The following appeared in the Summer 1995 Stanford Medicine magazine:

Investigations that seemed totally irrelevant to any practical objective have yielded most of the major discoveries of medicine. Basic research is the lifeline of practical advances in medicine.

I like the story of the surgeon who, while jogging around a lake, spotted a man drowning. He dove in, dragged the victim ashore, and resuscitated him. He resumed his jogging, only to see another man drowning. After he dragged the second one out and got him breathing, he again wearily resumed his jogging. Soon he saw two more drowning. He also saw a colleague, a professor of biochemistry, nearby, absorbed in thought.

The surgeon called to the scientist to go after one drowning victim while he went after the other. When the biochemist was slow to respond, the surgeon shouted, "Why aren't you doing something?"

The biochemist responded, "I am doing something. I'm desperately trying to figure out who's throwing all these people into the lake."

This parable is not intended to convey a lack of regard for fundamental issues among clinicians, nor a callousness among scientists. Rather, it portrays the reality that a serious problem, a war on disease, must be fought on several fronts. Some contribute their special skills to the distressed individual while others try to gain the broad knowledge base necessary to cope with present and future enemies.

Both are essential.

But today we are suffering from the lack of adequate financial support for basic science, a poverty worsened by severe pressures to engage in "strategic" research, such as the treatment of breast cancer and AIDS or the development of biotechnologies to improve the economy.

Basic science has experienced stages of growth not unlike a microbial culture. Bacteria go through an exponential phase of growth, doubling every few minutes, until they inevitably exhaust the medium or some essential nutrient. Then, they go into a stationary phase.

We in the sciences have gone through an exponential phase of growth, and we now have to cope with some stresses and strains and lack of nutrients.

Three years ago, Bernadine Healy, then Director of the National Institutes of Health, developed a "Strategic Plan for Medical Research." A group of leaders in the basic and clinical sciences met in San Antonio to consider specific objectives and goals for the coming decades. In addressing the group, I pointed out that such a plan was fundamentally flawed because discoveries are commonly serendipitous. The best plan over many decades has been no plan. For lack of essential knowledge, timetables for assaults on particular disease targets have little meaning. Nor could we have anticipated the confrontations with novel diseases, such as AIDS, Legionnaire's Disease, septic shock and drug-resistant tuberculosis.

Medical research is still more a game of pool than billiards. You score points regardless of which pocket the ball goes into. This was eloquently explained recently by Harold Varmus, the present Director of NIH. In addressing the "Conference to Establish a National Plan on Breast Cancer," he cited his extensive studies on the virus that causes mammary cancer in mice, a line of research that I think he chose because of the breast cancer that killed his mother and her mother. Varmus' studies on breast cancer led to the discovery of cellular oncogenes, honored by a Nobel Prize he shared with J. Michael Bishop in 1989. Actually, Varmus' studies yielded no insights into human breast cancer, but they did provide an important advance in understanding brain development.

At the same time, a research program headed by Robert Weinberg at MIT, directed toward a rat brain tumor, did make a major contribution to understanding human breast cancer. Of the several genes now known to be involved in human breast cancer, all but one were discovered by researchers working on something other than breast cancer. Clearly, the ubiquity of biological design means that a specific disease model as a target is far too narrow to encompass the complexities of a disease process, such as cancer or a degenerative brain disease.

A well-designed plan, by its very nature, cannot lay the groundwork for the utterly novel techniques that make possible major transformations in the acqu the reagents for DNA analysis and the manipulations that created recombinant DNA and the genetic engineering revolution.

It may seem unreasonable and impractical--call it counterintuitive even to scientists--to solve an urgent problem, such as a disease, by pursuing apparently unrelated questions in basic biology or chemistry. Yet, the pursuit of curiosity about the basic facts of nature has proved throughout the history of medical science to be the most practical, the most cost-effective route to successful drugs and devices.

Investigations that seemed totally irrelevant to any practical objective have yielded most of the major discoveries of medicine--X-rays were discovered by a physicist observing discharges in vacuum tubes, penicillin came from enzyme studies of bacterial lysis, and the polio vaccine came from learning how to grow cells in culture. Cisplatin, a widely used drug in cancer chemotherapy, came about from studying whether electric fields affect the growth of bacteria and observing inhibition due to the unexpected electrolysis of the platinum electrodes. Once again, genetic engineering and recombinant DNA depended on reagents developed in exploring DNA biochemistry. All these discoveries have come from the pursuit of curiosity about questions in physics, chemistry and biology, apparently unrelated at the outset to a specific medical or practical problem.

Four years ago, a meeting in Washington celebrated the bicentennial of the U. S. Patent Office. From discussions among the inventors, corporate and government officials gathered there, a remarkable truth emerged. It was agreed that the age-old aphorism--"Necessity is the mother of invention"--is usually wrong. Generally, the reverse has proved to be true: Invention is the mother of necessity. Inventions only later become necessities!

Time and again, inventors created things that had to wait many years to be recognized for their practical value. Nobody really needed the airplane, the FM radio, television, or the quantum mechanics that led to the transistor.

Quite clearly, even industrial inventions emerge from a creative process. As such, they are haphazard rather than goal-oriented. The process of invention conflicts with prudent business strategy. A pioneering invention, almost by definition, is profoundly different from what a company has been doing. It is commercially unproven and therefore riskier than the established business.

The lessons to be learned from this history should be crystal clear. It is crucial for a society, a culture, a company to understand the nature of the creative process and to provide for its support. No matter how counterintuitive it may seem, basic research is the lifeline of practical advances in medicine; pioneering inventions are the source of industrial strength.

The future is invented, not predicted. Great innovations whether in art, literature or science, seldom take the world by storm. They must be cultivated to be understood, understood before they can be properly appreciated.

Of course it is important that basic discoveries be promptly and wisely applied to solve practical problems. The recent applications of biotechnology to medicine have given us major insights into diabetes, cancer and other metabolic diseases. Will these approaches and techniques be equally effective when applied to the human brain and behavior.

As our sphere of knowledge increases, so does the perimeter of our ignorance. The realm of the unknown will be populated by a vast menagerie of viruses, bacteria and fungi vying with ingenious genetic devices to invade and multiply in plant, livestock and human hosts. To cope with these and a variety of other problems, it is imperative that we continue to nourish the goose of basic research that has been faithfully laying the golden eggs of our knowledge of nature.

Arthur Kornberg, a Nobel laureate, is the Emma Pfeiffer Merner Professor of Biochemistry, Emeritus.