As an explanatory method, SEM requires the scientist to play an active role in the model evaluation process. A priori scientific knowledge is essential for the construction of the initial models. However, there may be a tendency for those beginning to use SEM to imagine that model evaluation, based on the data, is a tightly-scripted process defined by the rules of statistics. Earlier treatments of SEM tend to reinforce this impression. This is perhaps true of my own writing (e.g. comparing the presentations in Grace 2006 to the current paper), but also the writing in more general treatments of SEM (Kline 1998, 1^st Edition compared to Kline 2016, 5^th Edition). Some of the shift in recommendations reflects a broader shift in the view of the role of p-values and strict hypothesis tests. Experience with SEM applications to real-world problems also teaches us that the exercise of scientific judgement is an essential part of model evaluation.

The goal of model selection is not simply to describe the relationships in data. In my view, the goal is to balance twin objectives. First is the narrow task of evaluating the model-data inter-relationships. We must address the specific question, “What do these data say about the hypothesis?” SEM philosophy, however, imagines a sequence of studies and a process of sequential learning (Grace and Irvine 2020). Our initial model for each analysis represents an accumulation of knowledge from prior investigations. The evidence obtained from the analysis then updates our understanding with new information. We should assume, I feel, that there will be additional studies to follow that will test and strengthen our understanding. This looking forward motivates us to a second objective, which is to select a final model in this study that can serve to help us construct the initial model for the next study. These twin objectives motivate us to balance the reliance on empirical evidence in the current data sample against theoretical knowledge about the underlying mechanisms. Here, I describe more specifically the role of the scientist, as this topic is rarely covered in explicit fashion (e.g. Larson and Grace 2004; Grace and Irvine 2020.

The initial model construction process in SEM relies heavily on investigator knowledge. The reasoning process adopted during model construction (Grace and Irvine 2020) needs to be maintained during model evaluation as well. It will not always be necessary to explicitly consider alternative models. There is an aspiration in SEM that, through sequential studies, one will reach a confirmatory stage where new data may refine estimates, but not change our minds about the causal structure of the hypothesis. This paper addresses the more typical case where model refinements are proposed and competing models considered.

A Need to Support and Defend Critical Assumptions – There is a certain minimum amount of a priori knowledge that is required in order to use SEM. SE models include so-called “untestable” assumptions, along with assumptions that can be falsified by an appropriate dataset. The most fundamental untestable assumptions are the directions of the arrows. Often, in ecological studies, the investigator is able to justify arrow directionality. More challenging is for investigators to justify things that are omitted from their models. Of course, models must limit their scope to the essential components. There are rules relating to what can and cannot be omitted. First, only include variables that are essential to the modeling objectives. Often scientists attempt to include all measured variables and produce models whose complexity exceed the capacity of the data sample size (too many parameters per sample). Second, omitting variables that have strong effects on two or more of the variables of primary interest can lead to confounding. When very strong confounding relationships are omitted, they have the potential to bias conclusions.

For links not included in the initial model, post-estimation evaluations should reveal whether these assumptions need to be reconsidered. For direct links, these are straightforward to detect and include. However, we should not ignore the possibility that errors will be non-independent. Correlated errors are definite indications of omitted confounders. Finding error correlations may spark a need to consider model modifications. It is wise to consider how one might interpret such findings based on a priori knowledge, as these represent factors being omitted from explicit inclusion in the initial model.

Investigator’s Opinion of the Strength of Theory versus Strength of Data – A point that is rarely discussed outside of the sphere of Bayesian statistics is how to weight a priori scientific knowledge against the information content of a data set. This omission exists despite the fact that, in many ecological studies, analyses are based on very limited samples. In cases where there is a large and representative dataset for use in an analysis, one should be prepared to consider the data-derived estimates as the final arbiter for drawing inferences. In some cases, our a priori knowledge may be stronger than the dataset available for modeling.

A broad view of the quantitative sciences must recognise that we aspire for our models to transition over time from assumption-testing to assumption-based. Numerous sub-disciplines within ecology rely on assumption-based models. So-called ‘mechanistic models’ incorporate processes that operate on biological systems with enough regularity that the form of the model is accepted as given and data are used purely to estimate the parameters. Population models often fall into this group. For this model type, some of the processes may be of known functional form, while others may be of unknown form. When studying multi-species ecological communities, we often encounter mechanisms that are contingent on so many factors that relationship forms cannot be taken as given (e.g. effects of species additions or removals; Smith and Knapp 2003).

