Linear mixed-effects models (LMMs) and generalised linear mixed effects models (GLMMs) have, in recent decades, gained prevalence as statistical tools in biological research. They have replaced blocked, split-plot and hierarchical analysis of variance as the tool of choice for experimental biologists, and have helped countless surveyors of natural systems to measure hierarchical partitions of variation, and to deal with non-independence among their subjects. (G)LMMs are flexible, powerful, well-served by popular statistical software, and relatively easy to build and interpret. However, inevitably, they are also easy to get wrong. As peer reviewers, too often we see (G)LMMs being used naively and without validation.
(G)LMMs differ from simple linear models (LMs) and generalised linear models (GLMs) by incorporating random effects among the explanatory variables alongside fixed effects (Gelman & Hill, 2006; Bolker et al., 2009; Zuur, Hilbe & Ieno, 2013; Harrison et al., 2018). Fixed effects represent variables with intercepts, means or slopes to be estimated. Random effects describe experimental or survey units as members of groups, with these groups drawn from a larger population of other, unmeasured groups. For example, we might measure features of 10 populations of seabirds, but many hundreds of other populations of seabirds will not be measured in our study. Fitting ‘population ID’ acknowledges that each population represents a different group, that observations within a group are likely non-independent (i.e. seabirds in the same population will likely be more similar to each other than to seabirds in other populations), and that we have only measured a subsample of possible groups. The random effect components of mixed effects models infer the variance associated with group membership (Gelman & Hill, 2006; Schielzeth & Nakagawa, 2013). Consequently, the use of random effects is effective when measurements of a response variable within ‘groups’ or random effect levels tend to be more similar to each other than to those in the wider population. By inferring variance among groups rather than group-specific parameters, random effects absorb fewer degrees of freedom than fixed effects and this is exploited in many analyses to absorb real but ‘unwanted’ variation or covariance in the data (Bolker et al., 2009; Harrison et al., 2018). In other analyses, such as those used in quantitative genetics, the relative magnitudes of the variance components are of primary interest, because they provide estimates for the variation in traits explained at different levels of a model’s hierarchy.
The inclusion of random effects in biological regression models is often seen as a panacea for dealing with difficult or structured datasets. One will often read statements in papers that a grouping variable was ‘fitted as a random effect to control for non-independence among groups.’ However, if not used appropriately, (G)LMMs can fail to achieve their purpose, or can yield false positive tests of importance of fixed effects (Schielzeth & Forstmeier, 2008; Forstmeier, Wagenmakers & Parker, 2017; Arnqvist, 2020). The correct specification of random effects is essential to successful analysis, but guidance is often couched in specialist statistical language, code or algebra and can be hard to find. Here we use non-specialist language to highlight the risks of coupling fixed and random effects naively in models. We explain seven common perils and pitfalls (Table 1), use simple data simulations to demonstrate the risk of inappropriate mixed-effect modelling, illustrate the problems caused by these pitfalls and show the reader to diagnose them in their own data and models.
