generally provides a close approximation to maximum likelihood. In Does et al. (1988) the jackknife (see §10.7) is applied to reduce the bias in the maximum likelihood estimate: this issue is also addressed by other authors (see Mehrabi & Matthews, 1995, and references therein). How the dilutions used in the experiment are chosen is another topic that has received substantial attention. Fisher (1966, §68, although the remark is in much earlier editions) noted that the estimate of log u would be at its most precise when all observations are made at a dilution d  1Á59=u. Of course, this has limited value in itself because the purpose of the assay is to determine the value of u, which a priori is unknown. Nevertheless, several methods have been suggested that attempt to combine Fisher's observation with whatever prior knowledge the experimenter has about u. Fisher himself discussed geometric designs, i.e. those with d j  c jÀ1 d 1 , particularly those with c equal to 10 or a power of 2. Geometric designs have been the basis of many of the subsequent suggestions: see, for example, Abdelbasit and Plackett (1983) or Strijbosch et al. (1987). Mehrabi and Matthews (1998) use a Bayesian approach to the problem; they found optimal designs that did not use a geometric design but they also noted that there were some highly efficient geometric designs. Most of the literature on the design of limiting dilution assays has focused on obtaining designs that provide precise estimates of u or log u. Two aspects of this ought to be noted. First, the designs assume that the single-hit Poisson model is correct and some of the designs offer little opportunity to verify this from the collected data. Secondly, the experimenters are often more interested in mechanism than precision, i.e. they want to know that, for example, the single-hit Poisson model applies, with precise knowledge about the value of associated parameter being a secondary matter. Although the design literature contains some general contribution in this direction, there appears to be little specific to limiting dilution assays. Mutagenicity assays There is widespread interest in the potential that various chemicals have to cause harm to people and the environment. Indeed, the ability of a chemical or other agent to cause genetic mutationsÐfor example, by damaging an organism's DNAÐis often seen as important evidence of possible carcinogenicity. Conse- quently, many chemicals are subjected to mutagenicity assays to assess their propensity to cause this kind of damage. There are many assays in this field and most of these require careful statistical analysis. Here we give a brief description of the statistical issues surrounding the commonest assay, the Ames Salmonella microsome assay; more detailed discussion can be found in Kirkland (1989) and in Piegorsch (1998) and references therein. The Ames Salmonella microsome assay exposes the bacterium Salmonella typhimurium to varying doses of the chemical under test. This organism cannot 20.5 Some special assays 737 synthesize histidine, an amino acid that is needed for growth. However, muta- tions at certain locations of the bacterial genome reverse this inability, so, if the bacteria are grown on a Petri dish or plate containing only minimal histidine, then colonies will only grow from mutated cells. If there are more colonies on plates subjected to greater concentrations of the chemical, then this provides evidence that the mutation rate is dose-dependent. It is usual to have plates with zero dose of the test chemicalÐnegative controlsÐand five concentrations of the chemical. There may also be a positive controlÐa substance known to result in a high rate of mutationsÐalthough this is often ignored in the analysis. It is also usual to have two, three or even more replicates at each dose. The data that arise in these assays comprise the number of mutants in the jth replicate at the ith dose, Y ij , j  1, , r i , i  1, , D. A natural assumption is that these counts will follow a Poisson distribution. This is because: (i) there are large numbers of microbes placed on each plate and only a very small proportion will mutate; and (ii) the microbes mutate independently of one another. How- ever, it is also necessary for the environment to be similar between plates that are replicates of the same dose of test chemical and also between these plates the number of microbes should not vary. If the Poisson assumption is tenable, then the analysis usually proceeds by applying a test for trend across the increasing doses. In order to perform a test of the null hypothesis of no change of mutation rate with dose against an alter- native of the rate increasing with dose, it is necessary to associate an increasing score, x i , with each dose group (often x i will be the dose or log dose given to that group). The test statistic is Z P   D i1 x i r i Y i ÀY  p YS 2 x  , 20:27 where Y i   j Y ij =r i ,Y   i r i Y i =  i r i and S 2 x   i r i x i À  x 2 , with  x   i r i  x i =  i r i . Under the null