Shinichi Nakagawa

Bio: Shinichi Nakagawa is an academic researcher from University of New South Wales. The author has contributed to research in topics: Population & Medicine. The author has an hindex of 88, co-authored 439 publications receiving 39873 citations. Previous affiliations of Shinichi Nakagawa include Gravida & University of Waikato.

A general and simple method for obtaining R2 from generalized linear mixed-effects models

Abstract: Summary The use of both linear and generalized linear mixed-effects models (LMMs and GLMMs) has become popular not only in social and medical sciences, but also in biological sciences, especially in the field of ecology and evolution. Information criteria, such as Akaike Information Criterion (AIC), are usually presented as model comparison tools for mixed-effects models. The presentation of ‘variance explained’ (R2) as a relevant summarizing statistic of mixed-effects models, however, is rare, even though R2 is routinely reported for linear models (LMs) and also generalized linear models (GLMs). R2 has the extremely useful property of providing an absolute value for the goodness-of-fit of a model, which cannot be given by the information criteria. As a summary statistic that describes the amount of variance explained, R2 can also be a quantity of biological interest. One reason for the under-appreciation of R2 for mixed-effects models lies in the fact that R2 can be defined in a number of ways. Furthermore, most definitions of R2 for mixed-effects have theoretical problems (e.g. decreased or negative R2 values in larger models) and/or their use is hindered by practical difficulties (e.g. implementation). Here, we make a case for the importance of reporting R2 for mixed-effects models. We first provide the common definitions of R2 for LMs and GLMs and discuss the key problems associated with calculating R2 for mixed-effects models. We then recommend a general and simple method for calculating two types of R2 (marginal and conditional R2) for both LMMs and GLMMs, which are less susceptible to common problems. This method is illustrated by examples and can be widely employed by researchers in any fields of research, regardless of software packages used for fitting mixed-effects models. The proposed method has the potential to facilitate the presentation of R2 for a wide range of circumstances.

Effect size, confidence interval and statistical significance: a practical guide for biologists.

Abstract: Null hypothesis significance testing (NHST) is the dominant statistical approach in biology, although it has many, frequently unappreciated, problems. Most importantly, NHST does not provide us with two crucial pieces of information: (1) the magnitude of an effect of interest, and (2) the precision of the estimate of the magnitude of that effect. All biologists should be ultimately interested in biological importance, which may be assessed using the magnitude of an effect, but not its statistical significance. Therefore, we advocate presentation of measures of the magnitude of effects (i.e. effect size statistics) and their confidence intervals (CIs) in all biological journals. Combined use of an effect size and its CIs enables one to assess the relationships within data more effectively than the use of p values, regardless of statistical significance. In addition, routine presentation of effect sizes will encourage researchers to view their results in the context of previous research and facilitate the incorporation of results into future meta-analysis, which has been increasingly used as the standard method of quantitative review in biology. In this article, we extensively discuss two dimensionless (and thus standardised) classes of effect size statistics: d statistics (standardised mean difference) and r statistics (correlation coefficient), because these can be calculated from almost all study designs and also because their calculations are essential for meta-analysis. However, our focus on these standardised effect size statistics does not mean unstandardised effect size statistics (e.g. mean difference and regression coefficient) are less important. We provide potential solutions for four main technical problems researchers may encounter when calculating effect size and CIs: (1) when covariates exist, (2) when bias in estimating effect size is possible, (3) when data have non-normal error structure and/or variances, and (4) when data are non-independent. Although interpretations of effect sizes are often difficult, we provide some pointers to help researchers. This paper serves both as a beginner’s instruction manual and a stimulus for changing statistical practice for the better in the biological sciences.

Repeatability for Gaussian and non-Gaussian data: a practical guide for biologists.