|#1. Anticonservative significance tests at low sample size||Comparing crop yields in split-plot experiments with few replicates||p-value of Wald-like Chi-square test of significance is too low, causing high rates of Type I error||If better replication is not possible, use corrections for small sample size and accept that answers are approximations
Move to statements of credibility based on Bayesian analyses
|#2. Pseudoreplicated with group-level predictors||Infer the effect of maternal traits on the performance of several offspring per mother||Increased Type I error if pseudoreplication is not recognised
Increased Type I error if true replication is small even if pseudoreplication is recognised
|Have a firm grasp of the design level at which true replication occurs, and of the correct mixed-model specification
If better replication of experimental units is not possible, use corrections for small sample size
Move to statements of credibility based on Bayesian analyses with correct specification of design hierarchy
|#3. Too few levels of a random effect||Fitting sex as a random effect||Model degeneracy
Biased estimation of random effect variance
Inaccurate estimation of random effect variance
High error potential for questions related to random effects (less substantial for questions related to fixed effects)
|Fit the variable as a fixed effect rather than random effect
Use a Bayesian model with strong priors for the size of the random effect variance component. Such an approach requires caution and an ability to justify the inclusion of prior knowledge
|#4. Random intercepts when groups vary in their response to a treatment||Testing a relationship between body size and competitive advantage in multiple populations of the same species||Increased Type I error rate when there is variation in slopes between different random effect levels. This is regardless of any correlation between the fixed and random effects||Use of random slopes model instead of random intercepts only|
|#5a. Confounding by cluster||Multiple observation of foraging behaviour are made at a succession of sites to test the hypothesis that foraging rates are associated with disturbance levels. However, sites have different mean levels of disturbance. Both disturbance (fixed effect) and site (random effect) are used as explanatory variables||Biased estimates of fixed and random effect parameters||Use within-group mean centring of variables alongside a group-level covariate|
|#5b. Informative cluster sizes||A model with offspring weight as a response and maternal pathogen load as an explanatory variable and maternal ID as a random effect, if high pathogen loads also cause reduced litter sizes||Possibility of biased estimates for fixed effect parameters if they are correlated with the random effect especially if the model only includes random intercepts||Fit cluster size as a covariate where appropriate (see main text)
Joint modelling of the response variable of interest and cluster size in a multivariate model
|#6. Group means are not normally distributed||An unmeasured variable causes differences between sub-populations
Skewed differences in a trait between sub-populations that are unexplained by fixed effects
|Fixed effect estimates robust unless (a) mis-specification of random effects is extreme or (b) fixed effects are correlated with random effects
Random effect estimates can become less accurate and systematically biased
|Use non-Gaussian random effect distributions (challenging, but made available by use of Bayesian models)
Fit the variable as a fixed effect instead.
Take extra care to check for other violations of mixed model assumptions
|#7. Use of categorical random effects for autocorrelated data||Region is used as a random effect to control for spatial autocorrelation when modelling abundance of a species in response to a range of habitat variables||Poorly fitting model (with inaccurate predictions) and potential of statistical errors unless scale of random effect is correct||Use correlograms to check for covariance in the residuals of the model to ensure that categorical random effect is effective|
Mixed model basics
The fundamental assumption shared by simple linear models and mixed effects models is that residual error for each measurement of the response variable is an independent draw from a Normal distribution with mean zero and fixed variance. (G)LMMs are mixed because they include both fixed and random effects, and linear because they describe the relationship between the observed data and the explanatory variables as the additive contribution of intercepts and linear slopes (of the fixed effects), and deviations from these expectations caused by random effects and residual noise. The adjective Generalised in GLMMs refers to the use of canonical link functions that help deal with non-normal response variables. For both LMMs and GLMMs random effect group means are typically assumed to be Normally distributed on the link scale, although other distributions can be considered (described in more detail below). In general, the choice of whether a variable should be included as a random effect or a fixed effect is best decided by the researcher working on a problem based on a combination of question-driven and practical considerations (Schielzeth & Nakagawa, 2013; Harrison et al., 2018). We expand on other practical considerations in subsequent sections.
As a verbal model, any LMM can be described as a response variable (y) being an additive function of a global intercept, change caused by fixed effects, deviation caused by membership of a random effect category, and any residual variation not explained by the fixed or random effects. This is most elegantly described using statistical algebra (Fig. 1; this will be the only mathematical equation we will present). A simple example of LMM inference is provided in Fig. 2. While it is possible to fit mixed effect models in a variety of software (e.g. SAS (SAS Institute Inc.); SPSS (IBM Corp.); STATA (StataCorp. 2017)), we focus on the fitting of LMMs and GLMMs in the R statistical environment (R Core Team, 2019) using the packages lme4 (Bates et al., 2015) and nlme (Pinheiro et al., 2014). We, along with many of our biologist colleagues, enjoy the open source philosophy and community spirit associated with R. It is also free and extremely powerful.
