 Methodology Article
 Open Access
 Published:
Optimal alpha reduces error rates in gene expression studies: a metaanalysis approach
BMC Bioinformatics volume 18, Article number: 312 (2017)
Abstract
Background
Transcriptomic approaches (microarray and RNAseq) have been a tremendous advance for molecular science in all disciplines, but they have made interpretation of hypothesis testing more difficult because of the large number of comparisons that are done within an experiment. The result has been a proliferation of techniques aimed at solving the multiple comparisons problem, techniques that have focused primarily on minimizing Type I error with little or no concern about concomitant increases in Type II errors. We have previously proposed a novel approach for setting statistical thresholds with applications for high throughput omicsdata, optimal α, which minimizes the probability of making either error (i.e. Type I or II) and eliminates the need for posthoc adjustments.
Results
A metaanalysis of 242 microarray studies extracted from the peerreviewed literature found that current practices for setting statistical thresholds led to very high Type II error rates. Further, we demonstrate that applying the optimal α approach results in error rates as low or lower than error rates obtained when using (i) no posthoc adjustment, (ii) a Bonferroni adjustment and (iii) a false discovery rate (FDR) adjustment which is widely used in transcriptome studies.
Conclusions
We conclude that optimal α can reduce error rates associated with transcripts in both microarray and RNAseq experiments, but point out that improved statistical techniques alone cannot solve the problems associated with high throughput datasets – these approaches need to be coupled with improved experimental design that considers larger sample sizes and/or greater study replication.
Background
Microarrays and next generation sequencing (NGS) have been described as technological advances that provide global insight into cellular function and tissue responses at the level of the transcriptome. Microarray and NGS are used in experiments in which researchers are testing thousands of singlegene hypotheses simultaneously. In particular, microarrays and NGS are often used to test for differences in gene expression across two or more biological treatments. These highthroughput methods commonly use pvalues to distinguish between differences that are too large to be due to sampling error and those that are small enough to be assumed to be due to sampling error. There is little doubt that microarrays/NGS have made a large contribution to our understanding of how cells respond under a variety of contexts, for example in environmental, developmental, and the medical sciences [1,2,3].
High throughput methods have, however, made interpretation of hypothesis testing more difficult because of the large number of comparisons that are done in each experiment [4]. That is, researchers will examine the effects of one or more treatment on the abundance of 1000s of transcripts. For each gene, there will be replication and a null hypothesis test of whether there is a statistically significant difference in relative expression levels among treatments. In most cases, the statistical threshold for rejecting the null hypothesis (i.e. α) is α = 0.05 although it may occasionally be set at a lower value such as 0.01 or 0.001. Thus, for any individual comparison, the probability of rejecting the null hypothesis when it is true is 5% (if the threshold is set at 0.05). When multiple tests are conducted on 1000’s of transcripts, this creates the potential for hundreds of false positives (i.e. Type I error) at the experimentwide scale, with the expected number of false positives depending on both the number of tests conducted (known) and the number of those tests where the treatment has no effect on gene expression (unknown). Researchers identified this problem early on and have used a variety of posthoc approaches to controlling for false positives [5,6,7,8,9].
Approaches for adjusting pvalues and reducing false ‘positives’ when testing for changes in gene expression, such as Bonferroni or BenjaminiHochberg procedures, are designed to control experimentwide error probabilities when many comparisons are being made. Typically they reduce the α for each test to a value much smaller than the default value of 0.05, so that the experimentwide error is not as inflated due to the large number of comparisons being made. They all share the characteristic that they only explicitly address probabilities of Type I errors [4]. This has the effect of increasing the probability of false negatives (i.e. Type II errors) to varying degrees. This focus on Type I errors implies that it is much worse to conclude that gene expression is affected by a treatment when it is not than to conclude that expression is not affected by a treatment when, in reality, it is. Although there has been some focus on methods designed to balance Type I and Type II error rates [10], researchers rarely discuss the Type II implications of controlling Type I errors, and we believe this suggests that most researchers simply are not considering the effect of posthoc adjustments on Type II error rates. Krzywinski and Altman [4] note the problem and offer practical advice, “we recommend always performing a quick visual check of the distribution of P values from your experiment before applying any of these methods”. Our position is that this does not go far enough; we assert that posthoc corrections to control Type I errors don’t make sense unless (1) the researcher knows their Type II error probability (i.e. power) and (2) has explicitly identified the relative costs of Type I and II errors. We have recently developed a solution, optimal α, that balances α (the acceptable threshold for Type I errors – usually 0.05) and β (the acceptable threshold for Type II errors – often 0.20 but the standard practice is more variable than for α), minimizing the combined error rates and eliminating the need for any posthoc adjustment [11,12,13]. In the context of transcriptomics, this reduces the overall error rate in identifying differentially expressed genes by finding the best tradeoff between minimizing false detections of differential expression and minimizing nondetection of true differential expression.
While we have demonstrated this approach in the context of detecting environmental impacts of pulp and paper mills [13], it is of particular value in fields such as transcriptomics where many tests are conducted simultaneously. While microarrays and RNAseq have been tremendous technological advances for transcriptomics, when coupled with low sample sizes, it magnifies multiple comparisons problems. The objectives of this paper were to apply optimal α to a set of published microarray data to demonstrate that using the optimal α approach reduces the probabilities of making errors and eliminates the need for any posthoc adjustments. In addition, we discuss modifications to the experimental design of microarray data that directly address the problem of multiple comparisons.