The preceding material is presented to make two important points relevant to model evaluation and selection within SEM. First, when alternative models are suggested, based on empirical results, we should avoid constructing alternative models for consideration that we know are false representations of the system. Perhaps a birth rate estimate is low and its 95% confidence interval includes a value of zero. Do we prune the model to adhere to the principle of parsimony? That would mean we might end up presenting a final model that, by omission, suggests that births are not a contributing factor for population size. Scientific logic would suggest that we should not prune in this case, but what are the consequences? I will address this question in the context of our illustrative example in the section below. In summary, the rule I would suggest is for the investigator to not include models in your comparison set that you, as a scientist, are not willing to defend.

Historically, the use of p-values came into widespread use as a part of the machinery for null-hypothesis testing. P-values have traditionally been used for dichotomous decision-making and have been central to the practical application of statistical methods. Within a WOE paradigm, p-values can be used as continuous quantitative indicators without their being used as strict cutoffs. The case for this type of use of p-values has been recently articulated by McShane et al. (2019) who argue, “We propose that the p-value be demoted from its threshold screening role and instead, treated continuously, be considered ... as just one among many pieces of evidence.”

As mentioned in the Introduction, for SEM applications that utilise global estimation methods (e.g. LISREL, Mplus, AMOS or lavaan), model estimation returns an initial set of measures that quantify the overall correspondence between observed and model-implied covariances. Immediate focus is directed to the Χ² statistic, summarising model-data fit and its p-value. The p-value, in this case, has a counter-intuitive meaning in that it represents the probability that the observed data deviate from model expectations, which would imply the model structure is inappropriate for obtaining estimates from the data. When conducting SEM, there is an immediate decision that has to be made after the initial model is estimated, which is to decide whether there are one or more important links omitted. If there are, the reported parameter estimates are not to be trusted. This need to make sure the network is not missing important links has led to a history of reliance on dichotomous decision-making and this is perhaps unavoidable. The next section will discuss alternative indices for global fit assessment, but regardless of the fit index used, the question still arises, “Should we keep the original model or create a more complete one before we proceed?”

There are a number of factors that limit our ability to provide an omnibus model evaluation using the Χ² statistic. For example, the continuous increase in statistical power with increasing N (sample size) of course means appreciable differences between data and model could be missed when N is small, but trivial differences could be flagged when N is large. Additionally, it is well documented that the Χ² statistic can hide various types of mis-specification simply because it is a summary statistic for the entire model (Steiger 2007). As a result of these problems, a great many alternative measures of global model fit have been proposed and evaluated.

Kline (2016) provides an overview of the approximate fit indices developed for SEM. Most of these are not proper for use in significance tests, but continuous measures of model-data correspondence. That said, the urge to perform model sufficiency testing has led to various attempts to create thresholds for approximate fit indices (e.g. Hu and Bentler 1999). Kline (2016) places approximate fit indices into three primary categories, (1) absolute fit, (2) comparative fit and (3) parsimony-adjusted. Information metrics like AIC, which are technically model comparison measures, are discussed as a separate topic in a later section.

Regarding approximate fit indices, it is probably true that some are, on average, better than others. However, simulation studies indicate that the capacity to detect mis-specifications based on recommended thresholds depends on the particular mis-specification (Marsh et al. 2004). Some authors have even suggested such indices and associated thresholds not be used at all (Barrett 2007), while other suggest they do have a role to play (Mulaic 2009). The current practice amongst SEM users, particularly those in the social sciences using latent variable models, has come to be pluralistic and individualistic, with each investigator potentially relying on a unique combination of pieces of evidence. The fundamental problem with the approaches considered is that there is no clear way to combine the different types of evidence.

Under the WOE approach, I will demonstrate in this paper approximate fit indices can be useful measures to report. Kline (2016) suggests the following should be reported: (a) the Root Mean Square Error of Approximation (RMSEA) and its 90% confidence interval, (b) the Comparative Fit Index (CFI) and (c) the Standardized Root Mean Square Residual (SRMR). Simulation studies have shown that none of these indices is sufficient for detecting all types of mis-specifications. Each provides some quantification of evidence nonetheless and a description of how they are judged is presented below.