Perils and pitfalls
In this guide, we identify seven major risks of misuse of (G)LMMs. We explain each of them in simple terms, discuss when they are most likely to cause problems and provide solutions in the form of better-formulated models. Some of the problems stem from an assumption that simple (G)LMMs are a panacea for non-independent data and can be used universally to model difficult datasets. However, complicated hierarchical designs must be treated with appropriate caution, as (G)LMMs are not infallible if specified incorrectly (Arnqvist, 2020). Further issues can arise because these hierarchical models are amenable to the standard toolkit of significance tests, model simplification or multi-model inference taught in undergraduate statistics modules. Analysts, taught by frequentists to infer significance from p-values, commonly struggle to understand how to infer the importance of fixed and random effects reported by (G)LMMs. There is no simple answer here, but simple mistakes can be avoided. The perils and pitfalls we describe are focused on attempts to infer the importance of fixed-effect explanatory variables, but most remain relevant to attempts to understand the importance of hierarchical variance components.
Peril #1: (G)LMM p-values can be anti-conservative
A common worry for the frequentist statistician is the risk that the p-value of a test (i.e. the probability of finding signal as extreme, or even more extreme, than the observed signal, supposing that the null hypothesis is true) might exceed 5% even when the null hypothesis is true. This situation, also known as an inflated type I error rate or being anti-conservative, risks the false conclusion of the importance of a fixed effect explanatory variable (false positive) and has contributed to a replication crisis in some research fields (Forstmeier, Wagenmakers & Parker, 2017). Anti-conservative inference from (G)LMMs can arise when sample sizes are small because maximum likelihood estimates of variance components become biased. This problem is fixed by Restricted Maximum Likelihood (REML) algorithms, which are the default settings for (G)LMMs in most software. However, REML models are not amenable to standard model simplification or tests of significance. It is common practice to convert REML models to Maximum Likelihood and simplify these using likelihood ratio tests. These tests follow chi-square distributions only approximately. As sample size increases, the approximation improves, but for small sample sizes the outcome tends to be anti-conservative. Neither can analysts safely fall back on information theoretic approaches such as the well-known Akaike Information Criterion to compare REML models. AIC is a function of the model’s likelihood and the number of parameters estimated. However, REML likelihoods contain a nuisance factor that is dealt with differently by different software, meanwhile the number of parameters estimated is linked to the number of degrees of freedom associated with the random effects, and that number is hard to define (Bolker et al., 2009). Adjustments for AIC (such as AICc) that cope with small sample sizes are approximations and do not completely deal with this problem.
Guidance on what qualifies as a small sample size is lacking (Gelman & Hill, 2006), but it is safe to assume that some datasets in biology will suffer from these issues. Small datasets are also at risk from over-fitting of models, which can also lead to high rates of false positives (Forstmeier, Wagenmakers & Parker, 2017), and with more complex model structures it can be more challenging to identify situations where overfitting is an issue. These potential issues can arise regardless of the approach taken to statistical inference, although they can be exacerbated by model simplification (Forstmeier & Schielzeth, 2011; Forstmeier, Wagenmakers & Parker, 2017).
