Sci. Aging Knowl. Environ., 2 November 2005
Vol. 2005, Issue 44, p. pe33
[DOI: 10.1126/sageke.2005.44.pe33]


Developing a Research Agenda in Biogerontology: Basic Mechanisms

Huber R. Warner

The author is at the College of Biological Sciences at the University of Minnesota, St. Paul, MN 55108, USA. E-mail: warne033{at}

Key Words: cell senescence • apoptosis • oxidative stress • longevity genes • caloric restriction • Hutchinson-Gilford syndrome • stem cells


This article is adapted from a presentation I made at the 34th annual meeting of the American Aging Association in Oakland, California, on 5 June 2005, and an article in AGE (1) that resulted from that presentation. From July 1984 through May 2005, I was a staff member of the National Institute on Aging (NIA), serving the last 5 years as an Associate Director with responsibility for the Biology of Aging Program. The mandate of the Biology of Aging Program has been to fund research on the molecular, genetic, cellular, and physiological changes that accompany aging and underlie the development of adverse nonneurological age-related pathology. By 1984, biogerontology research was still mostly focused on testing theories of aging and on characterizing aging in humans and various animal models, especially mice and rats. As Couzin expressed it in the 1 July 2005 issue of Science, "Just 2 or 3 decades ago, research on aging was a backwater" (2). While at NIA, I witnessed, and was directly involved in, the transition of biogerontology from a very descriptive science to an increasingly mechanistic science. I will briefly discuss below a few of the areas where real progress has occurred in understanding the molecular basis of aging and age-related disease since I joined the NIA staff in 1984. This is also written as a personal reflection of some of the roles I believe my NIA colleagues (Jill Carrington, David Finkelstein, Anna McCormick, and Felipe Sierra) and I played during this transition from descriptive to more mechanistic research.

NIA Strategies for Development of Research Initiatives

Over the past 20 years, NIA has developed fairly standard procedures for developing new research initiatives. Most initiatives begin with individual NIA program staff members, who through reviewing the literature, attendance at scientific meetings, and monitoring progress on active grants in their portfolio(s), identify a new research need or opportunity. They often follow up by organizing a workshop or small meeting of investigators working in relevant fields, both to obtain advice and to evaluate whether their idea is ready for development. If the answer is yes, the proposed initiative will be discussed with other NIA staff members at one of two annual retreats NIA holds each year. At these retreats, requests are made to the NIA director to set aside funds to support the initiative, and if the director agrees that the initiative has promise, and if adequate funds are available, the director will allocate funds consistent with the relative importance and scope of the initiative. Finally, the initiative must be approved by the National Advisory Council on Aging before a Request for Applications (RFA) can be published in the National Institutes of Health (NIH) Guide. The RFA mechanism thus guarantees that a minimum amount of research will be supported, provided applications of sufficient merit have been submitted, and these applications are reviewed by a group convened especially for this purpose. This entire process may require as much as 2 to 3 years from initial conception to funding.

If an initiative is collectively deemed to be important enough to proceed, but not appropriate for an allocation of set-aside funds, it can be published in the NIH Guide as a Program Announcement (PA), which identifies it as a special area of interest to NIA, but the review is normally done by the Center for Scientific Review, not by a special review group, and specific funds are not set aside to fund the applications. The PA is the more frequently used mechanism to announce an initiative, primarily because it does not require a specific allocation of funds and because it can remain active for up to 3 years. Because research areas frequently overlap among two or more NIH institutes, initiatives are often sponsored by more than one institute, and this is more common for PAs than it is for RFAs.

The state of the art in biogerontology in 1984 depended on three salient observations: (i) restricting caloric intake [a process known as caloric restriction (CR)] increases longevity and delays the onset of age-related disease in rodents (3); (ii) oxygen radicals are continuously produced in vivo and damage cellular macromolecular components (4); and (iii) human fibroblasts grown in culture have a finite life span (5). While these three ideas still provide much of the basis for biogerontology research today, so much progress has been made in fleshing out details that the journal Cell devoted its entire 25 February 2005 issue to reviews of aging-related research. NIA initiatives to promote research in these and other areas are very briefly reviewed below.