Methods
Data collection
We collected data on microarray experiments conducted in teleost fishes spanning a period of 10 years (see Additional file 1: Data S1). Environmental toxicology is the research focus of one of the authors, however we point out here that this approach is not confined to aquatic toxicology and is applicable across disciplines. The search for microarray fish studies was conducted from January 2011–August 2011 using the search engines Web of Science, Science Direct, PubMed (National Center for Biotechnology Information), and Google Scholar. Keywords and combinations of key words used in the search engine included “microarray”, “gene expression”, “DNA chip”, “transcriptomics”, “arrays”, “fish”, “teleost”, and “aquatic”. In addition, references from papers were reviewed for information on manuscripts not identified by the search engines. This intensive search resulted in representation of studies encompassing a wide range of teleost fishes and scientific disciplines (e.g. physiology, toxicology, endocrinology, and immunology). There were a total of 242 studies surveyed for information (Additional file 1: Data S1).
The extracted data from microarray experiments included fish species, family, sex, analyzed entity (e.g. cell, tissue), experimental treatment, concentration (if applicable), duration, exposure type, microarray platform, type of normalization, number of biological replicates, endpoints assessed, number of differentially expressed genes (DEGs) identified by the researchers, total gene probes on the array, average fold change of DEGs, and the method of post hoc analysis. Approximately 50% of these studies applied an FDR threshold as the method of choice for detecting differentially expressed genes. All microarray data were normalized by the authors of the original studies using the method of their choice (there are different methods but they differ only slightly).
Calculating optimal Α
For each study, we calculated optimal α levels [11] that minimized the combination of Type I and Type II error probabilities, and compared the Type I and II error probabilities resulting from this approach to those associated with using α = 0.05. Data are summarized on a perpaper, not on a per test basis.
The calculation of an optimal α level requires information concerning the test type, the number of replicates, the critical effect size, the relative costs of Type I vs. Type II errors, and the relative prior probabilities of null vs. alternate hypotheses. Optimal α calculations are based on minimizing the combined probability or cost of Type I and II errors by examining the mean probability of making an error over the entire range of possible α levels (i.e. from 0 to 1). This is a 5 step process. Step 1 – Choose an α level between 0 and 1. Step 2 – Calculate β for the chosen α, sample size, critical effect size and variability of the data (this can be achieved using a standard calculation of statistical power for the statistical test being used, beta is 1 – statistical power), Step 3 – Calculate the mean of α and β, Step 4 – Choose a new α slightly smaller than the previous α and compare the mean error probability with the previous iteration. If it is larger choose a new α slightly larger than the previous α. If it is smaller choose a new α slightly smaller than the current α, Step 5 – Keep repeating until the improvement in mean error probability fails to exceed the chosen threshold – at this stopping point you have identified optimal α. Several assumptions or constraints were made to enable consistent optimal α analysis of studies with a wide degree of technical and statistical methodologies:
Assumptions
(1) We used the number of biological replicates in each group as the level of replication in each study. Microarrays were sometimes repeated on the same biological replicates but this was not treated as true replication, regardless of whether it was treated as replication within the study. Similarly, spot replicates of each gene on a microarray were not treated as replication, regardless of whether it was treated as replication within the study There were 39 studies which had levels of biological replication of n = 1, or n = 2. These studies were omitted from further statistical analysis, leaving 203 studies with biological replication of n ≥ 3.
(2) Two hundred and three of the 242 studies identified were suitable for analysis and to ensure that the optimal α value in all 203 studies were calculated on the same test and are comparable, we analyzed each study as an independent, twotailed, twosample ttest even though some studies used confidence interval, randomization or Bayesian analyses instead of ttests. ANOVA was also occasionally used instead of ttests but even in cases where ANOVA was used, it was the posthoc pairwise comparisons between each of the experimental groups and a control group that were the main focus. These posthoc pairwise comparisons are typically ttests with some form of multiple comparison adjustment. Onetailed or paired ttests were sometimes used instead of twotailed independent tests. Although these tests do increase power to detect effects, they do so by placing restrictions on the research question being asked.
(3) Critical effect size, in the context of ttests, is the difference in the endpoint (in this case, gene expression) between treatment and control samples that you want to detect. In traditional null hypothesis testing, β is ignored and critical effect sizes are not explicitly considered. We calculated optimal α levels at three potential critical effect sizes, defined in terms relative to the standard deviation of each gene (1 SD, 2 SD and 4 SD). Foldchanges or percent changes from the control group were occasionally used as critical effect sizes, but we avoided these effect sizes to maintain consistency across optimal α calculations and because we believe the difference in expression relative to the variability in the gene is more important than the size of effect relative to the control mean of the gene. A twofold change in a gene may be well within the natural variability in expression of one gene and far outside the natural variability in expression of another gene. However, there may be contexts where foldchanges are more appropriate than standard deviations and optimal alpha can accommodate this by setting separate optimal alphas for each gene. Separate thresholds would be required because detecting a 2fold change in a highly variable gene would result in a larger optimal alpha than detecting a 2fold change a gene with little variability.