A simple simulation illustrates how this issue arises in small datasets. Imagine a simple treatment-control experiment that applies a treatment to half of the members of each of six families. Here, family ID is the random intercept term, and the mean value for the response variable for each family is drawn from a Normal distribution with mean = 0 and standard deviation = 1. We then simulate values for the response variable so that the experimental treatment itself has no effect on values of the response variable (mean = family mean and standard deviation = 1). Here, family ID is the dominant source of variation in the response variable, and the null hypothesis is true and should be accepted. We conducted a poorly replicated version of this experiment, in which only one individual from each family is measured in each experimental group (treatment and control). We then tested for statistical significance of the treatment effect using mixed-effects models and: (a) by determining if the 95% confidence interval of the treatment effect in the full model overlapped zero; (b) a likelihood ratio test that compared Maximum Likelihood models with and without the fixed effect of treatment; and (c) a comparison of the AIC of the models with and without the treatment effect. We used a sigma threshold of 0.05 for approach (b) and considered the effect of treatment to be important for approach (c) when the AIC of the model including the fixed effect of treatment was more than two AIC units less than the null model. All three approaches produced high rates of false positives: in 122 out of 1,000 (12.2%) simulations, 105 out of 1,000 (10.5%) and 100 out of 1,000 (10%) respectively (with identical results from nlme and lme4). This is around double the 5% threshold desired by frequentists and indicates a high false positive rate. The analysis is anti-conservative. The problem of anti-conservatism fades with increasing sample sizes: when each of six families contribute ten control and ten treated individuals, the error rates recorded were 5.9%, 5.7% and 3.3% (5.1% for nlme) respectively. Consequently, while this is a pitfall to be aware of when using (G)LMMs in small datasets, it is likely to be less important with adequate replication.
Peril #2: (G)LMMs do not cure all types of pseudoreplication
Pseudoreplicated experimental designs are those in which fixed effects vary at a hierarchical scale higher than the measured subject. If, for example whole families are exposed to experimental treatment, and family members resemble each other beyond the impact of treatment, then individual members of families do not represent independent measures of the effect of treatment and should not be considered true biological replicates. In an extreme situation where there are many non-independent observations within each of a small number of random effect levels this could cause the number of residual degrees of freedom (those used to infer residual variance) to greatly exceed the number of experimental units to which treatments were applied (number of families). While, traditionally, F-ratio tests would reveal this problem, likelihood ratio tests hide it from the analyst because they use only the degrees of freedom associated with the explanatory variables (Arnqvist, 2020). AIC values also hide the problem by providing no information on degrees of freedom at all. When (G)LMMs are fitted in R this problem is managed by fitting fixed effects at the correct level of hierarchy. This deals with the pseudoreplication pitfall but can result in poor replication of the fixed effects if the number of random effect groups is low (Fig. 3). The model may struggle to partition variance explained by the random effects from unexplained (residual) variance. This results in a marked decline in the accuracy of model inference and increased risk of encountering anti-conservative p-values from likelihood ratio tests (see “Peril #1”) with no way for the inexperienced analyst to check.
To demonstrate, we repeated our simulation from the previous section, but this time applied experimental treatments to whole families (so that every individual in each family was in the same experimental group). We simulated 600 observations in total, then in separate analyses we divided observations among 6, 8, 10, 12, 15, 20 or 24 families (with concomitant reduction in sample size per family, ranging from 100 to 25). Each family was allocated either to the treatment or the control group. In this design, the individuals in each family do not provide independent measures of the effect of treatment. As before, we simulated treatment to have zero effect so the null hypothesis is true and should be accepted. When the number of families was small we observed a high false positive rate, even though the per-family sample size was large: the effect of treatment was statistically significant in >10% of simulations, except when a t-test using the mean and standard error of the treatment effect from the nlme model was used (Fig. 3). The false positive rate then declined to approximately 5% in cases where there more families were sampled (e.g. our simulation runs with 20 or 24 families). Our simulations therefore demonstrate that caution is required in interpreting the statistical significance of group-level explanatory variables when the number of random effect levels is small.
There are additional circumstances where using random effects to attempt to control for non-independence may not be straightforward. Imagine an experiment where we grow two genotypes of wheat in replicate planters containing varying, finite amounts of phosphate to test a hypothesis about the performance of each genotype in different conditions. You would be correct in assuming that measurements from within the same feeding trial are not independent. One potential option here would be to fit planter ID as a random effect to control for this. However, higher uptake by one genotype within an experimental block means less phosphate available for the other, causing the performance of each genotype within a planter to be negatively correlated. A standard ‘blocked’ (G)LMM with planter ID as a random effect would not control for this issue.