The second phase in evaluating models after first examining global fit measures is often to search for indications of what changes could be made to improve model-data concordance. Specially designed for this purpose are so-called modification indices (MI). All global-estimation-based software packages, with which I am familiar, report this information upon request. The critical role of the investigator’s scientific judgement comes into sharp focus once one tries to make sense of the MI table provided for a model that is mis-specified.

MI values are expressed in terms of the drop in the Χ² statistic that would be observed if a link were added to the model. The categories of possible additions include, (a) regressions, (b) latent variable loadings, (c) error correlations and (d) variance constraints. The modification indices are not arrived at by actually fitting alternative models. Rather, they are approximations and therefore do not always correspond to the changes that will be observed.

Perhaps the best way to gain some intuition about the challenge MI values attempt to overcome is to look at the raw materials for computing evidence of mis-specification, which are the residuals. In this case, the residuals are not those between predicted and observed individual data values, but instead, between the observed and model-implied variance-covariance matrices. Requesting to see residuals in a standardised metric will illustrate where model-implied and observed matrices are most discrepant. Because As the parts of a model are intercorrelated, there are many different model changes that might be implied. From a very practical standpoint, the investigator must realise that any change in the model can potentially resolve many of the listed modification possibilities. Therefore, one should decide on a single addition to the model before re-estimation. It is essential that the chosen modifications make substantive sense, because they must explain to the reviewers the scientific basis for the modifications of their initial model (see Grace 2006 for an in-depth discussion of this issue).

When working with models having latent variables with multiple indicators, MI tables sometimes return no usable advice, even though global model fit is poor. In this case, it becomes essential to consult the residual matrix unless theoretically predefined alternative specifications are available. While matrices of residuals provide a more undistilled source of information, they are commonly a fundamental source of evidence for selecting alternative models for consideration.

As with all other types of fit measures, information-based measures have a long history of use in SEM. This is a complex topic that I will treat lightly because the jury is still out on whether universally-applicable recommendations are even possible. Also Complicating things is also the sheer variety of information metrics that have been proposed for use. Fortunately, a recent review of past studies and set of simulation studies by Lin et al. (2017) provide a basis for summarising the topic for SEM users.

Two types of information measures have captured most of the recommendations, AIC-type indices and BIC-type indices. The Akaike Information Criterion (AIC) was proposed for use in 1974 (Akaike 1974), while Schwarz (1978) proposed a Bayesian alternative (BIC). In Burnham and Anderson (2002), the foundational arguments were laid out for using AIC within a multimodel inference system as a replacement for p-value-based null hypothesis testing. Much discussion of this index and comparisons with other approaches, including BIC, have taken place and a concise summary of the discussion can be found in Brewer et al. 2016) and Aho et al. 2014). The result of all this attention has led to widespread adoption of information-based multimodel comparisons in the natural sciences. The separate history of discussion of the same issues amongst SEM practitioners has led to a distinct body of literature where practices and recommendations vary widely. One lack of overlap relates to the sample-size corrected version of AIC, known as AICc. Since it is not theoretically justified for multivariate models, it has not been included in SEM studies. For univariate models, it has been shown to outperform AIC under small sample sizes and is the default index for many studies in the natural sciences.

In their book, Burnham and Anderson (2004) suggest models separated by more than 2 AIC units could be seen as distinct, while later (Burnham et al. 2011), they suggest 4-7 units might be a better criterion. As I will show below, multimodel inference should use the full set of models evaluated for summarising the evidence for any one of the set.

In this paper, I do not wish to attempt to propose a definitive answer to the question of which information index is best nor consider the detailed studies and arguments association with that question. My intent is to show how the various types of evidence, associated with SEM, can be used to build up a set of candidate models for comparison and how information measures can be used to assist in the comparisons. For that purpose, I will rely on the following synoptic view, taken from various sources.

The relative performance of different information measures has been shown to vary with a number of factors, including (a) sample size, (b) the composition of candidate model sets, (c) the magnitude of effects to be detected and (d) heterogeneity in the data. I will try to summarise our current understanding (and my own experience) in a few summary statements:

1. The behaviour of AIC versus BIC indices can be anticipated by the fact that the latter group imposes stronger penalties for model complexity. Variant types of AIC (e.g. Consistent AIC - CAIC) and of BIC (e.g. Haughton's BIC - HBIC and sample-size adjusted BIC -ABIC) all have different types of behaviour. The performance of different indices depends strongly on the above factors. There is no single indicator that is superior across all assumptions and conditions.
2. There are two key questions for the investigator to consider that influence the guidance to take home from simulation studies. First, is the true data-generating process complex and with tapering effect sizes? Second, is it likely that not all the important variables in the true model are in your candidate models?
3. If you answer yes to both questions in number 2, AIC and ABIC are perhaps the best choices up to N = 400. Above that, HBIC is a good choice.
4. If your answer to only the first question is yes, AIC remains a consistent performer up to N = 300, but ABIC is not as consistent.