(4) We assumed the relative costs of Type I and Type II errors to be equal, representing a situation where researchers simply want to avoid errors, regardless of type. However, optimal alpha can accommodate any estimates of the relative costs of Type I and II errors (See code in Additional file 2: Appendix S1). So, where there is clear evidence of different relative Type I and II error costs they should be integrated into optimal alpha estimates. Multiple comparison adjustments that reduce Type I error rates without (1) estimating Type II error probability and (2) the relative costs of Type I and II errors are illadvised.
(5) We assumed that the prior probabilities for the metaanalysis and the required within and amongstudy replication to be  H_{A} prior probability = 0.50 and H_{o} prior probability = 0.50. For the simulations comnparing optimal alpha error rates relative to traditional multiple comparisons approaches we used three prior probability scenarios  Scenario 1: H_{A} prior probability = 0.50 and H_{o} prior probability = 0.50, Scenario 2: H_{A} prior probability = 0.25 and H_{o} prior probability = 0.75, and Scenario 3: H_{A} prior probability = 0.10 and H_{o} prior probability = 0.90. There has been relatively little empirical work done describing the proportion of genes that are affected by treatments in microarray studies but [14] examined the effects of mutations in different subunits of the transcriptional machinery on the percent of genes that showed differential expression and concluded that the percent of genes ranged from 3 to 100% with a mean of 47.5%. Another estimate by Pounds and Morris [15] suggested that slightly more than half the genes in a study examining two strains of mice showed differential gene expression. In addition, accurate estimation of global gene expression has been complicated by inappropriate assumptions about gene expression data [16, 17] and further research in this area is critical. There is no way of being certain of how many true positives and true negatives there are in each study but in the absence of any prior knowledge the rational assumption is that the probabilities are equal (Laplace’s principle of indifference). However, in the context of gene expression a differential expression prior probability of 0.50 is at the high end and so we also examined H_{A} prior probabilities of 0.25 and 0.10. Prior probabilities other than equal can be accommodated by optimal α and using other prior probabilities would result in quantitative differences in the results. However, the general conclusion that optimal alpha error rates will always be as low or lower than traditional approaches does not depend on the assumed prior probabilities.
Analyses
Minimum average of α and β for each of the 203 studies at 3 different critical effect sizes (1, 2, and 4 SD’s): We calculated the average of α and β using optimal α and the traditional approach of setting α = 0.05. To do this we calculated optimal α for each of the 203 studies as described above, extracted the β associated with optimal α for each of the 203 studies, and calculated the average of α and β. Similarly, we extracted the β associated with α = 0.05 for each of the 203 studies when and then calculated the average of α and β. We could then compare the average of α and β for optimal α and α = 0.05.
Effect of posthoc corrections on error rates (see Additional file 3: Data S2)
We simulated 15,000 tests of the effect of a treatment for each of 3 prior probability scenarios and 3 effect size scenarios. The prior probability scenarios were Scenario 1: H_{A} prior probability = 0.50 and H_{o} prior probability = 0.50, Scenario 2: H_{A} prior probability = 0.25 and H_{o} prior probability = 0.75, and Scenario 3: H_{A} prior probability = 0.10 and H_{o} prior probability = 0.90. The effect size scenarios were Scenario 1: 1 SD, Scenario 2: 2 SD, and Scenario 3: 4 SD. All comparisons were made using twotailed, twosample ttests. Based upon experience and the literature, gene expression studies vary widely in the proportion of genes that are differ entially expressed and usually show a small effect (1 SD). We only select larger values (2 and 4 SD) above to illustrate the application of the optimal α compared to other posthoc tests. All differences between treatment and control were chosen from normal distributions that reflected the ‘true’ differences (i.e. 0, 1, 2 or 4 SD’s). We calculated error rates using optimal α, α = 0.05, α = 0.05 with a Bonferroni correction and α = 0.05 with a BenjaminiHochberg False Discovery Rate correction. We then compared the total number of errors across all 15,000 tests for the four different approaches. For example, using Scenario 1 for both effect size and prior probability we compared the 4 approaches under the assumption that half the genes were affected by the treatment and the size of the effect for those 7500 genes was 1 SD. By contrast, using Scenario 3 for both prior probability and effect size we assumed that 1500 of the genes were differentially expressed and the size of the effect was 4 SD.
Minimum number of withinstudy replicates needed to meet desired error rate
The same iterative process that can be used to calculate minimum average error rate for a specific sample size can be used to calculate minimum sample size for a specific average error rate. Here we identified a range of minimum acceptable average error rates from 0.00001 to 0.125 (reflecting the common practice of α = 0.05 and β = 0.2) and calculated the minimum sample size required to achieve the desired error rates for 3 different effect sizes (i.e. 1, 2, and 4 SD’s).
Minimum amongstudy replication needed to meet desired error rate
An alternative to large withinstudy replication is to synthesize similar studies that have been replicated several times. Here we simply identified how often a study would have to be repeated at a specific optimal α to achieve a desired error rate. For example, to detect a 1 SD difference between treatment and control using a 2sample 2tailed ttest with a sample size of 4 the optimal α is 0.29. If optimal α is 0.29 but the desired error rate is 0.00001 we solve for x in 0.00001 = 0.29^x and conclude that 10 studies showing a significant difference between treatment and control expression would be necessary to meet our desired threshold. Similarly, β at this optimal α is 0.38 and we would need 12 studies showing no significant difference between treatment and control to meet our desired error rate.
