Still Crazy Enough to Study Aging

Curiosity about aging, stimulated by many long-lived relatives, motivated my research from the beginning. For many generations, some of them lived to age 90 or more. As a child I was intrigued by how differently people age, so that some retained mental clarity and memory into advanced old age while others began to fail 20 years earlier. Was this mostly hereditary, or also the result of nurtured expectations for high mental performance throughout life? Born in 1939 I thrilled to hear elderly relatives recall the days before 1900. Only six generations of passed-on stories brought me to the days when my grandmother’s great-great-grandfather was kidnapped by British soldiers. I regretted that no family yarns had come down from even earlier times. Once I calculated that the Roman Empire had ended only 80 generations before mine. The idea of doing research on the mechanisms of aging came when I was a Yale undergraduate. I was lucky to be befriended by Carl Woese, Don Caspar, Ernie Pollard, Dick Setlow and others in the biophysics department whom I met through a scholarship job. They included me in many free-wheeling discussions about the remarkable prospects for molecular biology that made me boil with excitement. In one session, perhaps in 1958, Carl said, “Why don’t you study aging? Nothing is known, and you are crazy enough to try.” I was also much influenced by two courses, Pollard’s on thermodynamics and Setlow’s on atomic physics, which stressed how crucial assumptions are to building theories. Like many others, I hoped that rigorous and comprehensive theories in molecular biology could emerge by using approaches that were so effective in physics. I considered research on aging now and again as a graduate student in my first years at the Rockefeller University, but not until I joined Alfred Mirsky’s lab did I begin work. Mirsky and Eric Davidson (then a junior faculty member in that lab) greatly helped to formulate my ideas about aging. The Mirsky lab of the 1960s was pioneering in gene regulation. Lab discussions about selective gene regulation and cell differentiation provided a crucial context for considering the clonal senescence of cultured diploid fibroblasts (the Hayflick phenomenon), which was attracting great interest as a model for senescence in more complex systems. Eric thoughtfully suggested as a thesis project that I fuse postmitotic (“senescent”) fibroblasts with other dividing cells as a way to probe the senescence of nuclear functions. In mulling this over, I became concerned that vital complexities in aging of postmitotic cells in the brain or other integrated organs could not be studied in cultured cells. Moreover, clonal senescence of fibroblasts seemed quite different from cell aging in the mammal, though it was not recognized until later that postmitotic fibroblasts did not necessarily die. The physics outlook that led me to scrutinize implicit assumptions also figured here. I wondered, too, if cell aging in vivo might reflect hormonal changes rather than the intrinsic aging mechanisms presumed for senescent fibroblasts. Potential hormone influences on cell aging seemed analogous to the inductive interactions during development that determine differentiated cell characteristics. Another influence was two papers that I chanced on while attempting to read all the literature in biogerontology (a goal that was feasible in 1965, but no longer). Birren and Wall’s 1956 study of the sciatic nerve in the Journal of Comparative Neurology found no loss of myelinated fibers or changes in their biophysical properties during the life span of the rat. This finding was the first serious challenge to the popular view that postmitotic neurons always deteriorate, and it fit my impression that mental strength could continue after the age of 90. The postmitotic cell might not, after all, be inevitably destined for senescence. A strategy I’ve often used, suggested in 1950 by Solomon and Shock in the Journal of Clinical Endocrinology and Metabolism, resolved age changes in human pituitary and adrenal functions by selectively challenging each level of regulation. Thus it seemed rewarding to ask cellular and molecular questions about complex physiological systems, which cultured cells could never represent. So I began to study hormonal mechanisms in aging. After false starts, I established a mouse colony with the C57BL/6J strain, chosen on Tibby Russell’s advice that they were a long-lived and healthy sort. I’ve stuck by these mice, looking to the days, which came only recently, when molecular genetic approaches to aging would be possible. Their inbred status later enabled studies of ovary-brain interactions during aging by ovarian grafting. While the founders of my present colony began aging, I examined enzymes regulated by hormones in hopes of finding a physiological aging process that could be analyzed with available probes at the level of gene regulation. I required that the enzyme system be regulated during physiological responses which change with age, that enzyme responses depend on modulations of gene expression and that enzyme-cells could respond directly to the same hormones involved in the physiological age changes. These requirements were met in liver tyrosine aminotranferase, which was rapidly induced by cold stress in young mice but showed striking delays in old mice. Perhaps the idea of cold stress occurred to me because of family elders who shivered while I was comfortable in shirtsleeves. I then showed that hormones that acted directly on the liver could induce this enzyme as fast in young or old. Thus gene functions could change with age because of altered extrinsic regulatory factors. This finding, also obtained by Dick Adelman (then at Temple University) using a different enzyme, suggested to me the hypothesis that neuroendocrine age changes could cascade to many other cells. Adelman and I were lucky to report similar results within a few months at the end of 1969, because we few researchers often waited years before data were replicated. " These studies on aging and stress then led me to study steroid-induced neuroendocrine changes in rodents, and catecholaniine changes of the rodent and human brain that help explain why some neurological diseases occur in specific adult age groups. In realization of long-sought goals, the new recombinant gene techniques have at last allowed my lab to start cloning genes implicated in aging, such as those involved in neuronal responses to cumulative effects of steroids or in Alzheirner’s disease. We now can look to insights about genomic mechanisms in cell aging, though I do not expect that the tremendous variety of aging phenomena in different cells and organisms will easily permit a unifying and rigorous theory of biological aging. Finch's lab is at the Ethel Percy Andrus Gerontology Center at the University of Southern California Los Angeles, CA, 90089-0191. (The Scientist, Vol:2, #2, p.14, January 25, 1988) (Copyright © The Scientist, Inc.) WE WELCOME YOUR OPINION. IF YOU WOULD LIKE TO COMMENT ON THIS STORY, PLEASE WRITE TO US AT EITHER ONE OF THE FOLLOWING ADDRESSES: editorial@the-scientist.com or The Scientist, 3600 Market Street, Suite 450, Philadelphia, PA 19104, U.S.A.

Still Crazy Enough to Study Aging

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