In this paper, my focus is on globally-estimated models where the investigator must contend with multiple forms of evidence encountered within a sequential evaluation of overall model fit and individual links included in the model. However, many investigators use local estimation methods (e.g. Lefcheck 2016). For this reason, I briefly describe methods for d-separation (d-sep) testing here. Further, Kline (2016) (Chapter 11) discusses the potential for including evidence from local fit indicators, such as d-sep tests, in the evaluation of globally-fit models.

Pearl’s redescription of SEM in foundational terms, referred to as the Structural Causal Model (Pearl 2000), includes the proposal that the testable implications of models can be expressed in terms of d-separation tests. Shipley (2000) subsequently developed formal d-sep tests that could be used for empirical evaluation of conditional independence claims in recursive path models. Initially, Shipley’s test statistic was based on p-values, which were used in conjunction with the testing of individual independence claims. They were also used in developing an overall test statistic, the C score, which is a function of the sum of p-values across the entire set of independence claims evaluated.

In 2013, Shipley subsequently developed a version of his method based on AIC (Shipley 2013). He demonstrated that, for a set of equations whose parameters are estimated using maximum likelihood, the C statistic equates to a maximum likelihood quantity as long as null probabilities, from which a C statistic is computed, are maximum-likelihood probabilities. Fulfilling this requirement makes it possible to compute AIC from a C score. He went on to show how to apply the AIC statistic to model comparisons based on d-sep criteria.

Most recently, Shipley and Douma (2019) have revisited the use of AIC in conjunction with locally-estimated model comparisons. They pointed out that the “d-sep AIC”, which is the name they suggested for their original computation, only captures evidence contained within the conditional independence tests and not within the entire model. To remedy this limitation, they developed a “full-model AIC” that takes into account both the causal topology of the model and the parameter estimates.

Model 1 (Fig. 1) provides our starting point for the selection of a explanation for the data. Covariance matrix input and Model 1 code are in Table 2.

Estimation of Model 1, using lavaan, returns the measures of overall model fit shown in Table 3. We can see that lavaan converged rapidly and without warnings. My discussion of results will follow the proposed sequence of examinations described above.

1. Consideration of Sample Size – Since N = 150, all of the fit measures presented can be interpreted in a fairly straightforward fashion.

2. Examination of Model Χ² Statistic, Model Degrees of Freedom and associated P-value –While the p-value returned is above the criterion of 0.05, it can be anticipated at a sample size of 150 that we have sufficient statistical power to detect modest effect sizes. For this example, it is appropriate to assume that the true model contains a wide range of effect strengths, including some of scientific interest, but of modest size. With a p-value of 0.058, it would be naïve to simply accept this model without looking any further.

3. Examination of Select Approximate Fit Indices –

a. RMSEA is below 0.10, the lower CI boundary is 0.0 and associated p-value is 0.153. All these values suggest approximate fit.

b. CFI is estimated to be 0.978, which implies that we are probably not missing any large effects (assuming no interactions, as I do for this illustration).

c. SRMR is 0.055, well below the warning level of 0.10.

d. Summary: This evidence suggests that when model-data discrepancies are average across the whole model, there is reasonable correspondence. However, this level of fit could be the result of averaging many equal-sized minor mis-specifications OR averaging many areas of the model with very close fit and a few important model-data mismatches. The limitation of global fit measures is their inability to distinguish these two possibilities.