Results
Metaanalysis
Across all studies, the median number of genes tested with ≥3 replicates was 14,900 and the median number of replicates ≥3 was 4 (Fig. 1). Using optimal α instead of α = 0.05 resulted in a reduced probability of the combination of Type I and II errors of 19–29% (Table 1). One important conclusion is that under current practices, tests intended to detect effect sizes of 1 SD will make errors in 5% of tests if there are no treatment effects on any of the genes but the median level of replication (3 replicates per treatment) will make errors in more than 77% of tests if all the genes are affected by the treatment(s) and will make errors in more than 41% of the tests if half the genes are affected by treatment(s). That is, they will maintain the probability of making Type I errors at 0.05 but have highly inflated Type II error probabilities (i.e. low power). For tests intended to detect a 2 SD effect size, again the overall error rate will be 5% if none of the genes are affected by treatment(s) but will be more than 34% with median replication if all the genes are affected by the treatment(s) and almost 20% if half the genes are affected by treatment(s). So, current experimental design practices for microarrays are inadequate, especially with respect to Type II errors, and posthoc corrections are not mitigating this problem (see below). It is important to note that we do not know the true error rates – for that we would have to know how many and which genes were actually differentially expressed. These are estimated error rates under the assumptions that (1) prior probabilities for H_{A} and H_{0} are equal and (2) critical effect sizes are SD =1,2, or 4.
Sample size estimates (withinstudy replication)
Many microarray and RNAseq studies (n = 3 per treatment) are only appropriate for detecting effects sizes at least of 4 SD at Type I and II error rates of 0.05 or greater. Traditionally, the least conservative acceptable error rates have been set at 0.05 for Type I errors and, when they consider Type II errors, at 0.20 for Type II errors. This implies an average error rate of 0.125 (i.e. [α + β] / 2 ≤ 0.125, the average of α and β associated with using α = 0.05 and achieving 80% statistical power). To detect an effect of 2 SD at an error rate of 0.125 would require sample sizes greater than 5 per treatment, and detecting an effect of 1 SD would require at least 16 samples per treatment (Table 2).
Repeating the experiment (among study replication)
Using the optimal α minimize the combined probabilities of Type I and II errors, to reduce the probability of making a Type I error for any particular gene to 0.10 for an effect size of 1 SD using a sample size at the high end of what is usually used in microarray studies (i.e. 10 replicates per treatment), an experiment would have to show a statistically significant effect for a gene in two consecutive experiments. To reduce the probability to 0.001, the experiment would have to show a statistically significant effect for a gene in 4 consecutive experiments. Similarly, to reduce the probability of missing a real effect to 0.10 for an effect size of 1 SD, an experiment with 10 replicates per treatment would have to show no statistically significant effect for a gene in two consecutive experiments. To reduce this probability to 0.001, there would have to be no statistically significant results in 5 consecutive experiments. On the other hand, if the critical effect size is 4 SD, one experiment is all that would be needed for most traditional sample sizes and error rates (Tables 3a and b)
Optimal α versus no posthoc and traditional posthoc analyses
We used three sets of simulated scenarios of 15,000 tests with 4 replicates per group. The scenarios differed in the assumed prior probability of the null and alternate hypotheses with Scenario 1 assuming a 50% probability of the alternate being true, Scenario 2 a 25% probability and Scenario 3 a 10% probability. Each scenario examined 3 different critical effect sizes, 1, 2, and 4 SD. Optimal α consistently resulted in fewer or the same overall errors when compared to any of the following approaches; no posthoc test, Bonferroni correction, or an FDR (Table 4AC).
Optimal α reduced the number of overall errors (α and β) relative to other approaches by as much as 96%. When the assumed prior probability of H_{A} is low (i.e. 10%) and the critical effect size is small (i.e. 1 SD) Bonferroni and FDR adjustments do as well as optimal alpha because the threshold is so stringent that they find no significant results. Thus, the only error that is made is a Type II error and these approaches miss all 1500 true effects. Optimal alpha makes slightly fewer Type II error, at 1495. In addition, half of the 10 significant results found using the optimal alpha threshold are false positives resulting in the same number of errors which was 1500 and the same number as for Bonferroni or FDR adjustments. No posthoc adjustments under these circumstances result in many more true effects being detected but also many more type I errors – more than half of the statistically significant results are false positives. The most conservative posthoc adjustment, Bonferroni, routinely resulted in the largest overall error rate when the critical effect size was large while not using a posthoc analysis resulted in fewer errors than either a Bonferroni or FDR except when the prior probability and critical effect size were small. Of course, the distribution of Type I and II errors varies among approaches, with no post hoc adjustment and the FDR adjustment resulting in a relatively large number of Type II errors when the critical effect size was 1 or 2 SD. However, no posthoc adjustment produced relatively large number of Type I errors when the critical effect size was 4 SD while the FDR approach still resulted in more type II errors. Bonferroni resulted in zero Type I errors but a large number of Type II errors at all effect sizes. Optimal alpha resulted in a much more even distribution of Type I and II errors except when the prior probability and critical effect size was small.
