Comments upon the document "America in the Age of Information," the Strategic Implementation Plan of the Committee on Information and Communications of the National Science and Technology Council, March 10, 1995. by Robert S. Boyer (boyer@cs.utexas.edu) Professor, Computer Sciences, Mathematics, and Philosophy Departments University of Texas at Austin and Computational Logic, Inc., 1717 W. 6th St., Suite 290 Austin, Texas 78703 June 27, 1995 The document "America in the Age of Information" should be very largely rethought because it fails to reflect an understanding that federal research funding should first and foremost be invested in basic research, rather than corporate welfare. The document proposes goals that are certainly reasonable but many of them are hardly inspiring, imaginative, or important for the federal government to pursue: to make computer systems bigger, faster, easier to use, and easier to learn. Why should the federal government pursue computer systems that are merely bigger, faster, easier, etc., and not pursue, say, automobiles or refrigerators with appropriate enhancements? Industry should be left alone to do these things, and will probably do them better. On the other hand, the document largely ignores that which it is most important for scientists to discuss when planning: what are the basic and fundamental scientific problems, and how might we possibly address them? I do not propose that we focus on basic scientific questions only in order to see basic science funded. Rather, it is my opinion that an emphasis upon basic research has by far the highest payoff for the federal research dollar. In support of this position, let me quote Prof. Donald Knuth, Stanford: The hardest applications and most challenging problems, throughout many years of computer history, have been in artificial intelligence---AI has been the most fruitful source of techniques in computer science. Because AI pursued the hardest questions, it attracted many of the greatest minds and resulted in the most amazing spinoffs. Take a serious look at the history of computing, especially the ARPA supported computing laboratories at MIT, CMU, Stanford, SRI, and BBN in the period 1960-1975. I believe that you will discover an amazing phenomenon. While researchers were left largely to pursue as their objectives such fundamental problems as how to get machines to do very intelligent things, the spinoff from this pursuit created the basis of much of the current computer industry. It is easy to trace back to ARPA supported research at these labs any of the following extraordinary pieces of modern industrial technology: word processing, networking, computer vision, symbolic manipulation, robotics, computer windows, the mouse, virtual memory, interactive computing, time-sharing, computer control of laser printers, and even video games! By focusing on the hardest of scientific problems, we will, on the one hand, make the greatest breakthroughs, attract the deepest minds, and see the most interesting spinoffs. (As for more immediate and direct payoff, Vic Reis, former ARPA director, has said that the DART system used in planning Desert Shield justified ARPA's entire investment in AI.) What are the hardest scientific problems in the area of computing? I cannot begin to assert that I know them all or that I can articulate them as well as possible, but I will venture to formulate some nevertheless, simply as an antidote to "bigger, faster, easier". 1. How can we represent information about the external world within a computer? The number of types of information is extremely vast and rich, encyclopedic it is not too much to say: musical, philosophical, physical, political ... We have hardly begun to see how to represent such information other than superficially, i.e., by storing text as simple sequences of bits. It is of the greatest importance and interest to learn how to represent the "information in the information" so that we can learn what to do with it. What is the theme in the music? What is the thought in the argument? What are the objects in the picture? What is the motive of the speaker? 2. How can we intelligently manipulate information within a computer? With the advent of modern logic, crucial to the history of computing, we have learned to make a few sorts of feeble inferences in a mechanical fashion about logical statements. But how can computers make inferences about other kinds of information? How can we get computers to make inferences about any sort of information within reasonable time and space limitations? The creation of intelligence via computer is the most exciting problem in computing. 3. How can computers learn? 4. How can digital systems acquire information about the world and how can they affect the world intelligently? The creation of the science of sensors and actuators for use with computers has only begun. The development of this topic will undoubtedly be integrated with the development of the representation of information. 5. How can the construction of computer systems become a science, in which clear thought prevails, rather than the mishmash of increasingly unintelligible pseudo-formalisms called "systems" in which computing finds itself today? The typical disclaimer of all warranty for most computer products should give us the greatest pause. Will anything trustworthy ever be built using current methods? The use of formal logic is undoubtedly a key here, but the practical use of formal logic, as opposed to its theoretical study, has only begun. The formalization of models of the world will be crucial to the specification of safety and of security critical systems. Automated formal reasoning may be essential to proving or checking theorems about safety or security critical computing systems. 6. How will computation deeply interact with biology? How can advances in the foundations of computing help in the search for representations of biological structure and function, e.g., chromsomal information? Can we build computers upon biological principles, thereby obtaining vast parallelism? To quote Knuth again, "Biology is so digital." In conclusion, let me reiterate that we can be relatively sure that industry will continue to see the greatest value in making computers that are bigger, faster, and easier. However, because of its concern with profitability, industry is much less likely to seek to achieve dramatic new insights into the potential of computing, and so a wise federal government will put its research dollar into the hardest and deepest questions about computers, some of which I have attempted to list above. A wise federal government will do this because it will understand that advances in basic science are crucial, that there are deep problems of basic science in computing, and that it is unlikely that industry will pursue such deep questions. (For those who do not know who Prof. Knuth is, let me mention that among his distinctions are National Medal of Science, National Academy of Sciences, National Academy of Engineering, American Academy of Arts and Sciences, Turing Award (Highest Award in Computing), and 18 Honorary Doctorates. Knuth is not generally regarded as being "in" artificial intelligence but is known primarily as a leading authority on algorithms.) Naturally, I speak only for myself, not for my employers. Appendix. In view of the following two reports, I wonder how much of the document "America in the Age of Information," was conceived prior to last November? 1. In the Wall Street Journal of May, 11, 1995, (p. A4) we find these brief remarks about the impact of the just proposed vast cuts in the Senate and House budget resolutions. True to GOP philosophy, basic research would fare better than anything with "technology" in the title. The National Science Foundation would be told to concentrate on grants for basic research rather than applied research that Republicans brand "corporate welfare." 2. On Thursday, 13 April, 1995, I read: An excerpt from "Views and Estimates", a letter from Rep Robert Walker (R-Pa), Chairman, House Science Committee to Rep John Kasich (R-Ohio), Chairman, House Budget Committee: "...In order for technological revolution to continue, a strong fundamental science base is needed....Budget realities dictate that basic research be reemphasized.....The President's FY 1996 budget submission for the programs under the Committee on Science totals $27.85B, up $840 M from the FY 1995 appropriated level... The Committee is concerned and disappointed that the Administration's FY 1996 budget submission makes no real effort at R&D priority setting.....While the Administration has elected not to make tough decisions, the Committee will not shirk its responsibilities and intends to produce responsible authorization bills that will reflect a commitment both to good fundamental science and a balanced budget. As a starting point, the Committee intends to authorize every agency under its jurisdiction at less than FY 1995 levels..... In prioritizing R&D funding, the Committee intends to apply the following six criteria: 1. ..FOCUS ON LONG-TERM NON-COMMERCIAL RESEARCH...LEAVING ECONOMIC FEASIBILITY AND COMMERCIALIZATION TO THE MARKETPLACE. 2. Federal funding... should not be carried...beyond demonstration of technical feasibility.. 3. Revolutionary new ideas and pioneering capabilities that make possible the "impossible" (that which has never been done before) should be pursued. 4. ..avoid funding research in areas that are receiving, or should be reasonable expected to obtain, funding from the private sector, such as evolutionary advances or incremental improvements. 5. Government-owned laboratories should confine their in-house research to areas in which their technical expertise and facilities have no peer and should contract out other research to industry, private research foundations, and universities. 6. All R&D programs should be relevant and tightly focused to the agency's stated mission....."