Disentangling the Contributions of Plant Taxonomic and Functional Diversities in Shaping Aboveground Biomass of a Restored Forest Landscape in Southern China
Round 1
Reviewer 1 Report
The article is very interesting since it combines productive aspects (such biomass) with spatial, morphological and physiological.
Comments:
2-3. Change title. The conclusions of the study should not be part of the title
43-54. The hypotheses on which the article is based should be explained more clearly.
80-84. The variable “aboveground biomass” is not described.
The variable functional diversity should be described in the introduction. The concept would be clearer if the analytical variables that form it are described. I think it is relevant that the authors explain why there is a relationship between biomass and SOC and TN but there is no relationship with nutrients. The number of hectares is not clear. 12,22?? Soil analysis is chemical and not physiochemical. It only measures nutrients. Adjust the table. The data in the table looks bad. The AGB range values is 341-3523 kg ha-1 (3T ha-1 maximum). I consider this data to be excessively low. The values should be higher considering that it is a tree repopulation of more than 30 years. These data should be reviewed.Figure 2 and A2. The meaning of NS should be described in the figure foot.
Figure 4. Increase the quality of the image.
Table 1 is not mentioned in the text.
Author Response
"Please see the attachment"
Author Response File: 
Author Response.pdf
Reviewer 2 Report
This manuscript is very well written and clear. It addresses an interesting and important question. I am generally satisfied with the analytical approach. However, it appears that the forests are plantations and not native forest. Moreover, the four different plantations are not taken into account in the analyses. Of course we are looking for generalities so the details of the individual plantations is not of tremendous interest, but in some manner they need to be taken into account in the analysis, perhaps as blocks (random effects) or separate regressions.
You analyse a large number of functional traits which is good. How were these chosen? Have you considered calculating and including phylogenetic diversity in your analysis to help take account of a broader view of trait diversity? Why is taxonomic diversity represented only by species richness and not metrics that include species abundance such as Shannon's H', evenness, or Hill's numbers? It is perhaps not surprising the FD was more informative than taxonomic diversity when the former incorporates species abundance with functional trait values whereas the latter is simply the species richness.
Line 55-56 - reword, incomplete sentence.
Figure 2 & Figure A2 - omit non-significant regression lines as they mislead.
Figure 4 - add a legend for the functional trait abbreviations.
Line 181 and elsewhere. You need to be cautious in attributing causation from correlation. You don't know that diversity is driving aboveground biomass, you know that they are related.
Line 345 - why use just the first PCA axis for soil properties and CWM traits? Use Longman's Test or Parallel Analysis to determine how many significant PCA axes should be retained for interpretation and subsequent analysis.
Table A4. The variation in species among plantations reinforces my point above about the need to take account of the plantations in the analysis.
Table A4. * = common species.....what's the definition of a common species?
Author Response
"Please see the attachment"
Author Response File: Author Response.pdf
Reviewer 3 Report
The authors have a forest inventory dataset of plantations from within a small study region. They are attempting to expand on our understanding of biodiversity-ecosystem function relationships to include below-ground functional traits and soil conditions. This is a useful and important area of research, one that has implications for general ecology and ecological restoration. I feel that this manuscript has the potential to contribute to this discourse in a meaningful way.
Currently, however, the manuscript fails to set up the authors' intentions in a meaningful way, the authors do not justify or discuss decisions they have made, and some of the methods are opaque and not well established.
Major concerns
(1) Discussion of identified ‘mechanisms’ and causality where the study design is limited to patterns and correlation. Even with functional traits, the authors are still using an observational dataset, and cannot truly capture mechanisms. The authors should revise their terminology.
(2) Most BEF research has examined ‘productivity’ or variation in biomass as an ecosystem function, not ‘above-ground biomass’. Meta-analyses on this topic use some metric of productivity, such as biomass increment (tonnes per year), diameter increment (cm per year) or true primary productivity. I’m not sure how ‘biomass’ relates to an ecosystem function of importance for restoration, and the authors don’t justify this. Given these are planted forests, with a known year of planting, ‘productivity’ could be estimated.
(3) Restoration used in a non-core definition way, including the planting of simplified ‘plantation-style’ communities of non-native species. The assumed definition of “ecological restoration” refers to returning a degraded system back to its’ pre-human composition, determined either from a nearby undegraded reference site, or some historical records (McDonald et al. 2016). This doesn’t invalidate their work, but they need to be much clearer about what their study entails, as use of the term ‘restoration’ has implied meaning that is not borne out in their study.
(4) The introduction discusses ‘realistic’ communities, and the limitations of artificially managed plant communities, as functional diversity is potentially lower than natural communities. But the authors study sites are in managed plantations, mostly consisting of two or three species mixes. The authors then go on to discuss collecting traits from 40 dominant species. I’m not sure where these additional species came from? Are they species that subsequently dispersed into the plots after planting? In addition to this, 20 of those species cannot be found anywhere in the manuscript. Table A3 has 20 species listed for AGB estimation via allometric equations, Table A4 only has 20 species. It’s difficult to read Figure 2a accurately, but the maximum richness appears to be 21 species.