The risk of anti-conservatism does not mean that (G)LMMs have no value in pseudoreplicated designs. However, it does mean that the analyst must have a clear understanding of the hierarchical design of the model, in particular whether fixed effects are observation-level (apply uniquely to each observation in the dataset) or group-level (apply uniquely to each level of the random effect) (Schielzeth & Nakagawa, 2013). It is also important to be aware of the number of independent experimental units, the extent and nature of pseudoreplication and the ability of the statistical software to test the importance of signal at the correct level of the design hierarchy. Experimental units, that is those which can be claimed to be independent replicates of the experiment or survey design, must be replicated sufficiently to provide confidence in their inference and to avoid Type I errors (false positives).
Peril #3: too few random effect categories
The standard definition of a random effect is that it should describe membership of a group that is part of a random sample of a larger population of groups. Random effect hyperparameters infer the variance of means and slopes among groups. Inference of any variance parameter requires several independent replicates and improves with increasing sample size of the number of groups. Hence, accurate estimation of random effects can only occur when several groups are represented in a dataset (Harrison, 2014, 2015; Harrison et al., 2018). In practice, however, mixed effects models are commonly used to capture and absorb any non-independence due to group membership. When only few groups have been measured, inference of random effect hyperparameters will be poor; models might be degenerate; and there will be consequences for the correct inference of fixed effect parameters and tests of their importance. For example fitting sex as a random effect in a model implies the choice of calculating a variance using only two values: we wouldn’t infer a simple standard deviation from a sample of two individuals, so we shouldn’t use the (G)LMM algorithm to make the same crude inference. In general, it is suggested to only fit a categorical variable as a random effect if it has 5–6 levels or more (Bolker et al., 2009; Harrison, 2015).
We illustrate this problem in Fig. 4 using simple data simulations. A sample of 200 individuals is subdivided into between two and 40 groups. A single covariate has a positive effect on our response variable. Full code for the example is provided in the Supplemental Material. Estimates of random effect variance are biased small when there are fewer than six or seven groups (Fig. 4A), with the greatest problems caused by having only two or three groups. The inaccuracy of estimates of the random effect variance shows an exponential decline. This means that models tend to underestimate the standard error of the fixed-effect covariate’s slope when there are too few random effect levels (Fig. 4B), indicating increased risk of Type I (false positive) errors when there are fewer random effect levels.
Peril #4: effect of predictor varies among random effect categories
Many studies that use (G)LMMs use a random intercepts model, in which the random effect measures or controls for variation among group means. However, there is no guarantee that this is a sufficient control for variation among groups, especially when modelling a covariate whose effect may itself vary among groups (Schielzeth & Forstmeier, 2008; Barr et al., 2013; Bell, Fairbrother & Jones, 2018). The use of random slopes models is advisable in these contexts (Barr et al., 2013). Random intercepts models risk anti-conservative tests of importance, and typically predict responses of unsampled groups worse than models that include random slopes (Bell, Fairbrother & Jones, 2018). To provide an ecological example, we simulated a relationship between oxidative stress and parasite burden in 20 populations of wild amphibian (n = 20 frogs measured per population), where parasite burden is a non-integer measure of genomic equivalents of a parasite. We allowed both mean parasite burden (random intercepts) and the strength of relationship between parasites and oxidative stress (random slopes) to vary by population. We also randomly assigned populations to a two-level factor as either ‘treatment’ or ‘control’, so having no effect on parasite burden. We fitted a ‘maximal’ model with Gaussian error structure allowing for an interaction between oxidative stress and treatment, and containing either only random intercepts for population ID, or both random intercepts and random slopes for oxidative stress given population. After 10,000 iterations, when fitting only random intercepts, the model erroneously estimated the treatment * oxidative stress interaction to be significant (95% confidence intervals not crossing zero) in 30% of cases. Fitting a random slopes model reduced the incidence of Type I (false positive) errors to 6.7%, far closer to the desired 5% rate. For further details on this phenomenon, and a more detailed set of simulations, see Schielzeth & Forstmeier (2008). Clearly, not including random slopes results in elevated type I (false positive) error rates.
