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Microarray Data Analysis

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Statistical Tests

Statistical Tests

The Purposes of Statistical Tests
Microarray studies often aim to identify genes that are differentially regulated across different classes of samples; examples are: finding the genes affected by a treatment, or finding marker genes that discriminate diseased from healthy subjects. Statistical tests, rather than cluster analysis, are the right tool for this purpose. Statisticians have developed many new procedures that seem more useful than conventional tests for microarray data. Some studies also aim to identify groups of genes that act together, or to uncover molecular similarities among subsets of samples. The section on Exploratory Analysis describes appropriate techniques for these studies. Some investigators confirm results found by exploratory analysis by using formal statistical methods, or do cluster analysis on differentially expressed genes. Such procedure can be circular in logic; better procedure is to identify differences between groups defined on biological grounds.
Microarray data is often used as a guide to further, more precise studies of gene expression by qt-PCR or other methods. Then the goal of the statistical analysis is heuristic: to provide the experimenter with an ordered list of good candidate genes to follow up. Sometimes the experimenter plans to publish microarray results as evidence for changes in gene abundance; in this case it is important to state the correct degree of evidence: the ‘p-value’. Many microarray papers still present p-values, as if each gene had been tested in isolation, even though many genes were actually tested in parallel; these p-values are wrong in the context of testing thousands of genes. Perhaps a better way to specify the confidence of microarray results is the ‘false discovery rate’.
 
Transforms
Often the first step is transforming the values to log scale, and doing all subsequent steps on the log-transformed values. Although taking logarithms is common practice, and helpful in several ways, there are other options. The main justification for transforms in statistics is to better detect differences between groups whose within-group variances are very different. Most commonly the within-group variances are higher in those groups where the mean is also higher. A different kind of variation, the measurement error in expression level estimates, grows with the mean level. If the measurement error is proportional to the mean, then the log-transformed values will have consistent variance for all genes. For both reasons many researchers argue that gene expression measures should be analyzed on a logarithmic scale.
However the gene abundances on the log scale usually show greater variation near the bottom end, giving rise to the characteristic ‘funnel’ shape of many microarray plots. The log transform is too ‘strong’, and partly reverses the inequality of measurement variances. A weaker transform, such as a cube root, would bring the variances closer to equal. Some researchers have devised ‘variance-stabilizing’ transformations, which attempt to equalize measurement errors for all genes.
However we are not in principle comparing different genes, but rather the same genes across different groups, and in most experiments, few genes change more than three-fold in mean levels. For studies where gene levels are fairly constant, and changes are expected to be modest, such as neuroscience studies, there is no need to transform data. For studies of cancerous tissue, where often some genes are elevated ten-fold or more, and these increases are highly variable between individuals, the log transform is very useful. For studies with at most moderate fold changes – such as most experimental treatments on healthy animals – it would be better to use a weaker transform, such as a cube-root transform or a ‘variance-stabilizing’ transform’. However most people find these less common transforms confusing; then as a practical alternative, it is worth doing the analysis in parallel in both log and true scale, and discarding genes whose significance disappears entirely under one or the other. However there are other reasons to equalize variances for all genes; roughly equal variances are necessary for SAM and for the empirical Bayes methods described below.
These issues are discussed more fully in the section on Transforms in Distributions of Microarray Intensities.
 

Comparison of Two Groups of Samples

The simplest and most common experimental set-up is to compare two groups: for example, Treatment vs. Control, or Mutant vs. Wild type. The issues arising in simple comparisons arise also in more complex settings; it is easier to explain these in the simpler context.
The long-time standard test statistic for comparing two groups is the t-statistic:
t = (xi,1 – xi,2) / si,
where xi,1 is the mean value of gene i in group 1, xi,2 is the mean in group 2, and si is the (non-pooled) within-groups standard error (SE) for gene i.
Usually the majority of genes are not consistently changed between groups. For the unchanged genes, the values of their t-statistic would follow the t-distribution indexed by n1+n2 – 2 degrees of freedom, in repeated trials, provided there are no outliers in the samples. As a matter of practice, in almost all cases, the values of the t-statistics for all of the unchanged genes in a single experiment also follow a t-distribution. If the researcher expects only a small number of genes are greatly changed, then a convenient way of assessing the most likely true positives is to plot the t-scores obtained, against the t-distribution. Usually the t-scores of the unchanged genes follow the t-distribution; if the unchanged genes are the overwhelming majority, then this plot will be a straight line at 45o. The t-scores for the few really significant genes are more extreme, and stand out from the straight line, where they can be easily seen. A small R program that does this is here.
 