Cell Senescence

When cells die, maintaining adequate tissue function requires that these cells be replaced either through proliferation of a neighboring cell, or through recruitment of cells from an appropriate stem cell or progenitor cell niche. However, senescent cells are unable to proliferate and replace these dead cells. By 1984, cell senescence was an established in vitro phenomenon, but little was known about the mechanisms by which it occurs, whether senescent cells occur in living organisms, or what the potential impact is if they do. These seemed to be tractable questions, so I chose cell senescence as my first research initiative. Hence, we organized a series of workshops on the mechanisms of cell senescence in 1986, 1989, and 1992, and published a PA in 1986 titled "Control of cell proliferation in senescent cells." The latter two workshops were held in Montreal, Quebec, with Eugenia Wang as the local host. This has been a fairly productive initiative and has led to a number of important discoveries about how the cell cycle is regulated.

An early breakthrough was made by Seshadri and Campisi (6), who showed that senescent fibroblasts cannot induce the expression of the c-fos gene; the c-fos protein is a transcription factor required for fibroblast proliferation. This finding was followed by the important discovery that senescent cells produce an inhibitor of the cell cycle called p21 (7, 8). Another important breakthrough occurred when Harley et al. (9) showed that telomere shortening occurs with increasing number of generations in culture and that once telomeres reach some minimum length, replication stops. Some time later, Bodnar et al. (10) demonstrated a strong linkage between proliferative potential and the presence of telomerase activity in human fibroblasts and that transgenically expressed telomerase could overcome the senescence-induced block to proliferation. In the meantime, an increasing number of proteins have been implicated in telomere binding and regulation of the structure and function of the telomere (11, 12). Mice deficient in telomerase activity are initially viable, but by the third generation of inbreeding they begin to show aging-like phenotypes, and by the fifth generation they can no longer reproduce (13). Furthermore, humans with dyskeratosis congenita are deficient in telomerase activity and proliferative potential and develop numerous pathologies (14). Although it has been proposed that telomerase could be a target for anticancer drug therapy, telomerase seems to be a factor in maintaining health and function during aging, presumably being required for stem cell and lymphocyte proliferation and for production of germ cells.

An important and persistent question in the field of aging has been whether human cells senesce in vivo and, if so, what impact this has. Using the senescence-associated {beta}-galactosidase assay, Dimri et al. (15) showed that some human cells do senesce in vivo. This phenomenon could potentially create a tissue environment that synergizes with oncogenic mutations to drive the rise in cancer incidence with age, because senescent cells secrete factors that disrupt tissue architecture and/or stimulate nearby cells to proliferate (16, 17) (see "Faustian Bargain" and "Led Astray"). Thus, "the senescence response may be antagonistically pleiotropic, promoting early-life survival by curtailing the development of cancer, but eventually limiting longevity as dysfunctional senescent cells accumulate" (18).

Cell Death

Soon after we started the cell senescence initiative, I began to wonder whether senescent cells resist cell death in vivo, and thus compromise tissue function in this way. Eugenia Wang, Gabriel Fernandes, and I even suggested that CR promotes death of senescent cells (19), and that this could partially explain the benefit of CR. Although it had long been known that cell death occurs routinely in many tissues during development, the genes by which cell death is programmed were not known until Robert Horvitz's isolation of nematode mutations in cell-death genes, known as ced genes (20). Thus, in 1989 I issued a PA ("Mechanisms of cell death in aging") soliciting proposals to elucidate mechanisms of cell death during aging. One of the first applicants funded in response to this PA was Junying Yuan, who shortly thereafter demonstrated that the Caenorhabditis elegans ced-3 gene codes for a protease similar to mammalian interleukin-1{beta}-converting enzyme, also known as ICE (21). This discovery eventually led to the identification of a series of proteases, now called "caspases," that play various roles in programmed cell death (apoptosis). This work was summarized recently (22).

Although the general outlines of the execution pathways in apoptosis have now been worked out (23), much remains to be learned about (i) how this process is triggered, (ii) how the stimulus is transduced to the execution machinery, (iii) how the tissue specificity of different apoptotic pathways is determined, and (iv) how tissue structure and function are retained when cell death does occur. It is of utmost therapeutic importance to determine the molecular basis for the neuronal cell specificity of apoptosis observed in various neurodegenerative diseases such as Parkinson's disease, Alzheimer's disease, and amyotrophic lateral sclerosis, so that specific treatments can be devised to delay the onset of these pathologies.