Discussion
Researchers using high throughput expression techniques enjoy the benefits of global analyses, but must acknowledge the statistical issues associated with an extremely large number of comparisons. Problems may become exacerbated as even higher throughput techniques such as RNASeq become more common and genome projects continue to increase the capacity of microarray platforms. RNAseq experiments are currently restricted due to cost to small sample sizes for each comparison which further exacerbates the error rates. Researchers have generally dealt with the issue of multiple comparisons by using one or more posthoc adjustments designed to control Type I error rates [18, 19] and it is unlikely that one can publish transcriptomic datasets without using some form of posthoc correction (e.g. FDR [20], Bonferroni, Tukey’s range test, Fisher’s least significant difference and Bayesian algorithms). Techniques are more conservative (i.e. less likely to result in a Type I error) or less conservative (more likely to result in a Type I error) and implicit in choosing one technique over another is a concern about making a Type II error. That is, the only reason to use a less conservative posthoc adjustment is if one is concerned about the increasing Type II error rate associated with lowering the probability of making a Type I error. This has, inevitably, led to a largescale debate that has been relatively unproductive because it is rarely focused on the fundamental issue, that all posthoc adjustments are designed to reduce Type I error rates (i.e. concluding gene expression has been affected by a treatment when it has not) with little or no explicit regard for the inevitable increase in Type II error rates (i.e. concluding that the treatment has had no effect on gene expression when it has) [21]. Any informed decision about posthoc adjustments requires a quantitative understanding of both α and β probabilities [22, 23] and a clear assessment of the relative costs of Type I and II errors. However, no posthoc test currently attempts to explicitly and quantitatively integrate control of Type I and II errors simultaneously and the result is that none of them minimize either the overall error rates or costs of making an error.
One proposed solution to balancing concerns is to set Type I and II error thresholds to be equal [24]. However, the threshold that minimizes the probability of making an error may not be where the Type I and II error probabilities are equal and if Type I and II errors have equal costs, then we should seek to minimize their average probability with no concern for whether the individual probabilities are equal. This is a critical and underemphasized problem in bioinformatics. Our results demonstrate that using optimal α results in reduced error rates compared to using p = 0.05 with or without posthoc corrections. However, it is unlikely that the improvement in error rates attributed to using optimal α will be the same as those estimated here. These results were calculated based on the assumption that the prior probabilities of the alternate being true were 0.5, 0.25 and 0.10, that the costs of Type I and II errors are equal, that the targeted critical effect sizes are 1, 2, or 4 SD and that the results in these 203 studies are representative of all disciplines. But optimal α can accommodate different assumptions about prior probabilities, relative error costs and critical effect sizes and, though the degree to which optimal alpha is superior to traditional approaches may vary, the fundamental conclusion that optimal α error probabilities are as good or better than traditional approaches holds under different assumptions about prior probabilities or critical effect sizes. That said, this is only certain to hold true when we make the assumption implied in null hypothesis testing, that there is either no effect (H_{0}) or there is an effect as large as the critical effect size (H_{A}).
Multiple comparisons problem
One particular advantage of optimal α is that it makes posthoc corrections unnecessary and, in fact, undesirable (correction implies that something desirable has occurred when that isn’t necessarily so – we were tempted to call it a posthoc distortion). This should dispel some of the complexity and confusion surrounding the analysis of transcriptomic data. However, while optimal α can minimize the errors associated with the large number of comparisons made using microarrays for example, neither optimal α nor any form of posthoc correction can eliminate the problems associated with multiple comparisons. Any posthoc test that is done to lower the probability of a Type I error will increase the probability of making a Type II error. While optimal α minimizes the probability of making an error, there will still be an enormous number of unavoidable errors made simply because we are doing a large number of comparisons. There is no simple solution to solving the effects of multiple comparisons of error rates. However, progress can be made by developing new standards for the experimental design of microarray data including large increases in withinstudy replication, increased among study replication and/or use of ‘network’ approaches which broaden hypotheses to include suites of genes and reduce the total number of hypotheses being tested.
Experimental design solutions
Our results suggest that standard withinstudy replication (i.e. 3–8 replicates per treatment) is adequate for critical effect sizes of 2 or 4 SD’s at a target overall error rate of 0.05. Thus, increased replication would only be warranted if detecting smaller effect sizes were desirable. However, we question whether error rates = 0.05 are appropriate when 44 thousand comparisons are being made because a threshold error rate of 0.05 still results in thousands of errors. This is a particular problem when even a handful of statistically significant results might be considered reason enough for publication. We suggest that where thousands of comparisons are being made, the standard for statistical significance must be higher, say, 0.0001 or 0.00001 but not through the use of posthoc corrections that will increase the probability of Type II errors. To meet these standards and retain high statistical power, withinstudy replication would require dramatic increases in the number of biological replicates used in experiments. Currently, the standard appears to be 3–8 biological replicates per treatment. Replication is limited by a variety of factors including financial costs, available person hours, sample availability, and physical space. However, where possible, it would often be preferable to test fewer genes using much larger samples sizes, especially because the price of microarrays/NGS will likely to continue to drop, making replication of 50, 100 or 200 possible and, in some cases, warranted. These may seem like drastic replication recommendations but the problems associated with high throughput of molecular data are unusual and perhaps unprecedented and it is not surprising that when the number of comparisons that can be made at one time is large the number of replicates per comparison will also need to be large. Our results suggest that the number of replicates per treatment required to maintain acceptable error rates is large, and estimated to be 15–150, depending on the critical effect size.