A quantile plot
Figure 2. A quantile plot
A drawback of the t-statistic for microarray datasets is that most experiments have only a few samples in each group (n1 and n2 are small), and so the standard error si is not very reliable. In a modest fraction of cases, si is (by normal sampling variation) greatly under-estimated, and genes that are little changed give rise to extreme t-values, and therefore false positives. The theory compensate for some of these false positives, in that the tails of the t-distribution are much further out than those of a Normal curve. This causes a reverse problem: a truly changed gene has to change a great deal to give convincing evidence; therefore many of the moderately changed genes won’t show convincing evidence of change.
Tusher and Tibshirani suggested (a form of) the following test statistic t* rather than the usual t statistic[1]. The SE in the denominator is adjusted toward a common value for all genes; this prevents gross underestimation of SE’s, and so eliminates from the gene list those genes that change only a little:
t* = (xi,1 – xi,2) / ((si + s0)/2)
where s0 is the median of the distribution of standard errors for all genes. The range of values of the revised denominator is narrower than the range of sample SEs; it is as if all the SE’s are ‘shrunk’ toward the common value s0. Unfortunately no theoretical distribution is known for this statistic t*, and hence the significance levels of this statistic must be computed by a permutation method (see below). A similar statistic also crops up in empirical Bayes analysis (see below).
Another approach to detecting more of the differentially expressed genes is to use a more precise estimate of the variation between individuals, for each gene, in tests of that gene. If a good deal of prior data exist on the tissue and strain used in the wild-type (or control) group, measured on the same microarray platform – and this is sometimes the case now – then it is defensible to pool the estimates of wild-type variation from each of the prior studies, and use this as the denominator in the t-scores. The t-scores should then be compared to the t-distribution on a number of degrees of freedom, equal to that used in computing the pooled standard error. A variant of this approach may be used in a study where many groups are compared in parallel. The within-group variances for each gene may be pooled across the different groups to obtain a more accurate estimate of variation. This presumes that treatments applied to different groups affect mostly the mean expression levels, and not the variation among individuals. Of course one should test that the discrepancies in variance estimates are not too large for many of the genes that are selected as differentially expressed. This may be done by computing the ratios of variances between groups (F-ratios), and comparing to an F-distribution.
Since gene expression values are not distributed according to a Normal curve, some researchers have used non-parametric tests. The most commonly used test of this type is the Wilcoxon signed-rank test. Unfortunately this is not really a good choice, because the Wilcoxon test assumes that the distribution of the gene expression values, although not Normal, is strictly symmetric; the p-values from this test are inaccurate, if this assumption is badly wrong; and in practice the distribution of values of a single gene is frequently quite asymmetric. A thoroughly robust non-parametric test is the rank, or binomial test, which counts the number of values in each group greater than the median value, and compares this number to the binomial distribution. This test has very little power to detect differences in small groups, which are typical of microarray studies, and is never used in practice to detect differential expression.
Gene expression values don’t follow a normal curve, but the p-values from a standard t-test aren’t far away from truth when the distribution is moderately asymmetric. However the t-test does fall down badly when there are outliers (values more than twice as far from the mean as all the others). For this reason, when doing a t-test, it is wise to confirm that neither group contains outliers. In practice, it often happens that genes detected as different between groups, are actually expressed very highly in only one individual of the higher group. Some methods for doing this pre-analysis are discussed in the Exploratory Analysis section. Probably the best way to avoid the problem with outliers is to use robust estimates of mean (trimmed mean) and variability (mean absolute deviation). However no theoretical distribution is known for these; and their significance levels (p-values) would have to be computed by permutations.
 
