## Co

\$161,779

\$26,578

The values in Table 3.1 were calculated as follows: The cost of a 3-month-old mouse is estimated as \$7. The cost per month thereafter is calculated as \$7 times the number of mice alive at the start of the month. The colony size is 1000 mice initially. It is assumed that no mice die until age 12 months. Mortality rate doubling time is taken as 0.3 years. The risk of death in any given month (after age 12 months) is calculated as m(t) = 0.01 * exp(2.31 * t/12), where t = (number of months of age — 12). Cumulative cost is the sum of cost for all previous months. The cost per mouse is calculated as the cumulative cost divided by the number of live mice at the start of the interval. These calculations were performed for each month of a three-year period, but to save space Table 3.1 shows only the odd-numbered months. The table shows, for example, that the production cost of a 35-month-old mouse is approximately 100-fold higher than that of a 25-month-old mouse, which is itself about twice the cost of an 18-month-old mouse.

The values in Table 3.1 were calculated as follows: The cost of a 3-month-old mouse is estimated as \$7. The cost per month thereafter is calculated as \$7 times the number of mice alive at the start of the month. The colony size is 1000 mice initially. It is assumed that no mice die until age 12 months. Mortality rate doubling time is taken as 0.3 years. The risk of death in any given month (after age 12 months) is calculated as m(t) = 0.01 * exp(2.31 * t/12), where t = (number of months of age — 12). Cumulative cost is the sum of cost for all previous months. The cost per mouse is calculated as the cumulative cost divided by the number of live mice at the start of the interval. These calculations were performed for each month of a three-year period, but to save space Table 3.1 shows only the odd-numbered months. The table shows, for example, that the production cost of a 35-month-old mouse is approximately 100-fold higher than that of a 25-month-old mouse, which is itself about twice the cost of an 18-month-old mouse.

as possible consistent with the experimental question under consideration.

Lastly, very old populations are likely to be unrepresentative, in that individuals subject to early and midlife illnesses, for whatever known or unknown reasons, have already been removed by death. Studies of centenarians (or other cohorts of very long-lived people) often show clearly, for instance, that they resemble much younger populations in many physiological parameters (Franceschi et al., 1995; Perls et al., 2002); cross-sectional tables of such traits would show a retardation, or reversal, of age-specific trends as those with typical patterns of aging are eliminated by death, leaving only atypical survivors. Among men who are healthy at age 60, for example, only about 30% are expected to be alive and healthy at age 80, but those destined for good health at age 80 are typically healthier than average at the age of 60 years (Metter et al., 1992). Differences between 60- and 80-year-olds therefore confound effects of aging (and disease) with those of survivorship.

Thus studies that focus on very old rodents are not only far more expensive, they are on the whole less informative than those which use younger animals in the aged cohorts, because data on survivor animals, or sick ones, may give few insights into the life-long process of aging. In my own laboratory we prefer to evaluate animals at ages where 90% or more of the population is still alive, and we almost never make experimental use of mice older than the age of median survival.

Principle #2: Don't Use Mice that are too Young, Either

The goal of this precept is to avoid confusing developmental changes with the effects of aging. Although it takes a mere 8 weeks or so for mice to become reproductively competent, many physiological systems and body dimensions continue to change along developmental trajectories that can, in poorly designed studies, be confused with aging. Consider, for example, the trait shown in the top panel of Figure 3.1, which rises progressively until age 6 months and then remains stable thereafter.

A study which evaluated mice at ages 2 and 20 months would misleadingly conclude that the trait in question ''goes up with aging,'' although a more judicious interpretation, based on a wider range of ages, would conclude instead that the trait shows increases only in juveniles and young adults, with no effects of aging per se. A human or dog that has completed 25% of its lifespan is likely to be 20 or 3 years old, respectively, well within the ''mature young adult'' stage of life; a corresponding stage for mice would recommend animals of 6-7 months as the ''young'' control group of a descriptive study of age trajectory in a variable of interest. Beginners tend to prefer designs that use the youngest available animals, again from a mistaken desire to see maximally-sized effects, and because these are the least expensive and are usually available on short notice. Certainly information on maturational process has its own merits and may even be useful in understanding ways in which early life changes modulate the pace of aging or risks of late-life illnesses, but the use of very young mice under the mistaken impression that they are typical of young adult animals may lead to misleading impressions of the ways in which aging alters the outcomes of interest.