An alternative approach is to replicate experiments rather than increasing the number of replicates within an experiment. This would involve identifying the number of times one would have to see the same result repeated, given a particular experimental design, before we would be willing to accept the result. Our results suggest that if 8–10 replicates per treatment are used and the critical effect size is 2 or 4 SD’s then an experiment would not need to be repeated to meet at error rate = 0.05. However, the argument for a more stringent acceptable error rate applies here as well and so at an error rate of 0.0001 experiments would need to be repeated 2–10 times. It’s not clear whether increased withinexperiment or among experiment replication would be more efficient and may depend on the limiting factors in particular labs. However, it is clear that amongexperiment replication adds an additional layer of inferential complexity because it would require interpretation of cases where a subset, but not all, of the experiments was consistent.
It’s not clear whether within or amongstudy replication is preferable – which is preferable may depend on context – but it is clear that one or both are necessary if conclusions of microarray studies are to be rigorous and reliable.
Relative costs of type I and II errors
All of our analyses assumed that the costs of Type I and II errors were equal but we do not preclude the possibility that Type I and II errors should be weighted differently [25,26,27] and an additional advantage of optimal α is that the cost of error can be minimised rather than the probability of error. Thus, if the relative costs of Type I and II error can be estimated they can be integrated into the selection of appropriate statistical thresholds. The question of relative costs of Type I and II errors is a difficult and relatively unexplored one but the objectives of a study can often guide setting relative costs of Type I and II error. For example, preliminary work ‘fishing’ for genes that may respond to a specific treatment might be more concerned about missing genes that were actually affected than identifying genes as affected when they really weren’t and would choose to set the cost of Type II errors greater than Type I errors. By contrast, a researcher attempting to identify a single gene (i.e. biomarker) that is regulated by a specific treatment or drug might decide that Type I error is a larger concern.
Posthoc multiple comparison adjustments to reduce Type I errors at the expense of increased Type II errors imply that Type I errors are more serious than Type II errors. Although we don’t believe Type I errors are actually more serious than Type II errors under all circumstances in which multiple comparison α adjustments have been used, similar outcomes can be obtained through the optimal α approach by selecting a large Type I / Type II error cost ratio a priori.
SD versus kfold effect size
One potential complication is that the convention in microarray analysis is often to use effect sizes expressed as multiples of the control mean (e.g. 1fold, 2fold or 4fold change). Unlike effect sizes measured in standard deviations, which combine the raw effect size with the variability of the data, kfold effect sizes, even when combined with a statistical significance threshold, do not quantitatively incorporate variability in the data. This implies that if a constant kfold effect size was set as the critical effect size, say 2fold, that there would be a different optimal α for each comparison, depending on the variability in expression of each gene. That is, if there were 44,000 comparisons, it would require 44,000 different optimal α levels. However, if kfold effect sizes are used, solutions include (i) setting a single optimal α based on the ‘average’ variability across genes, (ii) grouping genes into variability categories and using a single optimal α for each category based on the average variability in each category, and (iii) setting an individual optimal α for each gene. While both –kfold and SD effect sizes are reasonable indices of effects, using SD simplifies the application of optimal alpha. However, for microarray and RNAseq, there are approaches such as Voom [28] that would allow using both kfold changes and a single optimal alpha for all genes by making the variance homoscedastic.
A priori H_{0} and H_{A} probabilities
The accuracy of estimates of optimal alpha is a function of assumptions about the a priori probabilities of H_{0} and H_{A}. It is inarguably true that estimates of optimal alpha will be less reliable if estimates of a priori H_{0} and H_{A} probabilities are inaccurate. Thus, research into prior probabilities of global gene expression is critical. One key advantage of optimal alpha is that it has the explicit objective of identifying the threshold that will result in the lowest probability of cost of making a mistake. There is, indisputably, a true optimal alpha – if we know the true a priori probabilities of H_{0} and H_{A} and the true relative costs of Type I and II errors then the statistical threshold that minimizes the probability or cost of making an error can be calculated for any target critical effect size. By contrast, the approach of alpha = 0.05 with post hoc corrections (i.e. Bonferroni or FDR) doesn’t explicitly address Type II errors, it only explicitly addresses Type I errors. Of course, there is an implicit concern about Type II error – if there wasn’t we would simply always set alpha = 0 and never make a Type I error. We don’t set alpha = 0.00 because the goal is to make as few type I errors as possible while also detecting true effects. This implies that we should explicitly address (1) Type II errors, (2) the balance between Type I and II errors and (3) the assumptions about a priori H_{0} and H_{A} probabilities and relative costs of Type I and II errors. Optimal alpha does this and alpha = 0.05 with or without posthoc corrections does not.
Application
We have included R code (Additional file 2: Appendix S1) that can be used to calculate optimal α for ttests ANOVA’s and regressions. To apply optimal α to microarray analysis, you must choose the type of test, sample size, critical effect size, a priori null/alternate probabilities and relative costs of Type I/II errors.