An important risk of random intercepts models is that unusual groups can cause false inference of whole-population effects. Imagine a test for a linear relationship between body size and the size of a status signal in a hypothetical bird species consisting of 10 different subspecies. There is a positive body size-signal size relationship for only one of these subspecies (Fig. 5A). A random intercepts model may conclude that there is a positive effect of body size on status signal size across all subspecies if the relationship in that single subspecies is sufficiently strong (Fig. 5B). In contrast a random slopes model that controls for differences in this relationship among subspecies is likely to detect no overall effect, but also show that the slope for one subspecies was unusual. The difference between the random slopes and random intercepts models does not occur because of differences in their estimates of the effect of body size (Fig. 5C) but instead because the random intercepts model consistently underestimates the standard error around this estimate (Fig. 5D). Note that often random slopes models can return low estimates of variance for the among-group slopes, but this is to be expected if there is only one group with a strong relationship with the response. This is especially the case if the random effects sample size is large. Measuring the ‘importance’ of random effects based on these variance components is a contentious issue (Harrison et al., 2018), but random effects shouldn’t automatically be immediately discounted/removed just because a variance component appears negligible.
Peril #5: correlations between fixed and random effects, and informative group sizes
Mixed models assume that values of fixed effect variables are independent of the groups (clusters) used as levels of a random effect. When this assumption is violated, the models suffer ‘confounding by cluster’ (Seaman, Pavlou & Copas, 2014a). Confounding by cluster will therefore be a potential problem when there is both within- and between-group variation in the values of an explanatory variable. It can lead to misleading estimates for fixed effect parameters and biased estimations of variance components (Neuhaus & McCulloch, 2006). A number of potential solutions have been suggested (Seaman, Pavlou & Copas, 2014a), although one of the most accessible and intuitive is to decompose the effect of a fixed effect variable into between-group (and therefore group-level) and within-group (observation-level) covariates (Neuhaus & McCulloch, 2006). For example a study determining the relationship between fitness and body size in a population made up of multiple social groups could contain a group-level effect of mean body size, and an individual-level effect that is group-mean centred, so that it describes the size of that individual relative to other individuals in the group.
A similar problem can arise if the cluster/grouping size (number of samples for each level of the random effect) is correlated with one or more fixed effect variables (Seaman, Pavlou & Copas, 2014b). For example if modelling the association between maternal stress (response variable) and offspring weight at fledging (explanatory variable) in a passerine bird, clutch ID would typically be included to control for variation in offspring weight among different breeding attempts (as might be caused by genetic differences, parental effects or the shared environment). However, if females that are more stressed tend to lay smaller clutches then the size of the cluster is informative. Informative cluster sizes can result in biased inference, especially when fixed and random effects are correlated (Neuhaus & McCulloch, 2011). This is a particular problem for models that only include random intercepts, where failing to account for informative cluster sizes can lead to biased estimates for the intercept. However, for most covariates model estimates are unaffected by the presence of informative cluster sizes (Neuhaus & McCulloch, 2011). One potential solution for dealing with informative cluster sizes is by including cluster size as a covariate, however this is not a sensible choice when cluster size lies on the causal pathway linking a particular explanatory variable to a response variable (Seaman, Pavlou & Copas, 2014a): inclusion of the cluster size as a fixed covariate risks masking the real influence of the main explanatory variable. Another more complex approach is to jointly model the response variable of interest and cluster size (Dunson, Chen & Harry, 2003; Chen, Zhang & Albert, 2011; Seaman, Pavlou & Copas, 2014a).