hypothesis, (20.27) has approximately a stand- ard normal distribution. This straightforward analysis is usually satisfactory, provided the conditions outlined above to justify the assumption of a Poisson distribution hold and that the mutation rate does increase monotonically with dose. It is quite common for one of these not to hold, and in such cases alternative or amended analyses must be sought. The mutation rate is often found to drop at the highest doses. This can be due to various mechanismsÐe.g. at the highest doses toxic effects of the chemical under test may kill some microbes before they can mutate. Consequently a test based on Z P may be substantially less powerful than it would be in the presence of monotone dose response. A sophisticated approach to this problem is to 738 Laboratory assays attempt to model the processes that lead to this downturn; see, for example, Margolin et al. (1981) and Breslow (1984a). A simpler, but perhaps less satisfying approach is to identify the dose at which the downturn occurs and to test for a monotonic dose response across all lower doses; see, for example, Simpson and Margolin (1986). It is also quite common for the conditions relating to the assumptions of a Poisson distribution not to be met. This usually seems to arise because the variation between plates within a replicate exceeds what you would expect if the counts on the plates all came from the same Poisson distribution. A test of the hypothesis that all counts in the ith dose group come from the same Poisson distribution can be made by referring  r i j1 Y ij ÀY i  2 Y i to a x 2 distribution with r i À 1 degrees of freedom. A test across all dose groups can be made by adding these quantities from i  1toD and referring the sum to a x 2 distribution with  r i À D degrees of freedom. A plausible mechanism by which the assumptions for a Poisson distribution are violated is for the number of microbes put on each plate within a replicate to vary. Suppose that the mutation rate at the ith dose is l i and the number of microbes placed on the jth plate at this dose is N ij . If experimental technique is sufficiently rigorous, then it may be possible to claim that the count N ij is constant from plate to plate. If the environments of the plates are sufficien- tly similar for the same mutation rate to apply to all plates in the ith dose group, then it is likely that Y ij is Poisson, with mean l i N ij . However, it may be more realistic to assume that the N ij vary about their target value, and vari- ation in environments for the plates, perhaps small variations in incubation temperatures, leads to mutation rates that also vary slightly about their expected values. Conditional on these values, the counts from a plate will still be Poisson, but unconditionally the counts will exhibit extra-Poisson varia- tion. In this area of application, extra-Poisson variation is often encountered. It is then quite common to assume that the counts follow a negative binomial dis- tribution. If the mean of this distribution is m, then the variance is m  am 2 , for some non-negative constant a a  0 corresponds to Poisson variation). A crude justification for this, albeit based in part on mathematical tractability, is that the negative binomial distribution would be obtained if the l i N ij varied about their expected values according to a gamma distribution. If extra-Poisson variation is present, the denominator of the test statistic (20.27) will tend to be too small and the test will be too sensitive. An amended version is obtained by changing the denominator to  p Y1  ^aYS 2 x , with ^a an 20.5 Some special assays 739 estimate of a obtained from the data using a method of moments or maximum likelihood. 20.6 Tumour incidence studies In §20.5, reference was made to the use of mutagenicity assays as possible indicators of carcinogenicity. A more direct, although more time-consuming, approach to the detection and measurement of carcinogenicity is provided by tumour incidence experiments on animals. Here, doses of test substances are applied to animals (usually mice or rats), and the subsequent development of tumours is observed over an extended period, such as 2 years. In any one experiment, several doses of each test substance may be used, and the design may include an untreated control group and one or more groups treated with known carcinogens. The aim may be merely to screen for evidence of carcino- genicity (or, more properly, tumorigenicity), leading to further experimental work with the suspect substances; or, for substances already shown to be carci- nogenic, the aim may be to estimate `safe' doses at which the risk is negligible, by extrapolation downwards from the doses actually used. Ideally, the experimenter should record, for each animal, whether a tumour occurs and, if so, the time of occurrence, measured from birth or some suitable point, such as time of weaning. Usually, a particular site is in question, and only the first tumour to occur is recorded. Different substances may be