Principle #3: Don't Use too Few Age Groups

The common error here is to investigate whether a trait is age-sensitive by comparing its level in two groups, one allegedly young, the other supposedly old. The middle panel of Figure 3.1 shows another hypothetical data set, showing a trait that rises to a plateau in midlife and then declines thereafter. The bottom shows three possible misinterpretations of this data set, compiled by three laboratories, each of which has conducted assays at two

Figure 3.1. The top panel shows a hypothetical data set, as an illustration of errors that can occur when a survey of aging effects starts with mice that are too young to be considered fully mature; see text for interpretation. The middle panel shows a second hypothetical data set, as an illustration of the hazards of evaluating only two age groups. The bottom panels represent reports by three different laboratories of the data shown in the middle panel; each laboratory has selected different age groups. Laboratory A, for example, has reported data at 2 and 15 months of age, extracted from the complete data.

Figure 3.1. The top panel shows a hypothetical data set, as an illustration of errors that can occur when a survey of aging effects starts with mice that are too young to be considered fully mature; see text for interpretation. The middle panel shows a second hypothetical data set, as an illustration of the hazards of evaluating only two age groups. The bottom panels represent reports by three different laboratories of the data shown in the middle panel; each laboratory has selected different age groups. Laboratory A, for example, has reported data at 2 and 15 months of age, extracted from the complete data.

arbitrary ages. Laboratory A concludes that the trait increases with age; Laboratory B finds no age effect; and Laboratory C infers that the trait declines with age. None of these conclusions agrees with the other two, and none is very helpful. Two ages may be sufficient for traits that show a simple, monotonic change over the entire age range, but this default assumption fails too often for comfort and cannot itself be tested without evaluation of a wider range of subject ages. A study of cytokine production in responses to schistosomal egg antigens (Chiu et al., 2002), for example, found several examples of cytokines whose production increased between 6 and 18 months of age and then declined at later ages, helping to resolve conflicts among earlier papers that had disagreed on the extent, and even the direction, of age change in cytokine production based on less comprehensive data sets.

Principle #4: Use Mice that are Specific Pathogen Free and be able to Prove it

A specific pathogen-free (SPF) rodent colony contains mice or rats that are known not to be infected with any members of a specific, defined list of pathogenic microorganisms and parasites. The animals are not free of all bacterial and viral species, i.e., they are not gnotobiotic. Vendors of SPF rodents, and managers of SPF colonies, are able to define the pathogens for which their mice or rats have been tested, and can produce documentation of the diagnostic testing. Our own mouse colonies, for example, are tested routinely for serological evidence of infection by mouse hepatitis virus, mouse parvo-virus, minute virus of mice, ectromelia, Sendai, reovirus, lymphocytic choriomeningitis virus, and seven other viruses, and examined for pinworm by cecal inspection. Rat colonies are tested for exposure to each of 13 rat viruses. Testing for viral contamination typically involves looking for antibodies specific to viral antigens; such tests should be negative in rodents never exposed to the pathogen. Tests for pinworm involve direct examination of cecal samples for eggs. Most facilities use a sentinel system, in which the used bedding is pooled for a group of cages or racks, and then transferred to a fresh cage containing a group of mice from a strain known to be susceptible to the viruses of interest. After an interval of several weeks to allow the sentinels to become infected by the viruses or parasites—if these are present—and to form detectable antiviral antibodies, serum from the sentinels is checked for antiviral titers. This procedure is usually repeated 2-4 times per year for the most common viruses and at least annually for the others on the checklist.

Colonies that do not maintain mice under SPF conditions are referred to as ''conventional'' vivaria; these were in the clear majority until the 1980s, but are now fortunately becoming rare among top-level universities and medical centers. Conventional colonies may or may not have any particular virus or parasite present at any given time; the presence and prevalence of infection may fluctuate from year to year or month to month, and be reluctantly accepted as one source of undocumented ''technical'' variation in experimental outcomes.