Like cell senescence, apoptosis is a two-edged sword; it is required both for normal development and to remove damaged cells that could become transformed into cancerous cells, but the loss of cells in nonproliferative tissues via apoptosis can have severe pathological consequences (24, 25). In contrast to the role of apoptosis in specific diseases, a generalized role for apoptosis in aging is not yet well developed, but evidence for this role is mounting (25). For example, ablation of p66shc lengthens life span in mice (26), as p66shc may be transducing damage signals to the cell-death machinery by acting as a hydrogen peroxide generator (27) (see "Detour to Death").

Oxidative Stress

Since Denham Harman proposed that oxygen free radicals are a major factor in aging (4) (see Harman Classic Paper), considerable effort has been expended by the biogerontology research community to "prove" this theory of aging. Despite these efforts, many of them funded by NIA, no consistent picture emerged concerning the role of oxidative stress in aging, so I organized a workshop in Berkeley, California, in 1992 to discuss promising avenues for research on aging and oxidative stress. NIA then issued a PA titled "Oxidative damage, antioxidants, and aging" later that year to encourage submission of proposals in this area of research. This initiative was partly responsible for the fact that in fiscal year 1999 (the only year for which this analysis was done), NIA committed the second-highest amount of extramural research funding to support research on oxidative stress compared with other institutes in NIH and the highest amount based on the percentage of its total grant budget (28). There is an ongoing commitment at NIA to fund research clarifying the relation between free-radical damage and aging processes.

After reading a review article by Douglas Wallace (29) on the way to the meeting in Berkeley, I encouraged David Finkelstein to develop an initiative on the role of mitochondrial dysfunction in aging. Although there was wide acceptance that mitochondria generate oxygen free radicals in the course of normal metabolism, and that these free radicals damage nucleic acids, proteins, and lipids, it was not clear whether these free radicals actually cause or merely correlate with adverse aging changes. This situation remains true even today (30) (see Dugan Perspective). Nevertheless, CR reduces oxidative stress (31), and in several examples, overexpression of antioxidant enzymes does correlate with genetically induced life-span extension (32, 33). Therefore, it was a surprise that mice heterozygous for the gene encoding the mitochondrial manganese-containing superoxide dismutase activity (Mn-SOD) exhibit more oxidation of DNA and higher cancer incidence than wild-type controls, but do not die prematurely (34). Furthermore, mice with a proofreading-deficient mitochondrial DNA polymerase age rapidly but without a concomitant increase in oxidative damage in total liver DNA (35). These findings do not support the idea that nuclear DNA damage is a critical factor in aging. In contrast, transgenic expression of catalase targeted to the mitochondria, where it is not usually expressed, does lengthen life span (36), suggesting that oxidation of mitochondrial DNA may be a more critical factor, as proposed by Barja (37) and others.

Although DNA damage has long been assumed to be a major factor in aging, oxidative damage to specific proteins such as mitochondrial cis-aconitase (38) and adenine nucleotide translocase (39), and/or lipids, may be a more critical factor in aging than is global oxidation of DNA bases, but more research is needed to establish this view. Peroxidation of unsaturated fatty acids in complex lipids produces many toxic products, including 4-hydroxy-2-nonenal (4-HNE). These compounds can cross-link proteins and inhibit the degradation of altered proteins by the proteosome (40), thus compromising the ability of the cell to rid itself of damaged and/or aggregated proteins. Such aggregates have been implicated in a variety of neurodegenerative diseases, but in no case is it clear whether, or how, the aggregates actually cause the disease.

Longevity Genes

For the purpose of this brief discussion, a "longevity gene" is any gene that can be manipulated to increase life span. In 1984, Tom Johnson's long-lived C. elegans age-1 mutant had already been isolated and partially characterized (41). The idea that a mutation would actually increase life span seemed counterintuitive to me then, and therefore unlikely to be a general result, even for an organism as uncomplicated as a nematode. However, when I returned from a meeting at the Jackson Laboratory in 1988, where I heard Michael Rose discuss his own work (42) and that of Luckinbill et al. (43), showing that long-lived fruit flies could be obtained by selecting for mothers able to reproduce late in life, I came to believe that alleles or combinations of alleles with regulatory effects on longevity exist and have the potential to be identified and characterized. Thus, I encouraged Anna McCormick to develop an initiative to identify these genes. Following a couple of workshops held in Irvine, California, she issued an RFA in 1992 on longevity assurance genes titled "Genetic and molecular basis of aging."