Permutation Tests
Permutation testing is an approach that is widely applicable and copes with distributions that are far from Normal; this approach is particularly useful for microarray studies because it can be easily adapted to estimate significance levels for many genes in parallel. The major drawback for experimentalists is that these tests usually require some programming. Some recent software packages, notably SAM, implement permutation testing in a menu-driven interface.
The meaning of a p-value from a permutation procedure differs from the meaning of a model-based p-value. The model-based p-value is the probability of the test statistic, assuming that the gene levels in both the treatment and control groups follow the model (eg. a Normal distribution). A permutation-based p-value tells how rare that test statistic is, among all the random partitions of the actual samples into pseudo-treatment and pseudo-control groups. The steps in a permutation-based computation of the significance level of a test statistic are as follows:
  • Choose a test statistic, eg. a t-score for a comparison of two groups,
  • Compute the test statistic for the gene of interest,
  • Permute the labels on samples at random, and re-compute the test statistic for the rearranged labels; repeat for a large number (perhaps 1,000) permutations, and finally,
  • Compute the fraction of cases in which the test statistics from iii) exceed the real test statistic from ii).
The p-value for the gene is the fraction of cases in which the randomly permuted samples give a test statistic for that gene, at least as extreme as the one that occurs in the properly labelled samples. The idea is that if the gene is distributed similarly in both treatment and control groups, then the difference statistic (a t-statistic or any other) will appear about as big in the permuted arrangement, as in the true arrangement. If the gene levels in the treatment group are higher than any levels in the control group, then no value of the permuted statistic will be as great as the true value.
A permutation test needs at least two groups of six samples, in order to have enough different permutations. For two groups of six, there are C(12,6) = 924 permutations that give different groups; although half of these permutations are mirror images of the other half, so the true number of distinct pseudo-scores is 462. Some statisticians use balanced permutations: where each pseudo-group has roughly equal representation from both the true treatment and the true control group. The true test statistics typically stand out better from this group of permutations, giving more extreme p-values, but at the cost of requiring larger numbers of samples; for example for two groups of six there are only C(6,3)2 /2 = 200 distinct balanced pseudo-groupings.
 
Volcano Plot
However one chooses to compute the significance values (p-values) of the genes, it is interesting to compare the size of the fold change to the statistical significance level. The ‘volcano plot’ arrange genes along dimensions of biological and statistical significance. The first (horizontal) dimension is the fold change between the two groups (on a log scale, so that up and down regulation appear symmetric), and the second (vertical) axis represents the p-value for a t-test of differences between samples (most conveniently on a negative log scale – so smaller p-values appear higher up). The first axis indicates biological impact of the change; the second indicates the statistical evidence, or reliability of the change. The researcher can then make judgements about the most promising candidates for follow-up studies, by trading off both these criteria by eye. With a good interactive program, it is possible to attach names to genes that appear promising.
 