Maintenance of an SPF colony depends upon strict adherence to well-known, but often violated, safety precautions. The rules seem simple: purchase mice only from a small, predefined list of vendors whose health reports document the SPF status of their colony; do not permit mice removed to a non-SPF colony or laboratory to be returned to the vivarium; be compulsive about use of head and shoe covers and protective gowns for each entry into the colony, and compulsive about the use of filter tops for each mouse cage; restrict access to the housing rooms to those whose duties require them to be there; never allow people or cages or equipment to go from a dirty (conventional) colony to an SPF colony. But the hazards are many. They include the peer review committee whose members wish to see the animal housing area (including one visitor whose own lab is a hotbed of pinworm contamination). They include the new faculty member whose laboratory work requires importation of several knock-out stocks whose construction was the key outcome of her postdoctoral work at her previous laboratory. They include the technician who keeps pet mice at home, or the student who stopped by the conventional colony to drop off some syringes on the way to the SPF part of the facility. Use of cage-washing facilities that service clean and unclean housing areas, or transport of water bottles or cage cards from one area to another are also common, but risky, practices. Hazards of this kind are compounded when animal rooms must be shared by multiple investigators; a slip by any one laboratory can lead to spread of infectious agents to rodents used by many colleagues. The introduction of pinworm eggs or a single virus-infected mouse can place an entire colony at risk, and in some cases eradication of the infection can require removal and elimination of all mice in the colony or a major section of it, a step that is always expensive and often impractical.

Why, then, go to all this fuss? The central basis for the emphasis on SPF rodent colonies, in aging research as in many other areas of science, is the need to be able to reproduce experimental findings at later times and in other places. Viral and parasitic infections have known effects on multiple biochemical and physiological outcomes, and are certain to have undocumented effects on many traits not formally studied in this context. Conventional colonies may well have infectious burdens that influence the outcome of a study of age effects or antiaging interventions, and the level and kind of infection may well fluctuate during the course of a single study with consequences that are unforeseen, unpredictable, irreproducible, and undocumented. The traits affected are not always those, like immune responses, most obviously linked to infectious status. Age-related changes in rat skeletal muscle fiber distribution, for example, have been shown to differ systematically between conventional and specific pathogen-free colonies (Florini, 1989).

A common scenario involves the importation of SPF rodents into a conventional colony, in the mistaken hopes that the experimental subjects can then be considered as

''almost SPF.'' Such a situation can, unfortunately, lead to infection of the newcomers by whatever local agents are then current in the host colony, so that the experimental assessments are conducted on mice at varying stages of an acute infectious process.

Advocates, or apologists, for the use of conventional vivaria sometimes raise the issue that SPF colonies are artificial, and thus fail to mimic the constant exposure to infectious agents that accompanies, and may mold, the aging process in real life. It is fair to acknowledge the potential importance of infectious agents in aging outside the vivarium, and important to encourage analyses of how aging might alter, and be altered by, specific defined pathogens. The point of SPF protocols, however, is not to duplicate some ''natural'' condition, but to define a set of environmental conditions well enough to permit replication and extension of the study's results.

Principle #5: Consider the Use of Non-isogenic Stocks

The large majority of work done with aging mice and rats makes use of inbred stocks, such as the C57BL/6J line of inbred mice, and the F344 stock of inbred rats. These inbred stocks of rats and mice were originally developed by geneticists who wish to have available groups of animals whose genetic characteristics did not change over time and which were uniform from laboratory to laboratory. They were invaluable for working out the basic rules of transplantation biology and played a major role in the development of experimental tumor immunology. Nowadays, many studies of aging rodents start with the assumption that inbred mice or rats should be used, in part because these animals are easy to obtain, and because the published literature contains a great deal of background information about their characteristics. In part, the preference for the use of inbred mouse in rat stocks is based upon a mixture of tradition and inertia, the tendency to use the same animal types that were used for previous studies in one's own lab and in the laboratory of one's mentor, and one's mentor's mentor.

In many ways, this unthinking attachment to the same old stocks is unfortunate, because the use of inbred rodents has several disadvantages. The first disadvantage is that each inbred line contains only animals of a single genotype. For this reason, it is not possible to tell, without further experimentation, whether the observations about the effects of aging on any specific trait of interest in a given inbred stock will or will not prove to be reproducible when analogous experiments are carried out on any other given inbred stock. Many traits, of course, are strongly influenced by genetic alleles that are polymorphic among the wide range of inbred mouse and rat stocks, and it is for this reason that each stock will have its own particular idiosyncratic properties, including disease susceptibilities and rates of change in age-dependent traits. Experimental studies of aging are often sufficiently expensive and tedious that most researchers are reluctant to duplicate or triplicate their workload by conducting the same study several times, ''merely'' to see if they get similar results in a second or third kind of mouse. For this reason, it would seem advisable for the aging research community to develop and to make use of genetically heterogeneous mouse and rat stocks for routine investigation.