The initiative was renewed with RFAs in 1998 and 2003, and once the human genome sequence became available, it was possible to show that the C. elegans age-1 gene codes for a phosphatidylinositol-3-kinase-like protein (44), which functions in the insulin-like signaling pathway. Many daf-2 mutations also promoted longevity, and the daf-2 gene was identified as an insulin-like receptor (45). These results placed two nematode longevity genes in the same pathway, suggesting that it can play a role in regulating longevity. This finding stimulated research to determine whether a similar situation obtains in fruit flies, and it does (46, 47). Furthermore, the observation that dwarf mice unable to produce growth hormone (GH) in the pituitary gland (48), or to respond to it (49), are also long-lived, indicates that insulin-like growth factor-1 (IGF-1) levels also regulate longevity in rodents, as the GH pathway triggers IGF-1 production (see "One for All"). A detailed discussion of this initiative was previously published in SAGE KE (50). The relevance of this work to humans and other primates is an important unanswered question (see "Power to the People" and "Will Humans Join the Club?").

Numerous genetic and a few pharmacological interventions that increase longevity in these various model organisms have now been identified, and much of this information has recently been summarized elsewhere (51). These interventions are usually associated with one of the following processes: (i) insulin signaling, (ii) stress resistance, or (iii) caloric deprivation. An NIA-funded program to take advantage of this knowledge by rigorously testing the effects of promising compounds on survival of genetically heterogeneous mice has been under way for more than 2 years (52). By now at least eight compounds are currently in trials. Compounds that significantly increase longevity will also be tested for their effects on development of age-related pathology.

Caloric Restriction

In 1988, Weindruch and Walford reviewed the status of knowledge about the effect of CR on aging and longevity in rodents (53). CR extends both mean and maximum life span and delays the onset of age-related diseases such as cancer, diabetes, kidney failure, and autoimmune disease, but the underlying mechanisms for these effects are poorly understood. To address this knowledge gap, NIA issued an RFA titled "Molecular and neural mechanisms underlying the effects of caloric restriction on health and longevity" in 2001, and 13 applications were funded by the Biology of Aging Program. At the time this RFA was issued, it was known that CR delays many age-related changes in gene expression, reduces oxidative stress, and increases the resistance of the animal to a variety of other stresses, including heat, UV light, and free-radical generators. CR can be mimicked by genetically suppressing appetite in mice (54).

One of the new findings to come out of the applications funded in response to the RFA is that activators of sirtuins (a family of protein deacetylases) may be mimicking CR in yeast (see Lamming Science paper), and Guarente and Picard (55) have suggested that protein deacetylation by sirtuins may play roles in "sensing low calories and triggering changes linked to health and longevity." One of these activators is resveratrol, a natural compound found in some foods and in red wine (56). Over-expressing the sir-2 gene in nematodes also increases life span (57), but it remains to be shown whether sirtuins are involved in CR in mammals.

In late 2001, NIA also issued an RFA ("Caloric restriction and aging in NIA nonhuman primates") for applications proposing to use the NIA calorically restricted rhesus monkey colony for limited noninvasive studies in cooperation with NIA intramural staff. Too few animals have died in the studies going on at the University of Wisconsin and the NIA Intramural Program to yet determine whether the monkeys undergoing CR have an extended life span, but the physiological changes seen so far do parallel those seen in calorically restricted rodents (58). Although it is too early to predict whether CR will extend longevity in humans, several gerontologists have pointed out that if it recapitulates the extension seen in rodents, CR rigorously practiced by humans would have a greater impact on longevity than eliminating deaths caused by age-associated conditions such as cardiovascular disease, cancer, and stroke (59).

Hutchinson-Gilford Syndrome: A Human Premature Aging Syndrome?