Peril #6: random effect category means are not normally distributed
In many situations random effect means or slopes deviate from a Normal distribution. They might be clustered along the y-axis, or might be skewed or heavy-tailed. Skew and kurtosis are rarely considered by biologists, but are important when comparing variances among samples (Hosken, Buss & Hodgson, 2018). Typically, the random effect hyperparameter used in (G)LMMs is the standard deviation of a Normal distribution. It is possible to specify alternative hyperparameters and allow random effects to have non-Normal distributions (Zhang et al., 2008; Molenberghs et al., 2010, 2012; Fabio, Paula & de Castro, 2012) but this requires non-standard modelling algorithms. In general, both LMMs and GLMMs have been found to be impressively robust against misspecification of the random effects distribution (McCulloch & Neuhaus, 2011; Neuhaus, McCulloch & Boylan, 2013; Schielzeth et al., 2020). The estimates of fixed effect parameters for individual-level variables are particularly robust (McCulloch & Neuhaus, 2011), while estimation of random effects and variances is more susceptible to misspecification (McCulloch & Neuhaus, 2011). However, when fixed effects are correlated with random effects, and if other assumptions of mixed models are not met, then misspecification of the random effects distribution can influence parameter estimates (Neuhaus & McCulloch, 2011). Diagnostic tools such as those found in the R package ‘sjPlot’ (Ludecke, 2019) allow users to diagnose the validity of their assumption of normality of random effects, and should be used where appropriate. While LMMs and GLMMs are typically robust to misspecification, other approaches are available when these assumptions are violated, for example the application of mixture models (Hamel, Yoccoz & Gaillard, 2017). Direct comparison of choices of random effect distributions can be made using Bayesian mixed effects models coded in standard software such as JAGS (Plummer, 2003) or Stan (Carpenter et al., 2017).
Peril #7: random effect categories used as a proxy for covariance structure
It is not unusual for non-independence among residuals, caused by spatial, temporal or phylogenetic autocorrelation, to be modelled using categorical random effects (e.g. region, year or genus). Despite increased prevalence of regressions that explicitly model covariance structures (Housworth, Martins & Lynch, 2004; Dormann et al., 2007; Miller, Franklin & Aspinall, 2007; Hadfield & Nakagawa, 2010; Ives & Helmus, 2011; Rousset & Ferdy, 2014), many researchers elect to control for these dependencies with categorical variables as an alternative. While some coarse control for spatial (or temporal) structure is better than none at all, the success of using a categorical random effect can vary depending on the nature of the true covariance structure in the data. First, random effects do not control for all types of non-independence and are useful only when there is positive autocorrelation (i.e. measurements closer together in time or space tend to be more similar). Second, the success of using a categorical proxy for a covariance structure will depend on how the granularity of the effect used (e.g. site ID vs. region ID) compares with the scale of any autocorrelation.
We demonstrate here that the success of categorical proxies for continuous covariation depends on how the granularity of the random effect compares with the scale of any autocorrelation. We simulated two Gaussian fields that influence the residual error in the relationship between a single explanatory variable (Temperature) and single response variable (Height). The first (Fig. 6A) varied at a much finer scale than the second (Fig. 6D). We varied the slope of the relationship, so that we could examine the impact on model performance at a various effect sizes. There were 320 measurements in total, occurring in eight regions that each contained four sites, with 10 individuals measured per site. We fitted three models: one directly modelled spatial covariance in the residuals (using Generalised Least Squares); one using site as a categorical random effect; and one using region as a categorical random effect. For the model in which the spatial field varied at a finer scale, model estimates from the models that used site as a random effect were in much closer agreement with the explicitly spatial model (Fig. 6B) and much more precise (Fig. 6C) than those that used region as a random effect. In contrast, when the scale of the spatial field was broader, the accuracy and precision of model estimates was much more similar (Figs. 6E and 6F). Biases in the accuracy and precision of model predictions will affect Type I (false positive) and Type II (false negative) error rates. This helps illustrate the benefit of selecting a categorical effect to control for spatial or temporal structure in the data that is as well matched to the autocorrelation in the data as possible.
Detecting and resolving problems with mixed model estimation
First, we recommend having a clear idea of the structure and hierarchy of the model. Identifying categorical variables with too few levels for random effect estimation can help avoid Peril 3, while identifying the level of the hierarchy that fixed effect variables apply at (observation-level vs group-level) can help identify situations where there is a risk of Peril 2 having an impact. Similarly, a clear idea of the hypothesis and model structure can help identify scenarios where a random slopes model might be more appropriate than a random intercepts model (Peril 4).