A second problem with the routine use of inbred lines is that these mice are not only genetically uniform, but they are also homozygous at every locus. The development of inbred lines from the starting population of genetically heterogeneous mice is, in a sense, an exercise in genetic compromise. Each person or mouse among us carries in our genomes a ''genetic load,'' a set of genetic alleles each one of which, if homozygous, might lead to early life mortality or to sterility; we are spared these consequences because each of these alleles is rare enough to be heterozygous in most individuals who carry the allele at all. Developing an inbred population, however, requires forcing each locus to the homozygous state. Most homozygous genomes, therefore, produce individuals who die at an early age, are sterile, or show other traits that are rare within the genetically heterogeneous population from which the inbreeding was begun. Genetic combinations that lead to early death or sterility are eliminated during the development of inbred lines, and in fact producing a new inbred line often requires starting many such lines knowing that most will die out during the inbreeding process. Those lines of mice that emerge from this highly selective process contain animals that are able to survive to adulthood and produce live progeny, but may differ in many other ways from the starting population. In particular, inbred lines are almost invariably shorter-lived than mice produced by crosses between any two given inbred stocks (Smith et al., 1967). This lack of robustness and vigor characteristic of inbred rodents, together with strain-specific idiosyncrasies, both well-known and hitherto undocumented, should render the stocks a questionable choice for routine work in biological gerontology.

There are a variety of other options, some attractive and others less so. A cross between two inbred stocks produces an F1 hybrid stock, which like its inbred parents is isogenic—all the mice are genetically identical—but unlike them is heterozygous at multiple loci, i.e., those loci where the two parents differ. F1 hybrid mice are more robust, i.e., longer-lived, than their inbred progenitors, but are vulnerable to the same objection of strain-specific idiosyncrasies that make it hazardous to generalize from data based on a single genotype.

The search for a source of genetic heterogeneity might prompt some researchers to purchase outbred rodents from commercial suppliers. Commercial vendors often sell mice and rats that are marketed as ''outbred,'' but that in some cases could more justly be characterized as approximately inbred stocks. In at least two cases, detailed by Miller et al. (1999), the vendor's own catalogue copy states that the ''outbred'' stock originated in a single pair of inbred progenitors. Production of outbred stocks from a single homozygous genotype can only be recommended by someone unaware that the loss of genetic heterogeneity, like the loss of virginity, is not easily reversible by continued reproductive efforts. Leaving aside clear errors of this kind, genetic heterogeneity can be irretrievably lost, inadvertently, if the breeding nucleus is reduced to a single pair or a small number of pairs at any point in the long history of the stock. This seems to be a frequent occurrence: DNA fingerprint analyses of six allegedly outbred rat stocks (Festing, 1995) supports the idea that these stocks contain only limited genetic heterogeneity: within each stock 84-95% of the animals shared any one individual DNA marker, as contrasted to 34% sharing for rats chosen from different inbred strains.

To help mitigate the disadvantages of relying on isogenic stocks for research on aging, a committee chartered by the U.S. National Academy of Science recommended, in 1981, that researchers make greater use of populations that exhibit controlled genetic heterogeneity, and in particular recommended use of four-way cross populations in aging research (Committee on Animal Models for Research on Aging, 1981). Such a population is produced by a cross between males and females of two different F1 hybrid stocks, for example using (BALB/c x C57BL/6)F1 females bred to (C3H x DBA/2)F1 males. Because each of the F1 parents is heterozygous at many loci, each of their offspring will receive different alleles, at multiple loci, from each parent. From the perspective of the nuclear (i.e., nonmitochon-drial) genome, each individual in the four-way cross population is a full sib of each other individual; each is genetically unique, but shares 50% of its alleles with any other mouse in the test population. Populations of this kind have genetic heterogeneity, but of a controlled sort, because additional populations with similar genetic structure can be produced at any time, at any place, and in any numbers, as long as the four grandparental inbred stocks are available. Production of such a colony requires no special expertise in genotyping or husbandry, and is rapid, because the F1 hybrids are commercially available and because breeding success and fecundity are typically high. Four-way cross stocks should be strongly considered for descriptive studies, in which the goal is to discover how a trait changes with age, for intervention studies, and for correlational studies, and they are particularly attractive when evaluation of the genetic control of the age-related phenomenon is potentially of interest. The virtues of these stocks have led to their selection by the National Institute on Aging for a multi-center mouse intervention project (Warner and Nadon, 2005), and one such stock has been selected for inclusion among stocks available, at multiple ages, from the NIA's aging rodent colonies (Nadon, 2005). There is now extensive information on late-life pathology of the population produced by the cross between (BALB/c x C57BL/6)F1 females bred to (C3H x DBA/2)F1 males (Lipman et al., 2004).