(1)
Type of test: We have written code for ttests, ANOVA’s and regressions. Here we have focused on ttests. The code allows the choice of 1 or 2tailed tests and one, two or pairedsample tests.

(2)
Sample size: This is usually limited by time and/or money. Most microarray studies test many genes with relatively few replicates (3–6) and the result is a large number of false positives and negatives due to insufficient power. A different experimental design may be desired, testing fewer genes with a higher number of replicates (12–24) to reduce the number of errors. This includes a priori hypotheses for specific pathways perturbed by a stressor.

(3)
Critical effect size type: This can be measured in standard deviations (e.g. 1, 2, and 4 SD’s), absolute differences (e.g. difference in signal intensity) or relative differences (e.g. fold differences between treatment and control samples – 0.5, 1, 2× more/less gene expression). SD’s are less labour intensive than absolute r relative differences because you set a single optimal α for all genes. If you target absolute or relative critical effects, it will require a separate optimal α for each gene tested in the microarray. This is because the variability among replicates for different genes will vary and therefore the power to detect the same absolute or fold difference will vary among genes.

(4)
Critical effect size value: A single critical effect size or a range of critical effect sizes can be chosen. Unless there is a defensible reason for choosing a single critical effect size, we suggest selecting a range of critical effect sizes that span small, moderate and large effects. Each critical effect will have a different optimal α (i.e. optimal α for large effects will be smaller than for moderate effects which will be smaller than for small effects) and this allows for different conclusions about small versus moderate versus large effects. For example, it would be reasonable to conclude that there is evidence for small effects but no evidence for moderate or large effects.

(5)
A priori probability of null and alternate hypotheses: There must be explicit quantitative probabilities for these values. We suggest assuming these to be equal (i.e. 0.5 for both) unless you have theoretical or empirical reasons to believe otherwise.

(6)
Relative costs of Type I and II errors: It is not unreasonable to expect that the costs of missing a real effect could be different than detecting a false effect and such difference can be assigned in the code for calculating optimal α. However, unless there is a clear, explicit reason for estimating the costs to be different, we recommend assuming equal costs of Type I and II errors.
Conclusions
While we don’t have empirical estimates of the true error rates associated with the studies used in the metaanalysis, both the metaanalysis and simulations estimated error rates under simple and reasonable assumptions and suggest that optimal α provides a simple and superior approach to setting statistical thresholds for transcriptome analysis than the traditional α = 0.05 with or without posthoc adjustments. Using optimal α will provide significantly lower probabilities of making errors and will eliminate the need to use complex and controversial posthoc adjustments. However, optimal α cannot eliminate the problems associated with the large number of tests that are traditionally carried out in transcriptome analysis. This problem will only become exacerbated as new highthroughput techniques such as RNASeq become more commonly used and increasing amounts of information are generated. Thus, moving forward, researchers should consider setting new standards for within and amongstudy replication and exploring novel approaches to evaluating gene expression data such as in the case of gene enrichment analyses.
Abbreviations
 ANOVA:

Analysis of Variance
 DEG:

Differentially Expressed Genes
 FDR:

False Discovery Rate
 NGS:

Next Generation Sequencing
 RNAseq:

RNA sequencing
 SD:

Standard Deviation
References
 1.
Pantalacci S, Sémon M. Transcriptomics of developing embryos and organs: a raising tool for evodevo. J Exp Zool B Mol Dev Evol. 2015;324:363–71.
 2.
Xu J, Gong B, Wu L, Thakkar S, Hong H, Tong W. Comprehensive assessments of RNAseq by the SEQC consortium: FDAled efforts advance precision medicine. Pharmaceutics. 2016;8:E8.
 3.
Evans TG. Considerations for the use of transcriptomics in identifying the'genes that matter' for environmental adaptation. J Exp Biol. 2015;218:1925–35.
 4.
Krzywinski M, Altman N. Points of significance: comparing samples – part II. Nat Methods. 2014;11:355–6.
 5.
Kooperberg C, Sipione S, LeBlanc M, Strand AD, Cattaneo E, Olson JM. Evaluating test statistics to select interesting genes in microarray experiments. Hum Mol Genet. 2002;19:2223–32.
 6.
Reiner A, Yekutieli D, Benjamini Y. Identifying differentially expressed genes using false discovery rate controlling procedures. Bioinformatics. 2003;19:368–75.
 7.
Pounds S, Cheng C. Improving false discovery rate estimation. Bioinformatics. 2004;20:1737–45.
 8.
Qian HR, Huang S. Comparison of false discovery rate methods in identifying genes with differential expression. Genomics. 2005;86:495–503.
 9.
Brand JPL, Chen L, Cui X, Bartolucci AA, Page GP, Kim K, et al. An adaptive α spending algorithm improves the power of statistical inference in microarray data analysis. Bioinformation. 2007;10:384–9.
 10.
Gordon A, Chen L, Glazko G, Yakovlev A. Balancing type one and two errors in multiple testing for differential expression of genes. Comput Stat Data Anal. 2009;53:1622–9.
 11.
Mudge JF, Baker LF, Edge CB, Houlahan JE. Setting an optimal α that minimizes errors in null hypothesis significance tests. PLoS One. 2012;7:e32734.
 12.
Mudge JF, Edge CB, Baker LF, Houlahan JE. If all of your friends used α=0.05 would you do it too? Int. environ. Assess Manage. 2012;8:563–4.