Second, we emphasise the importance of data exploration (Zuur, Ieno & Elphick, 2010). Plots of the raw data can help identify unusual random effect categories (helping to avoid Peril 6), small sample sizes (Peril 1) or confounding by cluster and informative cluster sizes (both part of Peril 5). Similarly, raw data plots might help provide an initial idea of the scale of any spatial or temporal structure to the data and so be informative in deciding an appropriate random effect (Peril 7).
Third, we highlight the value of conducting full model checks (Zuur & Ieno, 2016; Harrison et al., 2018). Plots of residuals for each level of the random effect are important in identifying heteroscedasticity in the residuals between levels of the random effect, or relationships between residuals and fitted values that necessitate random slopes models (Peril 4). Semi-variograms check the need for explicit modelling of covariance structures to avoid Peril 7 (Fletcher & Fortin, 2018). The simplest method to assess the extent to which the random effects distribution differs from normal (to avoid Peril 6) are quantile–quantile plots. However, various other diagnostic tools are available (Drikvandi, Verbeke & Molenberghs, 2017; Efendi et al., 2017). We demonstrate a comprehensive but simple approach to model checking in the Supplemental Material. We provide code to allow users to be confident in generating these checks themselves as well as using functions provided by existing R packages. New R packages such as DHARMa (Hartig, 2020) are making these model checks more available and accessible even for more complex GLMMs.
There are also now R packages that make more sophisticated modelling approaches available to a wider audience. For example brms (Bürkner, 2017) provides an interface to the Bayesian statistical model fitting software Stan (Carpenter et al., 2017). Users can exploit coding syntax similar to lme4, and an array of model specifications are available that deal with various pitfalls described here. Similarly, glmmTMB (Brooks et al., 2017) provides software to facilitate the fitting of more complex error distributions and correlation structures using similar syntax to lme4.
(G)LMMs are reassuringly robust to some of the individual pitfalls we have described here Schielzeth et al. (2020). However, there is very little understanding of the combined impact of multiple violations of the core assumptions: there is plenty of scope for simulation studies of the power and anticonservatism of mixed effects models. The pitfalls described here exist and are prevalent in the biological literature, with little opportunity for readers to check the validity of published models and results. Hence, raising awareness of these potential pitfalls and considering them together can help researchers use mixed models more assuredly and avoid pitfalls that impact on their statistical inference.
Mixed modelling approaches are firmly embedded as state-of-the-art for the analysis of biological data. As these methods become available to a growing user base it is necessary to reveal the perils and pitfalls associated with them (Arnqvist, 2020). Often with biological datasets it is not possible to meet the statistical assumptions of these models perfectly and it may be necessary to make compromises in model design. We have provided guidance on a set of typical perils and pitfalls by providing insights from the statistical literature and illustrating key points using simulated case studies and examples. While (G)LMMs can be robust to some of the perils we describe (Schielzeth et al., 2020), there remains little understanding of their combined impacts. Readers can only assess the quality of inference from mixed effects models if their hierarchical structures, levels of true replication, and checks of validity, are described clearly and honestly. This review will help readers be more aware of some of the key perils in mixed model design and so improve statistical inference when testing biological hypotheses. We hope that by providing an overview of these perils, we can help researchers feel better informed and more confident that they are using mixed modelling approaches to draw correct conclusions from their data.
Simple examples of linear mixed models.
Code used to produce Figure 2
(G)LMM p-values can be anti-conservative.
R code for Peril #1
Effect of predictor varies among random effect categories, amphibian example.
R code for the wild amphibian example in Peril #4
Effect of predictor varies among random effect categories, status signal example.
R code for the body size and status signal example in Peril #4
Random effect categories used as a proxy for covariance structure.
R code for Peril #7