Principle #6: Necropsy Data Provides Important Covariates

At a minimum, each researcher should conduct a careful gross inspection of each middle-aged or old mouse used in his/her study. This should include a notation of the presence or absence of masses in the skin, mammary glands, lungs, and abdominal organs, and a check for size of thymus, lymph nodes, and spleen suggestive of hematopoietic malignancy. Signs of bite wounds or scars on the skin should raise a suspicion of chronic or acute infection. Claims in the materials and methods section that the mice used were ''apparently healthy'' carry little conviction without a gross inspection of this kind, at a minimum. The best idea is to discard all data from mice with any lesions noted, although this advice becomes very expensive to follow, particularly if the mice are older than recommended by Principle #1 above. This recommendation is just as important for protocols in which animals are tested while alive—tests of antibody production or cognitive powers, for example; here, even though it is not necessary to euthanize the mouse to obtain the experimental data of interest, euthanasia as soon as possible after completion of the evaluation should be carried out to identify those mice in which a disease process may have influenced the outcome of the test.

Even better, of course, is to have the animal examined by a professional veterinary pathologist, or by a laboratory technician, with specialized training, working as part of the pathology team. This step will add a cost of approximately \$10 for each mouse examined. Reports are usually returned from the pathology office within a few weeks, making it possible for researchers to go back and eliminate, retroactively, those animals found to have been diseased. A complete histopathological necropsy can cost between \$25 and \$100 per case, and should be strongly considered when the objectives of the study include characterization of a new mutant, drug, or experimental system.

Principle #7: Pooling Across Individuals is Hazardous

Because the proportion of individuals with an illness serious enough to affect the outcome of an experimental test increases dramatically with age, the use of pooled samples from multiple individuals should be avoided whenever possible. In a study of antibody production, for example, sensible experimental designs would exclude those with hematopoietic malignancy. If the proportion of mice with lymphoma is as low as 20%, the chance that a pool of five mice will consist only of lymphoma-free mice is only 33%, and pools of samples from 10 mice are 89% likely to contain at least one diseased mouse. In other circumstances, the investigator may be unaware of the ways in which her test outcome might be influenced by specific forms of illness.

For many traits variability may increase in older subjects, and the routine use of pooled samples obscures this variability, and may prevent an appreciation of its effects on the biological question of interest. If, for example, a measure of muscle fatigue differs in important ways in subjects that do or do not have compromised pulmonary function, a study of individuals might reveal a bimodal distribution, with a fatigable subgroup— consisting of those with pulmonary adenomas—at one mode. Even without necropsy information, analysis of unpooled subjects would reveal a bimodal or strongly skewed distribution on the muscle outcome, raising issues about population heterogeneity that require careful follow-up work. Combining subjects into pools, each of which has some compromised individuals, would obscure this relationship, and provide a misleading impression of age effects on muscle function.

In some cases pooling may be required, particularly when the assay method is too insensitive to provide a reliable measure using the amount of material available from an individual donor. In such cases it will be necessary to test multiple pools of individuals from each age or treatment group of interest in order to perform a statistical analysis of the hypothesis. The power of the statistical test, of course, depends on the number of individually tested subjects, or the number of different pools, for which results are available. Thus combining a group of 12 subjects into 4 pools (of 3 subjects each) is certain to diminish statistical power, and the individual protocol will need to balance the practicality, and cost, of testing individual subjects against the loss of power that results from pooling.