a volcano plot
Figure 1. A volcano plot

Genome-Wide Comparisons, Corrected P-Values, and False Discovery Rates

P-Values and False Discovery Rates
Most scientific papers quote p-values, however few papers discuss their meaning. In order to understand what the problem is with quoting p-values for massively parallel comparisons, we need to be precise. Let’s consider, for example, a t-test of differences between two samples. If there is no systematic (real, reproducible) difference between groups, nevertheless the t-score for differences between groups is never exactly 0. Common sense cannot decide whether a particular value provides strong evidence for a real difference. The natural question to ask is: how often a random sampling of a single group would produce a t value as far from 0 as the t we observed. When you declare an effect is significant at 5%, you say you are willing to let one false positive sneak in, roughly every twenty tests. We don’t accept this for critical decisions; we won’t long continue to cross the street, if we do so on a 95% confidence that there is a break in traffic. We may call this the false positive rate (FPR); the FPR of a procedure is the fraction of truly unchanged genes which appear as (false) positives.
If the aim of the microarray study is to select a few genes for more precise study, then the goal is an ordered list of genes, most of which are really different (true positives). Another way to say this is that the expected number of false positives is some reasonable fraction (for example less than .3) of the genes selected. This goal leads naturally to specifying the false discovery rate (FDR) for a list, rather than significance level (FPR). The FDR is the expected fraction of false positives in a list of genes selected following a particular statistical procedure. For example, doing a t-test on all genes, and selecting those whose t-score is above a threshold of the .05-point of the t-distribution would be such a procedure. If following this procedure in many experiments would give gene lists including twenty per cent false positives, on average, then the procedure's FDR is 20%. The FDR is distinct from the false positive rate (FPR), which is the rate at which truly unchanged genes appear as false positives. If following a particular statistical procedure on samples with no (really) changed genes gives one positive (falsely) in every fifth experiment, then the procedure's FPR is 20%.
Related to the FDR is the q-value, introduced by Storey [2]. The q-value is the smallest FDR at which a particular gene would just stay on the list of positives. This is not identical to the p-value, which is the smallest false positive rate (FPR) at which the gene appears positive. The p-value is much stricter than the q-value. Most of the researchers, who compute significance of genes by permutations, are actually computing the q-value, rather than the p-value.
As of yet no conventions have been established for false discovery rate in published work. An FDR of 5 or 10% should be acceptable for journal publication of gene lists, in keeping with the practice of accepting 5% of erroneous single results. For individual follow-up experiments, the investigator must decide what's an acceptable waste of time. If the investigator is selecting only half of the genes for follow-up based on a priori biological plausibility, then perhaps a less stringent criterion is acceptable.
Multiple Testing P-Values and False Positives
Suppose you compare two groups of samples drawn from the same larger group, using a chip with 10,000 genes on it. On average 500 genes will appear ‘significantly different’ at a 5% threshold. For these genes, the variation between samples will be large relative to the variation within groups due to random, but uneven allocation of the expression values to the treatment and control groups. Therefore the p-value appropriate to a single test situation is inappropriate to presenting evidence for a set of changed genes.
The quantile plot can single out a modest number of genes that are really different, but it is not a rigorous or systematic procedure, and can’t really handle large numbers of differentially regulated genes. Statisticians have devised several procedures for adjusting p-values to correct for the multiple comparisons problem. The oldest is the Bonferroni correction; this is available as an option in many microarray software packages. The corrected p-value, pi* for gene i is set to: pi* = Npi, if Npi < 1, or 1, if Npi > 1; where pi is the p-value for a single test of gene i, and N is the number of genes being tested (which may be less than the number of genes on the array). This is correct, but too conservative. In practice, few genes meet this strict criterion, including many, which are known differentially expressed from other work. Some researchers use a related ‘single-step’ adjustment procedure: they find the smallest p-value, p(1), which is corrected to Np(1); then the next smallest p-value p(2) is corrected to (N-1)p(2), unless this is smaller than Np(1), in which case it is corrected to the identical value Np(1); successively larger p-values are corrected in similar fashion. This procedure is still too conservative; in fact since N is usually over 10,000, and the number of genes is a few hundred, this procedure gives corrected p-values that are almost the same as the Bonferroni. The reason that both these procedures are too conservative is that test statistics are correlated.  
To give some idea of why correlation makes a difference, imagine an extreme case: suppose all genes are perfectly correlated, and not changed between groups. In that case the tests for all the genes give identical results: the p-values for one gene are the p-values for all. In this case no correction for multiple-comparisons is needed, because all the t-scores either exceed or fall short of the threshold together. For example, if the researcher sets a threshold at the 5% point, then no genes will appear as (false) positives in 95% of all experiments testing for differential expression. Of course, when false positives occur, a great number occur: in 5% of all experiments, all genes will appear as (false) positives; the false positives are ‘clumped’. In practice real gene expression levels are highly correlated, because genes are co-regulated; hence the probability of false positives is much less than calculated by the Bonferroni procedure; on the other hand, when false positives do occur, they tend to occur in abundance. The number of extreme test statistics, and therefore apparently significant p-values, for correlated genes will be more variable than for independent genes, although it will have the same long-run average. Therefore for realistically correlated data, the multiple testing correction of p-values should be weaker than the correction for independent genes. For example, suppose repeated experiments are done with the two groups drawn repeatedly from the same cell line; suppose that 2% of the (unchanged) genes appear significant at the .05 threshold, in 90% of the experiments, and 40% of the genes appear significant at the .05 threshold, in 10% of experiments. Suppose we adopt a procedure of selecting ‘differentially expressed’ genes, only if more than 2% of the genes individually appear significant at the .05 threshold; this procedure will select false positives only in 10% of the experiments. That is, the corrected p-value for more than 2% genes at the .05 level, should be 0.10 (10%).
This gives us an approach to correcting for multiple testing: for a group of genes, which appear to differ between sample types, we ask how often would a group this size exceed the threshold that these genes exceed? To be precise: for a specific number k and a threshold α, how often will random sampling from the same group give at least k single test p-values will fall under the threshold for significance level α? In practice we don’t have the luxury of repeating experiments that could give us these estimates. However we can calculate the results of an experiment, where we resample from our existing samples, and calculate how often large groups of genes appear significant.
Calculating Permutation-Based Corrected P-values