Abstract: Repeatability (more precisely the common measure of repeatability, the intra-class correlation coefficient, ICC) is an important index for quantifying the accuracy of measurements and the constancy of phenotypes. It is the proportion of phenotypic variation that can be attributed to between-subject (or between-group) variation. As a consequence, the non-repeatable fraction of phenotypic variation is the sum of measurement error and phenotypic flexibility. There are several ways to estimate repeatability for Gaussian data, but there are no formal agreements on how repeatability should be calculated for non-Gaussian data (e.g. binary, proportion and count data). In addition to point estimates, appropriate uncertainty estimates (standard errors and confidence intervals) and statistical significance for repeatability estimates are required regardless of the types of data. We review the methods for calculating repeatability and the associated statistics for Gaussian and non-Gaussian data. For Gaussian data, we present three common approaches for estimating repeatability: correlation-based, analysis of variance (ANOVA)-based and linear mixed-effects model (LMM)-based methods, while for non-Gaussian data, we focus on generalised linear mixed-effects models (GLMM) that allow the estimation of repeatability on the original and on the underlying latent scale. We also address a number of methods for calculating standard errors, confidence intervals and statistical significance; the most accurate and recommended methods are parametric bootstrapping, randomisation tests and Bayesian approaches. We advocate the use of LMM- and GLMM-based approaches mainly because of the ease with which confounding variables can be controlled for. Furthermore, we compare two types of repeatability (ordinary repeatability and extrapolated repeatability) in relation to narrow-sense heritability. This review serves as a collection of guidelines and recommendations for biologists to calculate repeatability and heritability from both Gaussian and non-Gaussian data.

A farewell to Bonferroni: the problems of low statistical power and publication bias