 13.
Mudge JF, Barrett TJ, Munkittrick KR, Houlahan JE. Negative consequences of using α = 0.05 for environmental monitoring decisions: a case study from a decade of Canada's environmental effects monitoring program. Environ Sci Technol. 2012;46:9249–55.
 14.
Holstege FCP, Jenings EG, Wyrick JJ, Lee TI, Hengartner CJ, Green MR, et al. Dissecting the regulatory circuitry of a eukaryotic genome. Cell. 1998;95:717–28.
 15.
Pounds S, Morris SW. Estimating the occurrence of false positives and false negatives in microarray studies by approximating and partitioning the empirical distribution of pvalues. Bioinformatics. 2003;19:1236–42.
 16.
Loven J, Orlando DA, Sigova AA, Lin CY, Rahl PB, Burge CB, et al. Revisiting global gene expression analysis. Cell. 2012;151:476–82.
 17.
Chen K, Hu Z, Xia Z, Zhao D, Li W, Tyler JK. The overlooked fact: fundamental need of spikein controls for virtually all genomewide analyses. Mol Cell Biol. 2016;36:662–7.
 18.
Cheng C, Pounds S. False discovery rate paradigms for statistical analyses of microarray gene expression data. Bioinformation. 2007;10:436–46.
 19.
Martin LJ, Woo JG, Avery CL, Chen HS, North KE. Multiple testing in the genomics era: findings from genetic analysis workshop 15, group 15. Genet Epidemiol. 2007;31:S124–31.
 20.
Benjamini Y, Hochberg Y. Controlling the false discovery rate: a practical and powerful approach to multiple testing. J R Statist Soc B. 1995;57:289–300.
 21.
Mapstone BD. Scalable decision rules for environmental impact studies: effect size, type I and type II errors. Ecol Appl. 1995;5:401–10.
 22.
Kikuchi T, Pezeshk H, Gittins J. (2008) Bayesian costbenefit approach to the determination of sample size in clinical trials. Stat. Med. 2008;27:68–82.
 23.
O’Brien C, van Riper C III, Myers DE. Making reliable decisions in the study of wildlife diseases: using hypothesis tests, statistical power, and observed effects. J Wild Dis. 2009;45:700–12.
 24.
Munkittrick KR, McGeachy SA, McMaster ME, Courtenay SC. Overview of freshwater fish studies from the pulp and paper environmental effects monitoring program. Water Qual Res J Canada. 2002;37:49–77.
 25.
Yang MCK, Yang JJ, McIndoe RA, She JX. Microarray experimental design: power and sample size considerations. Physiol Genomics. 2003;16:24–8.
 26.
Lin WJ, Hsueh HM, Chen JJ. Power and sample size estimation in microarray studies. BMC Bioinformatics. 2010;11:48.
 27.
Matsui S, Noma H. Estimating effect sizes of differentially expressed genes for power and sample size assessments in microarray experiments. Biometrics. 2011;67:1225–35.
 28.
Law CW, Chen Y, Shi W, Smyth GK. Voom: precision weights unlock linear model analysis tools for RNAseq read counts. Genome Biol. 2014;15(2):R29.
Acknowledgements
Lillian Fanjoy for compiling studies.
Funding
Natural Sciences and Engineering Research Council of Canada (JH and CJM). NSERC was not involved in the design or conclusions of this research.
Availability of data and materials
The data used in this manuscript are available as supplemental materials.
Authors’ contributions
Concept and experimental design (JFM and JEH); Data collection (CM); Statistical analysis (JFM); First draft (JFM); Further drafts (JFM, JEH, CM). All authors approved the final version.
Competing interests
The authors declare that they have no competing interests.
Consent for publication
Not applicable.
Ethics approval and consent to participate
Not applicable.
Publisher’s Note
Springer Nature remains neutral with regard to jurisdictional claims in published maps and institutional affiliations.
Author information
Additional files
Additional file 1:
Data S1. Description of studies used in the metaanalysis. (XLSX 45 kb)
Additional file 2:
Appendix S1. Rcode for optimal alpha estimates for ttests, ANOVA’s, and regressions. (DOCX 15 kb)
Additional file 3:
Data S2. Raw and summarized simulation data. (XLSX 8649 kb)
Rights and permissions
Open Access This article is distributed under the terms of the Creative Commons Attribution 4.0 International License (http://creativecommons.org/licenses/by/4.0/), which permits unrestricted use, distribution, and reproduction in any medium, provided you give appropriate credit to the original author(s) and the source, provide a link to the Creative Commons license, and indicate if changes were made. The Creative Commons Public Domain Dedication waiver (http://creativecommons.org/publicdomain/zero/1.0/) applies to the data made available in this article, unless otherwise stated.
About this article
Cite this article
Mudge, J.F., Martyniuk, C.J. & Houlahan, J.E. Optimal alpha reduces error rates in gene expression studies: a metaanalysis approach. BMC Bioinformatics 18, 312 (2017). https://doi.org/10.1186/s1285901717283
Received:
Accepted:
Published:
Keywords
 Microarrays
 RNAseq
 Type I and II error rates
 High throughput analysis
 Multiple comparisons
 Posthoc corrections
 Optimal α