Examination of Modification Indices and Covariance Residuals – For now, I forego presenting a matrix of standardised residual covariances as their interpretation requires some experience. My typical process is to first examine modification indices and work with those, resorting to an examination of residuals, if it seems necessary. Seven modification suggestions are returned in this case (Table 4). Immediately one recognises that the MI value is identical for all of the suggested changes. All the suggested changes involve the densities of species A, species B or both at time 1. In fact, changes 1, 2 and 5 suggest adding a link between BioA1 and BioB1. Changes 3, 4, 6 and 7 are suggestions to add effects pointing from time 2 to time 1, which are not scientifically plausible. So, the modifications suggest we consider what kind of process could jointly influence the abundances of species A and B at time 1 (other than dependence on stem density). The expected parameter change values for the set of changes under consideration are all negative. This means we should be thinking of processes that could cause a negative association between the two species at the beginning of the study. The investigators imagined several, including (a) different establishment histories for the two biocontrol agents within the landscape sampled, (b) different habitat preferences or (c) some previous interaction between the species, such as competition. All of these mechanisms would best be represented by an error correlation between BioA1 and BioB1. This alternative model (Model 2) is shown in Fig. 2 and was fitted to the data for further evaluation (step 5).

Figure 2.  

Model 2, which includes an error correlation between species A and B at time 1 (parameter 12).

Fig. 2 represents our new model for evaluation. The modified lavaan codes is shown in Table 5. To consider the evidence in support of this model, we must estimate the new model and repeat the proposed sequence of steps. Less explanation is needed for the second model evaluation, so I condense steps.

Steps 2-5: Examination of Global Fit Measures and Consideration of Additions to Model 2 – The Χ² dropped from 9.125 to 1.155 (a decline of 8.03) and its p-value rose from 0.058 to 0.764 (Table 6). The RMSEA estimate is now 0.0 and CFI is estimated at 1.0, while SRMR shrunk from 0.055 to 0.013. Since the new Χ² is well below 3.84, there is not enough remaining model-data discrepancy to justify any further additions at this point. Therefore, there is no reason to examine modification indices for this revised model. It is worth noting that AIC dropped from 2629.654 to 2575.513, a decline of 54.141, a decisive magnitude of improvement.

Step 7: Considering Simplification for Model 2 – We now turn to judging support for the links included. The information reported by lavaan that is most helpful at this point are the statistics associated with individual parameters. These are presented in Table 7. There are 18 parameters listed, one of which is treated as fixed (the variance of Stems1). Stems1 is our only exogenous variable. In lavaan, exogenous variances are assumed to be those in the observed variance-covariance matrix by default, though that default can be relaxed. As for the rest of the parameters, we should, at this point, consider whether the signs of the parameters correspond to hypothesised mechanisms associated with those parameters. Based on Table 1, we expect negative effects for links 4, 6, 9 and 11 and positive effects for links 2, 3, 5, 7, 8 and 10. Link 1 could be either positive or negative, depending on the stage of establishment of the plant population. In this instance, we expect link 1 to capture negative density dependence, but the data will be the final determinant since there is no theoretical guarantee. The coefficients in Table 7 do not all conform to expectations. The most notable exception is for link 4 in Model 2. Parameter b4 is positive and its p-value suggests (based on experience) some degree of support. Importantly, link 4 is one of the parameters in our model of greatest interest relative to the question of whether biocontrol is being successful. The same parameter for the other biocontrol species (b9) is seen to be negative with a p-value of 0.002, conforming to expectations. At this point, we must decide how to proceed and the investigators, involved in the original study, chose to create a new model for further examinations.

A new model for evaluation is presented in Fig. 3. The lavaan code is given in Table 8.

Figure 3.  

Model 3, with link from BioA1 to BioB2 removed.

Steps 2-5: Examination of Global Fit Measures and Consideration of Additions to Model 3 – The fit statistics for Model 3 are similar to those for Model 2, but with even closer fit (full results not presented to economise on space). The Χ² is now 0.133 and p-value = 0.988. All other fit statistics suggest there are no other important links missing from this model.

Step 7: Considering Simplification for Model 3 – We now turn to an examination of the parameter-specific statistics for Model 3 (Table 9). For model simplification, we now look at the parameters with the least support (highest p-values). As always, we do not make model modifications we do not wish to defend later. Parameter labels now correspond to the numbered links in Fig. 3. Parameter b6 has the highest p-value, 0.828, which suggests very weak support for that process. This parameter represents an effect of BioA1 on BioB2, which was considered to be an open question at the beginning of the analysis. The a priori hypotheses being considered is that species A has a competitive effect on species B, which would anticipate a negative effect. The returned estimate is near zero and positive. All results suggest we should remove this link from our model, yielding Model 3B (Fig. 4).

Figure 4.  