compared on the `response' scale, by some type of measurement of the differences in the rate of tumour production; or, as in a standard biological assay, on the `dose' scale, by comparing dose levels of different substances that produce the same level of tumour production. The interpretation of tumour incidence experiments is complicated by a number of practical considerations. The most straightforward situation arises (i) when the tumour is detectable at a very early stage, either because it is easily visible, as with a skin tumour, or because it is highly lethal and can be detected at autopsy; and (ii) when the substance is not toxic for other reasons. In these circumstances, the tumorigenic response for any substance may be measured either by a simple `lifetime' count of the number of tumour-bearing animals observed during the experiment, or by recording the time to tumour appearance and performing a survival analysis. With the latter approach, deaths of animals due to other causes can be regarded as censored observations, and the curve for tumour-free survival estimated by life-table or parametric methods, as in Chap- ter 17. Logrank methods may be used to test for differences in tumour-free survival between different substances. The simple lifetime count may be misleading if substances differ in their non- tumour-related mortality. If, for instance, a carcinogenic substance is highly lethal, animals may die at an early stage before the tumours have had a chance 740 Laboratory assays to appear; the carcinogenicity will then be underestimated. One approach is to remove from the denominator animals dying at an early stage (say, before the first tumour has been detected in the whole experiment). Alternatively, in a life- table analysis these deaths can be regarded as withdrawals and the animals removed from the numbers at risk. A more serious complication arises when the tumours are not highly lethal. If they are completely non-lethal, and are not visible, they may be detected after the non-specific deaths of some animals and subsequent autopsy, but a complete count will require the sacrifice of animals either at the end of the experiment or by serial sacrifice of random samples at intermediate times. The latter plan will provide information on the time distribution of tumour incidence. The relevant measures are now the prevalences of tumours at the various times of sacrifice, and these can be compared by standard methods for categorical data (Chapter 15). In practice, tumours will usually have intermediate lethality, conforming neither to the life-table model suitable for tumours with rapid lethality nor to the prevalence model suitable for non-lethal tumours. If tumours are detected only after an animal's death and subsequent autopsy, and a life-table analysis is performed, bias may be caused by non-tumour-related mortality. Even if sub- stances under test have the same tumorigenicity, a substance causing high non- specific mortality will provide the opportunity for detection of tumours at autopsy at early stages of the experiment, and will thus wrongly appear to have a higher tumour incidence rate. To overcome this problem, Peto (1974) and Peto et al. (1980) have suggested that individual tumours could be classified as incidental (not affecting longevity and observed as a result of death from unrelated causes) or fatal (affecting mortality). Tumours discovered at intermediate sacrifice, for instance, are inci- dental. Separate analyses would then be based on prevalence of incidental tumours and incidence of fatal tumours, and the contrasts between treatment groups assessed by combining data from both analyses. This approach may be impracticable if pathologists are unable to make the dichotomous classification of tumours with confidence. Animal tumour incidence experiments have been a major instrument in the assessment of carcinogenicity for more than half a century. Recent research on methods of analysis has shown that care must be taken to use a method appro- priate to the circumstances of the particular experiment. In some instances it will not be possible to decide on the appropriate way of handling the difficulties outlined above, and a flexible approach needs to be adopted, perhaps with alternative analyses making different assumptions about the unknown factors. For more detailed discussion, see Peto et al. (1980) and Dinse (1998). 20.6 Tumour incidence studies 741 [...]... 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In order to perform a test of the null hypothesis of no change of mutation rate with dose against an alter- native of the rate increasing. and the curve for tumour-free survival estimated by life-table or parametric methods, as in Chap- ter 17. Logrank methods may be used to test for differences in tumour-free survival between different. 0Á1446 0Á1423 0Á1401 0Á1379 1 10 1357 0Á1335 0Á1314 0Á1292 0Á1271 0Á1251 0Á1230 0Á1 210 0Á1190 0Á1170 1Á20Á1151 0Á1131 0Á1112 0 109 3 0 107 5 0 105 6 0 103 8 0 102 0 0 100 3 0Á0985 1Á30Á0968 0Á0951 0Á0934