Principle #8: Cost-adjusted Power Analyses can Reduce Overall Expense

Most experimenters are familiar with the uses of statistical power analysis, in which the goal is typically to determine the number of subjects that will need to be examined in order to have a good chance of refuting a null hypothesis of interest. Such an analysis can tell us, for example, that if the mean value of some substance (''Vitamin X'') in controls is 1200 ± 200 units, and we wish to see if the experimental group will differ from the control level by 200 units, we will need to use 17 control and 17 treated mice to have an 80% chance (''80% power'') of documenting the difference at a level of p < 0.05. The number of mice needed will go up if the change induced by the experimental treatment is smaller; or if the standard deviation is larger; or if the significance criterion is made more stringent (e.g., p < 0.01); or if we wish to increase our chance of proving the matter from 80% to 90%; or if we plan to test more than two groups; or if we plan to test several hypotheses using the same set of mice. Power analyses are, appropriately, considered a critical element in designing experiments and seeking financial support for them; it may be hard to drum up support for a research protocol that has only a 10% chance of detecting an effect sufficiently large to be worth reporting. An experiment designed to see if mean lifespan is increased 10% by a specific diet, for example, may require 60 control and 60 treated mice to achieve 80% power; an experiment with only 20 mice per group might be judged not worth the effort.

This synopsis above has a hidden assumption, the assumption that the number of animals in the two comparison groups should be the same. The design is ''balanced,'' in the sense that each group has the same size, and such balanced designs minimize the total number of animals tested. This makes good sense when the cost of each test is the same, but in a typical aging experiment the cost of obtaining and testing an elderly mouse may be a good deal higher than the cost for a young control. As shown in Table 3.1, for example, the production cost of a 25-month-old mouse, under plausible assumptions, may be 10-fold the cost of a 5-month-old mouse. Unbalanced designs, in which groups are permitted to have different numbers of subjects, can minimize the cost of the experimental protocol by using more mice of the less expensive variety. The procedure for conducting a ''cost-adjusted'' power analysis has two steps. First, you conduct a standard power analysis, along the lines shown above for ''Vitamin X,'' to estimate the number needed to produce acceptable power using a balanced design. In the example, the balanced design would require Ne = 17 mice per group. Then one calculates NY and NO, the numbers of young and old mice needed, using the following formula (developed by Dr. Andrzej Galecki of the University of Michigan's Geriatrics Center):

where CY and CO are respectively the cost of each experimental datum for young and old mice.

Consider a specific example, an experiment comparing 5-month-old to 25-month-old mice, for Vitamin X, with mean and standard deviation as given above, so that an experiment using 17 mice/group provides 80% power. In this example, a 5-month-old mouse costs \$21 and a 25-month-old mouse costs \$251 (from Table 3.1). Assuming the test kit and the technical labor add \$10 per sample, the cost for each data point is \$31 for young mice and \$261 for old mice. The formula above suggests that the optimal distribution of resources would involve testing 33 young mice and 11 of the more expensive, old mice. The cost of this experimental series would be \$4011, a savings of

\$953 over the ''balanced'' design that uses 17 mice of each age. If half of the mice at age 25 months are found to have a tumor or some other illness that requires their exclusion from the test population, then the cost per tested, healthy aged mouse goes to \$512, the optimal distribution changes to 43 young and 11 (tumor-free) old mice, and the savings to \$2500 compared to the balanced design.

Principle #9: Prefer Protocols that Compare Young Adults Destined to Age at Different Rates

The large majority of experiments on rodent aging use an old-fashioned design, in which some trait is measured in rodents of two or more ages, to produce a description of what aging does. It is for this reason that the National Institute on Aging has committed itself to providing aged rodents of multiple ages, and for this reason that most of this chapter has implicitly focused on designs that involve comparisons among age groups. From a different perspective, though, the main goal of biological gerontology should not be to develop an exhaustive catalog of what aging does, at ever-deeper levels of molecular and cellular sophistication, but instead to develop a good idea of how aging works to produce aged individuals from young ones. Descriptions of how aged individuals differ from young ones are only a first, exploratory step in producing and testing hypotheses about aging mechanisms. An alternate design, already in fashion for studies of invertebrate aging, involves comparisons of young or middle-aged subjects that are known to be aging at different rates. There are now at least two diets that slow aging in both rats and mice, one based on caloric restriction (Weindruch and Sohal, 1997) and the other based on restriction of the amino acid methionine (Miller et al., 2005; Orentreich et al., 1993). There are at least eight published mutations that extend lifespan in mice (Bartke et al., 2001; Bluher et al., 2003; Holzenberger et al., 2003; Miller, 2001; Miskin and Masos, 1997; Tatar et al., 2003). Here the increases in maximal lifespan provide presumptive evidence that the aging process has been delayed or decelerated, and in some cases additional work has documented delays in aging effects on collagen cross-linking, immune changes, joint pathology, cataracts, kidney damage, cognitive decline, and tumor rates (Flurkey et al., 2001; Ikeno et al., 2003; Kinney et al., 2001; Silberberg, 1972; Vergara et al., 2004), thus building a strong case for broad effects on aging rate in these mutants. There is also good evidence that mouse stocks recently derived from wild-trapped progenitors retain genetic alleles, lost by inbred mouse stocks, that are responsible for increases in mean and maximal lifespan (Klebanov et al., 2001; Miller et al., 2002).