Model 3B.

Model 3B, Step 7: Considering Simplification for Model 3B – Model 3B was created by removing link 6 from Model 3. This is done by setting parameter b6 to zero (Table 10). We now re-examine p-values for those showing weak support (Table 11). We now see that parameter b11 has a p-value of 0.111. Parameter b11 corresponds to the link in Fig. 4 from BioB1 to BioA2. As with parameter b6, which we already fixed to zero, with link 6 we are looking for evidence of a cross-year competitive effect of species B on species A. It is entirely possible for competition to be asymmetric, so failing to find the effect of species A on B (b6 set to zero) does not automatically preclude an effect of B on A (b11). Still, in this case, setting b11 to zero seems like the next step, which leads to a model that is simplified further, Model 3C (not shown, but presented in Suppl. material 1).

Model 3C, Step 7: Considering Simplification for Model 3C – We now direct our attention to Table 11 and parameter b7, the effect of Stems1 on BioB1, which has a p-value of 0.072. Here, we encounter a parameter with marginal empirical support but with very strong theoretical support. The investigators (Larson and Grace 2004) made the decision to leave this link in all models because knowledge of the biology and evidence from the field, guarantee that the biocontrol beetles depend on the abundance of the invasive plant. Both data and field observations (as well as subsequent studies with longer time courses, Larson et al. (2008)) confirm this process, but contribute to an understanding of how the dynamics of beetles induces substantial variability in the measured association. Later, I will show the consequences of retaining b7 as a free parameter (or setting it to zero) for other model parameter estimates. This will give the reader a feel for what retaining a weakly-supported link implies. For now, we leave link 7 to be freely estimated and look further at the output. The only remaining parameter with marginal support is b4, the error correlation between BioA2 and StemChg12 (p = 0.031). This level of support is usually indicative of support for retaining a link. To evaluate this expectation, I estimated one additional model, Model 3D, in which b4 == 0. Results for Model 4 show no signs of mis-specification and no obvious opportunities for justifiable modifications. This completes our process of creating alternative models.

In this situation, we must decide which of the models that have been estimated are scientifically defensible. Model 1 was found to be obviously mis-specified due to lack of empirical support and is not a contender for model selection. Model 2, while exhibiting a close model-data fit, was found to lack theoretical support for the originally hypothesised effect of BioA2 on StemChg12. Model 3 was created to solve that problem. Subsequent models examined (Models 3B-D) were all attempts to evaluate simpler versions of Model 3 and are all scientifically defensible. The appropriate model comparison set in this case includes all versions of Model 3.

A model comparison table is presented in Table 12. There are two models that are virtually identical, Models 3B and 3C. This means the choice is up to the scientists to justify. This observed result could be interpreted as support for an effect of BioB1 on BioA2 (Model 3B), though certainly any such effect is weak and variable. Table 13 provides details. Parameter b11 is negative, consistent with theoretical expectations and has a two-tailed p-value of 0.111. Biologically, the debated process is potentially important because it may be that one of the species is a superior biocontrol agent and introducing a less effective biocontrol agent that competes with the first mentioned should be considered. The authors of the original study included this link (actual sample size was slightly larger and support slightly stronger, though scientific interest was the final determinant). Results for Model 3B are presented in Table 13.

Additional summary results for the selected model are shown in Table 13. Included are both the standardised parameter estimates and the R-squares. Often standardised parameter estimates are presented and used for conveying model findings. I refer the reader to the original paper (Larson and Grace 2004), if they have a deeper interest in the example.

A question raised earlier in the paper was about the consequences of retaining a weakly-supported link in a model for the other model parameters. It is known that leaving out an important link can have a major impact on estimated parameter values for the included links. This sensitivity is illustrated by the fact that model Χ² can drop abruptly when a single link is added (we observed a drop of over 8 points when we added link 12 to create Model 2). The elimination of link 6 from Model 3, however, only increased model Χ² by a tiny amount (0.05), which is typical when parameters with little support are removed. More to the point in this paper is the question of what would happen if we were to set the dependence of beetle species B on plant stems (parameter b7) to zero? The results from such a change are presented in Table 14. Model fit measures increase noticeably, but overall fit remains good. Comparing standardised parameter estimates to those in Table 13 shows the only non-trivial change is for the parameter set to zero (drops from 0.15 to 0.0). All other parameter estimates are very close to the same values as before.