Developing and Framing Meaningful Problems Daniel K. Lapsley University of Notre Dame SAGE Handbook for Research in Education: Pursuing Ideas as the Keystone of Exemplar Research (2 nd Ed) C.F. Conrad and R.C. Serlin (Eds). I. Introduction Induction into scientific practice hardly ever takes up the matter of how to formulate and frame meaningful problems. Most primers on research methods are geared to the culminating steps in research, on how to test, evaluate and dispose of hypotheses that otherwise seem to show up, like masked wrestlers, from ―parts unknown.‖ One might gather that educational and social science is mostly a technical matter of how to grapple unruly variables into submission; of how to assert proper experimental control, fit statistical models, and draw valid inferences. Nothing is trained so assiduously as the ability to indict a study for its yield of flaws. What is absent, however, is sustained reflection on the source and object of these exertions, which is a theoretical problem worthy of the effort. There is barely a word on how to ask questions, frame a problem, generate a theory; and very little guidance on what is to count as a meaningful problem or a good idea. In the absence of these considerations the default criterion is often sheer novelty---the good idea is that which has not yet been expressed or been found in print. Of course, the fact that an idea has never occurred to anyone is scarcely reason to invest it with meaning. Discovery and Justification: The Standard Account Karl Popper and Vienna Circle of logical positivists could claim some credit for this state of affairs. ―The work of the scientist,‖ Popper asserted, ―consists of putting forward and testing theories‖ (Popper, 1959, p. 30), although in his view only the theory-testing part of the work presented any interesting philosophical problems. How one happens to put forward a new idea was not worthy of notice. It always contains an ―irrational element‖ (p. 32). It is strictly a psychological matter of creativity, intuition and inspiration that can have no implication for the logical analysis of scientific knowledge. Nor is it possible to rationally reconstruct the steps by which a scientist comes to propose a theory. No logical analysis is possible for understanding how hypotheses occur to scientists; how inventions or discoveries cross their mind; for understanding ―the processes involved in the stimulation and release of an inspiration‖ (p. 31); there is ―no such thing as a logical method of having new ideas or a logical reconstruction of this process‖ (p. 32), but only for subsequent tests of the products of inspiration. Hence in this way are scientific methodology, logical analysis and rational reconstruction reserved strictly for justification but never for discovery. These strictures have solidified into a standard account that relegates the creation, invention, and origins of theory, the ―putting forward‖ of ideas, to the context of discovery of which little can be said; while the appraisal of a theory‘s evidential warrant is remanded to the context of justification, at whose disposal is placed the whole armamentarium of a discipline‘s methodological, analytical and logical tools. The context of discovery, if not entirely occult, is nonetheless beyond methodological specification, and is only preparatory to the real work of science, which is to justify winners among those theories that do manage show up for the match. One suspects that the lingering influence of the standard account in educational and psychological science has diverted attention away from the front end of discovery, invention and theory construction and towards the back end of justification, appraisal and evaluation. Standard Account Revisited Yet the distinction between discovery and justification has fallen on hard times. There is a consensus that there is a kind of logic of discovery that revolves around reasonable arguments for pursuing plausible lines of inquiry, and that these pursuit arguments are not irrelevant for theory appraisal. The arguments that make a line of research reasonable to pursue also have implications for how it is appraised once it is launched. Kordig (1978) argued, for example, that after the initial ―hitting upon an idea‖ one does, in fact, subject hypotheses to a kind of rational appraisal. One can deem them promising, worthy of exploration, meaningful, plausible to pursue, and all for good reasons. A question could be worthy of pursuit if its confirmation (―acceptability‖) constitutes a lethal blow against a rival; if it