The availability of multiple varieties of slow-aging mice allows investigators to look at factors that act, throughout early adult life, to determine the rate at which age changes occur. It is misleading to assume that aging occurs mainly in old age, i.e., at ages at which the signs of aging first become apparent and inconvenient. Because causes precede effects, the processes that begin to induce clear signs of aging in 18-month-old mice (and 50-year-old people) must have been at work at earlier ages. Thus the mechanisms by which calorie-restricted diets or genetic variations and mutations retard the development of aging effects must also be in action during the months prior to the onset of geriatric symptoms. Research designs that compare pairs of strains, similar to one another except for an age-retarding mutation or exposure to an antiaging intervention, are thus powerful tools for seeking, and then testing, ideas about the ways in which the aging process is itself differentially timed. From this perspective, for example, a gene expression survey which focused on comparisons of control, food-restricted, and slow-aging dwarf mutants at early or middle adult ages is expected to be more fruitful than one which instead compiled lists of genes whose expression is age sensitive. Comparisons among differentially aging mice at relatively early ages also have the benefits of being faster, less expensive, and less confounded by disease and survivor effects than experiments which require data from aged organisms.

Principle #10: Avoid using Laboratory Rodents for Studies of Aging

Or, to be more diplomatic about it, avoid using only laboratory rodents for studies of aging. This principle has two subcomponents: (a) an argument that laboratory-adopted rodent stocks are a particularly poor choice on which to develop general ideas about aging, and (b) the more important point that important insights into mammalian aging are likely to require data on species that age at different rates.

Theoretical biologists have postulated, and experimentalists have confirmed, that genes whose natural selection depends on their beneficial effects on early life survival and fitness may have ill effects in old age. Studies have shown repeatedly that selection for genes that influence early-life maturation and reproductive performance (Luckinbill et al., 1984; Rose and Charlesworth, 1980) or growth rate (Miller et al., 2000) can have major effects on aging rate and longevity. Similar conclusions emerge from analysis of the actions of evolution in field studies (Austad, 1993) and in domesticated dogs (Li et al., 1996; Miller and Austad, 2005; Patronek et al., 1997). The evolutionary history of the inbred mouse and rat stocks typically used in experimental biology, including bio-gerontology, features over a hundred generations of selection for rapid early life growth, large body size (an indirect result of selection for large litter size), independence from reproductive linkage to day length, promiscuity in mate selection, tameness, slow speed, and a preference to go into cages rather than out of them. These selection pressures were not the result of deliberate experimental decisions, but represent adaptation of the genome to optimal fitness in the laboratory environment and to laboratory breeding schemes. On theoretical grounds, intensive selection for rapid early growth and early maturation might be expected to eliminate polymorphic alleles that delay aging. In confirmation, two analyses of populations of mice recently derived from wild-trapped progenitors have shown increases in mean and maximal longevity compared to inbred strains and to genetically heterogeneous mouse stocks produced by crosses among laboratory-adapted inbred stocks (Miller et al., 2002). Unpublished data (Harper, Austad, and Miller et al.) have replicated these findings and shown further that hybrids produced by crosses between wild-derived and laboratory-adapted stocks have intermediate lifespans.

The laboratory mouse is a highly artificial construct, related to real mice in much the same way as a poodle is related to a wolf. Most pertinent for biogerontology, it is a short-lived construct, from which at least some significant antiaging genes have been stripped. Studies of the biology of aging in laboratory-adapted mice thus face some of the same critiques, detailed elsewhere (Miller, 2004a b), to which analyses of mouse models of so-called accelerated aging can be subjected.