) of scientific problems? The answer to this question should help us in our later task of critically evaluating problems as well as providing a clearer and more economical account of scientific inquiry. Again we turn to the literature for starting points, especially articles by Nickles, Hattiangadi, and van Fraassen.
We next turn explicitly to the problem of evaluating problems. Here there are few systematic studies to draw on, although there are important papers by Agassi, Bromberger, and Laudan. I will propose various dimensions of appraisal but do not try to give a unique solution to the aggregation problem and argue that it would be unwise to do so. However, much confusion can be avoided if we clearly distinguish between the anticipated value of the solution to a problem (be that value cognitive, economic, political, or whatever) and the probability that, given the available scientific resources, we will be able to find a solution. The distinction between desirability and feasibility must always be clearly drawn.
So far, most of our discussion will have construed problems primarily in terms of logical relationships between propositions. Yet both the rhetoric of problem-solving, and our experience of it is profoundly psychological. And whereas there may be an infinite number of problems connected with an axiom system in some formal sense, humans (and computers!) can only concentrate on a few at a time so we must at least introduce some sort of salience factor. So we are now led to discussions of the subjective and psychological aspects of problems as well as to the curious metaphor within evolutionary theory according to which even biological species solve problems. We will then be in a position to arbitrate between strictly intellectual theories of science (according to which scientists are trying to unravel the secrets of the universe) and sociological accounts (according to which scientists are trying to figure out the secret to success, e.g. winning a Nobel prize). Of particular interest here is Hull's theory of the role of credit in scientific inquiry. I will also discuss Giere's theory of cognitive resources.
Having analyzed the structure of scientific problems and the various dimensions along which they may be evaluated, it is now time to make some policy recommendations about the prioritizing of scientific problems. I also make a preliminary excursion into the question of the desirability and practicality of a problems-approach in education.

Chapter I: Bibliography

Brush, Stephen G. (1973). Introduction to Concepts and Theories in Physical Science, Second Edition. Reading, Massachusetts: Addison-Wesley Publishing Company.

Coulson, C.A. (1952). Valence. Oxford: At the Clarendon Press.

Hopkins, B. Smith and John C. Bailar, Jr. (1951). General Chemistry for Colleges, Fourth Edition. Boston: D.C. Heath and Company.

Russell, Bertrand (1912). The Problems of Philosophy. London: Oxford University Press.

Sears, Francis W. and Mark W. Zemansky (1950). University Physics. Cambridge, Massachusetts:
Addison-Wesley Press, Inc.