Abstract: Recently, Jennions and Moller (2003) carried out a metaanalysis on statistical power in the field of behavioral ecology and animal behavior, reviewing 10 leading journals including Behavioral Ecology. Their results showed dismayingly low average statistical power (note that a meta-analytic review of statistical power is different from post hoc power analysis as criticized in Hoenig and Heisey, 2001). The statistical power of a null hypothesis (Ho) significance test is the probability that the test will reject Ho when a research hypothesis (Ha) is true. Knowledge of effect size is particularly important for statistical power analysis (for statistical power analysis, see Cohen, 1988; Nakagawa and Foster, in press). There are many kinds of effect size measures available (e.g., Pearson’s r, Cohen’s d, Hedges’s g), but most of these fall into one of two major types, namely the r family and the d family (Rosenthal, 1994). The r family shows the strength of relationship between two variables while the d family shows the size of difference between two variables. As a benchmark for research planning and evaluation, Cohen (1988) proposed ‘conventional’ values for small, medium, and large effects: r 1⁄4.10, .30, and .50 and d 1⁄4.20, .50, and .80, respectively (in the way that p values of .05, .01, and .001 are conventional points, although these conventional values of effect size have been criticized; e.g., Rosenthal et al., 2000). The meta-analysis on statistical power by Jennions and Moller (2003) revealed that, in the field of behavioral ecology and animal behavior, statistical power of less than 20% to detect a small effect and power of less than 50% to detect a medium effect existed. This means, for example, that the average behavioral scientist performing a statistical test has a greater probability of making a Type II error (or b) (i.e., not rejecting Ho when Ho is false; note that statistical power is equals to 1 2 b) than if they had flipped a coin, when an experiment effect is of medium size (i.e., r 1⁄4 .30, d 1⁄4 .50). Here, I highlight and discuss an implication of this low statistical power on one of the most widely used statistical procedures, Bonferroni correction (Cabin and Mitchell, 2000). Bonferroni corrections are employed to reduce Type I errors (i.e., rejecting Ho when Ho is true) when multiple tests or comparisons are conducted. Two kinds of Bonferroni procedures are commonly used. One is the standard Bonferroni procedure, where a modified significant criterion (a/k where k is the number of statistical tests conducted on given data) is used. The other is the sequential Bonferroni procedure, which was introduced by Holm (1979) and popularized in the field of ecology and evolution by Rice (1989) (see these papers for the procedure). For example, in a recent volume of Behavioral Ecology (vol. 13, 2002), nearly one-fifth of papers (23 out of 117) included Bonferroni corrections. Twelve articles employed the standard procedure while 11 articles employed the sequential procedure (10 citing Rice, 1989, and one citing Holm, 1979). A serious problem associated with the standard Bonferroni procedure is a substantial reduction in the statistical power of rejecting an incorrect Ho in each test (e.g., Holm, 1979; Perneger, 1998; Rice, 1989). The sequential Bonferroni procedure also incurs reduction in power, but to a lesser extent (which is the reason that the sequential procedure is used in preference by some researchers; Moran, 2003). Thus, both procedures exacerbate the existing problem of low power, identified by Jennions and Moller (2003). For example, suppose an experiment where both an experimental group and a control group consist of 30 subjects. After an experimental period, we measure five different variables and conduct a series of t tests on each variable. Even prior to applying Bonferroni corrections, the statistical power of each test to detect a medium effect is 61% (a 1⁄4 .05), which is less than a recommended acceptable 80% level (Cohen, 1988). In the field of behavioral ecology and animal behavior, it is usually difficult to use large sample sizes (in many cases, n , 30) because of practical and ethical reasons (see Still, 1992). When standard Bonferroni corrections are applied, the statistical power of each t test drops to as low as 33% (to detect a medium effect at a/5 1⁄4 .01). Although sequential Bonferroni corrections do not reduce the power of the tests to the same extent, on average (33–61% per t test), the probability of making a Type II error for some of the tests (b 1⁄4 1 2 power, so 39–66%) remains unacceptably high. Furthermore, statistical power would be even lower if we measured more than five variables or if we were interested in detecting a small effect. Bonferroni procedures appear to raise another set of problems. There is no formal consensus for when Bonferroni procedures should be used, even among statisticians (Perneger, 1998). It seems, in some cases, that Bonferroni corrections are applied only when their results remain significant. Some researchers may think that their results are ‘more significant’ if the results pass the rigor of Bonferroni corrections, although this is logically incorrect (Cohen, 1990, 1994; Yoccoz, 1991). Many researchers are already reluctant to report nonsignificant results ( Jennions and Moller, 2002a,b). The wide use of Bonferroni procedures may be aggravating the tendency of researchers not to present nonsignificant results, because presentation of more tests with nonsignificant results may make previously ‘significant’ results ‘nonsignificant’ under Bonferroni procedures. The more detailed research (i.e., research measuring more variables) researchers do, the less probability they have of finding significant results. Moran (2003) recently named this paradox as a hyper-Red Queen phenomenon (see the paper for more discussion on problems with the sequential method). Imagine that we conduct a study where we measure as many relevant variables as possible, 10 variables, for example. We find only two variables statistically significant. Then, what should we do? We could decide to write a paper highlighting these two variables (and not reporting the other eight at all) as if we had hypotheses about the two significant variables in the first place. Subsequently, our paper would be published. Alternatively, we could write a paper including all 10 variables. When the paper is reviewed, referees might tell us that there were no significant results if we had ‘appropriately’ employed Bonferroni corrections, so that our study would not be advisable for publication. However, the latter paper is Behavioral Ecology Vol. 15 No. 6: 1044–1045 doi:10.1093/beheco/arh107 Advance Access publication on June 30, 2004

Multimodel inference in ecology and evolution: challenges and solutions

Abstract: Information theoretic approaches and model averaging are increasing in popularity, but this approach can be difficult to apply to the realistic, complex models that typify many ecological and evolutionary analyses. This is especially true for those researchers without a formal background in information theory. Here, we highlight a number of practical obstacles to model averaging complex models. Although not meant to be an exhaustive review, we identify several important issues with tentative solutions where they exist (e.g. dealing with collinearity amongst predictors; how to compute model-averaged parameters) and highlight areas for future research where solutions are not clear (e.g. when to use random intercepts or slopes; which information criteria to use when random factors are involved). We also provide a worked example of a mixed model analysis of inbreeding depression in a wild population. By providing an overview of these issues, we hope that this approach will become more accessible to those investigating any process where multiple variables impact an evolutionary or ecological response.