The final initiative I will discuss is one we backed into because of a meeting between Leslie Gordon of Tufts University and NIA staff in 2001. At this meeting, Gordon urged NIA to respond to congressional language about supporting research on Hutchinson-Gilford progeria syndrome (HGPS), an early progeroid syndrome that had by then drawn little more than curious and skeptical attention from the gerontology community. As a result of this discussion, I agreed that NIA would cofund a workshop with the NIH Office of Rare Diseases to discuss the possibilities for research on HGPS. Although only a few of the participants at the workshop had actually worked on HGPS, the discussion was very productive, and I came away from the meeting wondering if the underlying problem in HGPS might have something to do with inadequate cell replacement following excessive cell death, particularly in mesenchymal tissues. This hypothesis would explain not only the small stature of these patients (the typical patient only reaches about 3 feet in height) but also the selective nature of the affected tissues.

To encourage research, I issued a PA titled "Innovation grants for research on Hutchinson-Gilford progeria syndrome," hoping that the identification of the gene responsible for HGPS would be accomplished and lead to better insights about research possibilities. Although neither research laboratory was actually funded as a result of this PA, two independent laboratories soon and simultaneously reported that the gene responsible for HGPS coded for the nuclear envelope proteins lamin A and C (60, 61). To take advantage of this new information, NIA quickly followed up with a new PA titled "The biological basis of Hutchinson-Gilford syndrome: Relationship to mutations in the lamin A/C gene (LMNA)." The relevance of this syndrome to normal human aging remains unclear, but the production of a variety of mouse mutants that appear to age prematurely may help sort this out (see below).

If lamin A mutations disrupt the nuclear envelope (60, 62) and predispose the affected cells to undergo apoptosis in both mice and humans, stem cell replacement therapy might provide an actual cure for this condition, if applied early enough before overt pathology develops. This therapy would require isolating stem cells from an appropriate niche in the patient (perhaps in bone marrow), repairing the genetic defect, amplifying the repaired cells, and returning the cells to the patient to repopulate the niches and eventually replace the defective cells altogether through the selective survival advantage these repaired cells would have over the defective cells of the patient. This strategy appears to have been successful in the experiments reported by Sampaolesi et al. (63) to treat a mouse model for limb-girdle muscular dystrophy. An alternative approach might be to use cord blood cells as was done by Staba et al. (64) in human patients to treat Hurler's syndrome, a mucopolysaccharidosis leading to progressive deterioration of the central nervous system. The technique apparently worked because cord blood cells are tolerated reasonably well by a heterologous recipient.

Mouse Models of Premature Aging?

My interest in HGPS was also tweaked by the growing list of mouse mutants defective in some aspect of DNA metabolism that are small, display aging-like phenotypes, and die early. These include mice with mutations in the genes for telomerase (65), Ku86 (66), p53 (67), XPD (68), lamin A (69), and mitochondrial DNA polymerase (35, 70). The most obvious common element among these mutants is that all of their enzymatic deficiencies have the potential to increase the vulnerability of their cells to apoptosis caused by double-strand (ds) breaks in DNA, stalled transcription or replication complexes, or dysfunctional mitochondria or nuclei (Fig. 1).

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Fig. 1. Short-lived mutant mice with possible relevance in aging-related research. The life span of these mutants varies from 20% to 80% of normal, depending on the gene mutated.

If in fact the cells in these mutants are subject to excessive apoptosis, how does this relate to the premature development of adverse aging phenotypes? One possibility is a lack of balance between cell loss and cell replacement, caused either by a declining ability to recruit cells from stem cell or progenitor cell niches or by dysfunction in the differentiation pathways. For example, Nishimura et al. (71) showed that graying of hair can be caused by "incomplete maintenance of melanocyte stem cells" and suggested that stem cell apoptosis and/or ectopic differentiation "may contribute to stem cell loss in other aging organ systems." Age-dependent depletion of stem cell pools could provide an explanation for the interval of time between birth and the onset of observable pathology, and the small body size and eventual growth failure of these mouse mutants and HGPS patients. Kujoth et al. (35) proposed that their "findings suggest that apoptosis and loss of irreplaceable cells may be an important mechanism of aging in mammals." Chien and Karsenty (72) have recently reviewed evidence about how "aging influences tissue-specific progenitors and differentiated cell lineages" and the role that these influences may play in the development of cardiovascular disease, muscle wasting, and osteoporosis. Thus, the idea that cell replacement plays a critical role in slowing aging is gaining some momentum.