To calculate corrected p-values, first calculate single-step p-values for all genes: p1, …, pN. Then order the p-values: p(1), …, p(N), from least to greatest. Next permute the sample labels at random, and compute the test statistics for all genes between the two (randomized) groups. For each position k, keep track of how often you get at least one p-value more significant than p(k), from gene k, or from any of the genes further down on the list: k+1, k+2, …, N. ?After all permutations, compute the fraction of permutations with at least one apparently more significant p-value less than p(k). This is the corrected p-value for gene k. Although this procedure is complicated, it is much more powerful than the other corrections: that is, the procedure gives a much smaller corrected p-value for each gene than the Bonferroni procedure, and therefore a bigger list of significant genes at any corrected significance level (specified risk of false positives). This is known as the Westfall–Young correction <refs>.
There is a related procedure for computing false discovery rates in the presence of correlation. The FDR procedure is simpler, however it is still under some debate. When this debate is resolved, computing an FDR may be the best way to indicate degree of evidence within the traditions of classical statistics. However there are several emerging approaches from the tradition of Bayesian statistics, which seem even more powerful.
Empirical Bayes Methods
Bayesian approaches make assumptions about the parameters to be estimated (such as the differences between gene levels in treatment and control groups); used intelligently these assumptions can make use of prior experience with microarray data. A pure Bayes approach assumes specific distributions (prior distributions) for the mean differences of gene levels, and their standard deviations. The empirical Bayes approach assumes less, usually that the form of these distributions is known; the parameters of the prior distribution are estimated from data. As we get more detailed knowledge of the variability of individual genes, it should become possible to make detailed useful prior estimates based on past experience. A simple empirical Bayes approach to identifying changed genes runs as follows, in two stages.
We believe that all unchanged genes have a range of variances that follow a known prior distribution. We estimate the mean of that distribution as the mean of the experimental variances for all the genes. We estimate the variance of that distribution as the variance of the gene variances. Both of these estimates assume that a small minority of genes are actually changed. Then we consider each gene individually. We would like an estimate of the variability of that gene that is more reliable than its’ sample standard deviation. One way to derive that is to work backward from the assumption that the gene variances follow the known distribution. We can compute the probability of any value for sample variance, given a supposed value for the (unknown) true variance of that gene. If we combine that with the prior assignment of probability for each true variance of a gene, we can work out the probabilities that various possible true values underlie the one observed value of the variance. Not surprisingly it is more probable that a very high sample variance comes about by an over-estimate of a moderately high variance, than a true estimate of a very high variance, simply because there are many more moderate variances than high variances, and over-estimates are not very uncommon compared to precise estimates. In the Bayesian tradition we construct a density function for the probability function for the true value of the gene variance (called a posterior distribution). To come up with a single value we might estimate the expected value of the posterior distribution. By considerable algebra, this expected value turns out to be a weighted average of the sample variance for the gene, and the mean of the prior distribution, which was set to the mean of all the sample variances. Thus we can obtain a theoretically more reliable estimate of variation, by pooling information about variation, derived from all genes simultaneously. This more reliable estimate of variation should then translate into more reliable t-scores, with more power to pick up moderate differences in gene abundance between samples.
In practice this works not badly at all. The empirical Bayes estimate of variance is closer to the mean variance, more often than the sample variance, which means that the moderated t-score is more likely to have a moderate (not very small, not very large) value than a true t-score. However the tails of the moderated t distribution are fairly close to the tails of a t distribution based on a more reliable variance estimate, that is, with a higher number of degrees of freedom. This means that a given difference in means often gives a more significant p-value, and that more genes are selected at a particular threshold. However there is more possible, again if we are willing to make another fairly precise assumption.
The second stage of the empirical Bayes procedure is to use prior beliefs about the number of genes that will be changed. Suppose that based on past experience we believe that some fraction p1 of genes are actually changed by the treatment, and the remaining fraction p0 = 1 - p1 are unchanged. Then we examine the distribution of the p-values from all the t-scores from all the genes in the experiment (not just the significant ones). This is better done with the raw (rather than moderated) t-scores, since the distribution of moderated t-scores doesn’t quite match near 0, where the larger p-values are. The way that p-values are constructed for a t-score, we should find even numbers of p-values in any interval of the same length. We find generally that there are fewer p-values in the range 0.5 to 1.0 than there should be (there should be N/2 such p-values), and correspondingly more in the range 0.0 to 0.5. The natural assumption is that some genes are missing from the range 0.5 to 1.0, because they are really differentially expressed. The number of genes remaining, out of the total N/2 that we would expect, gives an estimate of p0, the fraction of genes that are unchanged. Let's look at the fraction of p-values between .5 and 1, say M. Then p0 ≈ M/(2*N).
Once we have prior empirical estimates of p1 and p0, we can construct the odds ratio for change in expression versus unchanged; that is, we can estimate the probability of getting any particular t-score if the gene is changed, and compare that to the probability if the gene is unchanged. The ratio of probabilities is the odds, and we imagine placing a bet on those genes with odds ratios in favor of change, above a particular threshold. The probability of getting a particular t-score from an unchanged distribution is the t-distribution. The probability of a particular t-score given a changed gene depends on the magnitude of the change. This would be easy to work out, if say we were interested only in genes with a two-fold or greater change. Then the probability distribution can be worked out. If we want to detect genes of any change, then we need to specify a prior distribution for the size of the fold-changes among genes. This is very difficult to estimate empirically.
Another approach to this does away with the assumption of a specific fold change in the changed genes, at the cost of considerably increased complexity. The distribution of t-scores from the unchanged genes is of course a t-distribution. The distribution of t-scores from changed genes is some other unknown distribution, presumably with wider tails, and possibly bimodal (see figure). The distribution of all scores is the mixture of these two distributions with mixture parameters p0, p1. The density function of all the t-scores is p0f0(t) + p1f1(t). Then for a given gene with t-score ti, the posterior probability of belonging to class 1, is given by Bayes' formula: P(1|t) = P(t & 1) / P(t) = p1f1(t) / f(t) = 1 - p0f0(t)/f(t), where f0 is the known t-distribution and f is the empirical distribution. In practice this is reasonably robust provided that the tails of f are fairly thick, and that a well-conditioned estimate for the density is used. It's best to fit the distribution function with a smooth curve and take a first derivative, insisting that it be monotone.