The PRISMA 2020 statement: an updated guideline for reporting systematic reviews

Abstract: The Preferred Reporting Items for Systematic reviews and Meta-Analyses (PRISMA) statement, published in 2009, was designed to help systematic reviewers transparently report why the review was done, what the authors did, and what they found. Over the past decade, advances in systematic review methodology and terminology have necessitated an update to the guideline. The PRISMA 2020 statement replaces the 2009 statement and includes new reporting guidance that reflects advances in methods to identify, select, appraise, and synthesise studies. The structure and presentation of the items have been modified to facilitate implementation. In this article, we present the PRISMA 2020 27-item checklist, an expanded checklist that details reporting recommendations for each item, the PRISMA 2020 abstract checklist, and the revised flow diagrams for original and updated reviews.

The Theory of Island Biogeography

Abstract: Preface to the Princeton Landmarks in Biology Edition vii Preface xi Symbols Used xiii 1. The Importance of Islands 3 2. Area and Number of Speicies 8 3. Further Explanations of the Area-Diversity Pattern 19 4. The Strategy of Colonization 68 5. Invasibility and the Variable Niche 94 6. Stepping Stones and Biotic Exchange 123 7. Evolutionary Changes Following Colonization 145 8. Prospect 181 Glossary 185 References 193 Index 201

Human biochemical genetics

Abstract: So far in this course we have dealt entirely with the evolution of characters that are controlled by simple Mendelian inheritance at a single locus. There are notes on the course website about gametic disequilibrium and how allele frequencies change at two loci simultaneously, but we didn’t discuss them. In every example we’ve considered we’ve imagined that we could understand something about evolution by examining the evolution of a single gene. That’s the domain of classical population genetics. For the next few weeks we’re going to be exploring a field that’s actually older than classical population genetics, although the approach we’ll be taking to it involves the use of population genetic machinery. If you know a little about the history of evolutionary biology, you may know that after the rediscovery of Mendel’s work in 1900 there was a heated debate between the “biometricians” (e.g., Galton and Pearson) and the “Mendelians” (e.g., de Vries, Correns, Bateson, and Morgan). Biometricians asserted that the really important variation in evolution didn’t follow Mendelian rules. Height, weight, skin color, and similar traits seemed to

A general and simple method for obtaining R2 from generalized linear mixed-effects models

Abstract: Summary The use of both linear and generalized linear mixed-effects models (LMMs and GLMMs) has become popular not only in social and medical sciences, but also in biological sciences, especially in the field of ecology and evolution. Information criteria, such as Akaike Information Criterion (AIC), are usually presented as model comparison tools for mixed-effects models. The presentation of ‘variance explained’ (R2) as a relevant summarizing statistic of mixed-effects models, however, is rare, even though R2 is routinely reported for linear models (LMs) and also generalized linear models (GLMs). R2 has the extremely useful property of providing an absolute value for the goodness-of-fit of a model, which cannot be given by the information criteria. As a summary statistic that describes the amount of variance explained, R2 can also be a quantity of biological interest. One reason for the under-appreciation of R2 for mixed-effects models lies in the fact that R2 can be defined in a number of ways. Furthermore, most definitions of R2 for mixed-effects have theoretical problems (e.g. decreased or negative R2 values in larger models) and/or their use is hindered by practical difficulties (e.g. implementation). Here, we make a case for the importance of reporting R2 for mixed-effects models. We first provide the common definitions of R2 for LMs and GLMs and discuss the key problems associated with calculating R2 for mixed-effects models. We then recommend a general and simple method for calculating two types of R2 (marginal and conditional R2) for both LMMs and GLMMs, which are less susceptible to common problems. This method is illustrated by examples and can be widely employed by researchers in any fields of research, regardless of software packages used for fitting mixed-effects models. The proposed method has the potential to facilitate the presentation of R2 for a wide range of circumstances.