The possibility that aging may be linked to an inability of stem cell niches to sustain the appropriate panoply of progenitor cells for cell replacement, independently led Jill Carrington to publish RFAs related to this question in 2001 ("Biology of adult stem cells in aging") and 2004 ("Biology of stem cells in aging"). The applications funded in response to these two RFAs added to the growing NIA portfolio of grants supporting research on stem cell biology, reaching a total commitment of $20 million by the end of fiscal year 2004. A PA titled "Testing stem cell therapy in mouse models of premature aging" to support research using short-lived mouse mutants to test potential cell-replacement therapies was developed by Felipe Sierra to provide "proof of principle" that such therapies could work in humans and was published in mid-2005.

Historically, the gold standard for identifying genes that regulate longevity has been to identify genes that can be manipulated to increase longevity, and many such genes have been discovered in fruit flies and nematodes, as discussed above. However, research with nematodes and fruit flies is not as likely to be informative about causes of age-related human pathology as that using mice would be; hence, mutant mice that age prematurely may in fact be useful in evaluating the relevance of these same genes in human aging (73). The relevance of mouse mutations that shorten life span remains controversial, because it is much easier to cause a mouse to die prematurely than to extend its life span (that is, mutations might shorten life span through mechanisms unrelated to life-span determination).

An alternative approach is to identify genes that can be manipulated to either delay or hasten the appearance of aging-related phenotypes such as osteoporosis, loss of muscle mass, loss of subcutaneous adipose tissue, cardiovascular disease, and loss or graying of hair. Genetically induced extension of longevity in animal models is often accompanied by a delay in the appearance of age-related phenotypes (74, 75), but the question remains whether the human homologs of such genes play any role in the development of these adverse phenotypes during human aging.

Summary and Conclusions

Although it is tempting to claim that progress in biogerontology during the past 20 years has been the direct result of a logical and linear research program developed with foresight and careful planning by NIA staff, this would be taking too much credit for what has actually been accomplished. Understanding the molecular mechanisms underlying cell senescence was a logical place to start in 1986, but progress was made as much because there was already a critical mass of investigators working in this area as it was because of NIA's efforts to stimulate research. Our interest in the mechanisms of cell death was a lucky guess that paid off when Robert Horvitz identified three genes in the nematode cell-death pathway. Belatedly, I realized that there must be alleles and combinations of alleles that promote longevity, but the identification of the genes involved required whole-genome sequence information that only became available about 10 years ago, and so on.

What NIA does provide is commitment of long-term support for research areas once they begin to develop, with the infusion of targeted funds when needed. The work of Harley et al. (9) identified telomere biology as a research area relevant to aging, but we discovered through a conference call among telomere biologists in the mid-1990s that a specific initiative was not needed, because most of the relevant investigators were already funded by NIA. Similarly, we discovered at a workshop organized by David Finkelstein that a PA or RFA on mitochondrial dysfunction was not needed to promote research in this area.

In contrast, an example where NIA has taken a definite leadership role is funding research on HGPS, even though there are still very few investigators working on this syndrome. Despite considerable skepticism within the biogerontology community about the relevance of HGPS to normal aging, an American Society of Cell Biology-sponsored workshop held in Ames, Iowa, in July 2005 provided substantial evidence that aberrant nuclear architecture can induce several aging-like phenotypes. Thus, nuclear architecture may well be a new frontier for research on aging, and laminopathies may have something to tell us about development of pathology during normal aging.

Thus, considerable progress has been made in elucidating genes and pathways involved in longevity regulation in yeast, fruit flies, nematodes, and mice. The roles of cell death, cell senescence, and oxidative stress in aging are less understood, but major clues are emerging. The development of stem cells for therapeutic use in dealing with the health problems of older people is a tantalizing possibility, but much remains to be done.

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Citation: H. R. Warner, Developing a Research Agenda in Biogerontology: Basic Mechanisms. Sci. Aging Knowl. Environ. 2005 (44), pe33 (2005).

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