Several Groups – Analysis of Variance

Many current microarray studies compare more than two groups. Sometimes the question is to determine differences among three or more cell lines, or strains of experimental animal. Another common design compares the effect of a particular treatment (often a ligand for a receptor), on cell lines (or animals) with wild-type and mutant versions of the receptor. Usually the experimenter wants to know which genes are actively regulated during treatment in both cell lines, or wants some criterion for selecting those that are differentially regulated among groups. These questions belong in the tradition of analysis of variance (ANOVA).
Generally, all of the procedures that were discussed above in the context of two-sample comparisons, carry over to analogues in ANOVA. However the ANOVA analogues are more complex, because many hypotheses are being tested, and some nested within others. Especially in the factorial design case, there is no obvious way to do permutation testing to obtain genome-wide p-values for the interaction (2nd order) effects. Several researchers have suggested permuting the residuals from a fit of the main effects to obtain a permutation distribution.
Analysis of variance is complex and many researchers don’t bother; they do t-tests on the contrasts that interest them. This procedure is less effective than analysis of variance for two reasons. The power of a t-test to pick up a difference increases with greater confidence in the denominator – the estimate of variability. ANOVA computes a consensus estimate of variability within groups, based on all the groups. This estimate, based on more information, has more confidence (greater degrees of freedom) than the variability estimated between two samples alone. Thus for the same degree of difference, and the same variability estimate, the ANOVA will pick up more differences than the t-test. It’s possible to use the consensus estimate of variability in the t-score denominators for all tests.
Sometimes when researchers compare treatment effects on WT and mutant, they look for genes that are significant on one list and not on the other. This procedure is very fallible; if genes are changed by treatment to the same extent in both samples, according to statistical theory, the significance levels should fluctuate considerably. Many should appear on one list but not on the other. The ANOVA for a factorial design is the most efficient way of identifying the true changes in regulation under treatment among the many noisy genes.
 
 
1.         Tusher, V.G., R. Tibshirani, and G. Chu, Significance analysis of microarrays applied to the ionizing radiation response. Proc Natl Acad Sci U S A, 2001. 98(9): p.5116-21.
2.         Storey, J.D. and R. Tibshirani, Statistical significance for genomewide studies. Proc Natl Acad Sci U S A, 2003. 100 (16): p. 9440-5.

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