(5) Multiple bivariate trait relationships are presented as unique mechanistic relationships, when a PCA of trait CWMs found almost all trait variation exists on a single axis. Given that the first trait CWM PCA axis explained 91% of variation, Figure 5 is misleading. A lot of these predictor variables are highly correlated with each other (otherwise your first PCA axis wouldn’t explain so much variation). Presenting each trait as a separate regression suggests that they all separately drive above-ground biomass. The authors also do not give any indication of what their PCA loadings were, so we don’t know which raw variables contributed strongly to PC1 (for either the trait or the soil PCAs).
(6) I also question the methodology of PCA transforming the trait CWMs. In my mind, it would be best to PCA transform the species level traits. This gives you plant strategy axes using species as individual replicates such as in (Díaz et al. 2016). The authors could then get the PCA loading for each species on the first PCA axis, and use the loadings combined with relative abundance to estimate a CWM for each study plot. These should be used instead of the raw traits in Figure 5, as they are potentially trait trade-off axes that are not only meaningful in terms of ecosystem function, but because the PCA trait axes are not correlated, you don’t run the risk of explaining the same plant strategy five times using highly-correlated traits, which is the case in the current discussion.
(7) I have some concerns about the complexity of models used in this manuscript. The authors appear to have 36 observations (study plots), which is far less than suggested guidelines for SEM models (e.g., 100-200, see discussion in Jung 2013)). Also, the SEM has 7 unknown parameters, more than the ‘rule-of-thumb’ 1:10 ratio of parameters to observations, which also puts the model at risk of overfitting. I note that for the bivariate trait models visualized in Fig 1, the authors use a machine learning technique that relies on averaging ‘trees’ of subsetted models, generally 2/3 of the observations. This seems like a bad idea with such a small sample size – at the very least, the authors need to justify their decision to use this technique.
(8) I’m also concerned that study design is not incorporated into statistical models. There is no accounting for landscape position, which was mentioned explicitly in section 4.2 as a driver of study plot selection. Landscape position is likely linked to water availability, and therefore AGB, as well as correlated with trait mixes. The authors should also explore whether there is spatial autocorrelation in their above-ground biomass estimates.
(8) Final, the manuscript suffers from a lack of readability. There are a number of grammatically-poor sentences and incorrect word choices. As examples, see the first two sentences of the introduction. “the biodiversity metrics” should be “biodiversity metrics”, and “Logistically” should be “Logically”. The entire manuscript could use revision by a professional editor.
Line comments
Abstract: The authors switch between using "FD" and “functional diversity”. Be consistent.
39: Decide whether ‘and’ or ‘or’ apply here.
40-42: I agree that BEF relationships in restored systems are understudied, but this mostly in woody systems. There are a number of grassland and prairie restoration studies that investigate BEF relationships. I suggest the authors rephrase this section to focus more on woody vs herbaceous restoration research, and emphasize that it is woody restoration that is lacking in BEF (but not entirely absent - I am one of the authors on (Staples et al. 2019), for a recent example).
43, 57: what are ‘soil functions?’
44-63: The authors misrepresent the relationships between taxonomic and functional diversity here. Species richness is a proxy of functional diversity, assuming that more species equates to greater niche coverage and lower niche overlap, which then results in greater biomass acquisition. Also, Trait CWMs are not measures of functional diversity. They are community averages used to describe the ‘average’ function of a community, or the ‘average’ response to abiotic conditions. Sentences at 50-52 and 52-55 are repeated information. I suggest the authors split their discussion of functional diversity, and the impact of diversity on whatever soil nutrient stocks, into separate paragraphs.
51: It’s complementarity, not complementary
Line 49: Fig. S1 does not exist in the provided manuscript. Do you mean the conceptual model, Fig. 1? Also, this sentence is difficult to understand. I think you’re trying to say that you examined functional diversity, taxonomic diversity and trait CWMs simultaneously as correlates of above-ground biomass.
53: sentence fragment, need to say “biomass in a forest community IS regulated”
56: period instead of comma following ‘moreover’
85: This topic sentence is value, and is not clarified in the rest of the paragraph.
86: You are not unveiling mechanisms, you are examining patterns.
107: When you say “OLS linear regression” do you mean your SEM?
120-121: this is a confusing sentence. Split up the percentages and match them with the corresponding variables.
124-125: So increased values on soil nutrient PC1 (whatever that means for the actual conditions, the authors don’t provide the PCA loadings) increase plot FD. This is an interesting finding, that suggests that either soil condition alters FD by controlling germination of new dispersers, or survival of planted/dispersing species, so that high PC1 plots had different FD to lower PC1 plots. Given the authors set-up, this is an important discussion point, which I didn’t see in the manuscript’s discussion.
Figure 3: SEM results don’t show HOW predictor variables drive biomass, just that there is a relationship. How implies mechanisms, which you don’t directly address here.
Figure 3: Given that species richness is a proxy for functional diversity, you might consider an indirect relationship between species richness and FD in your SEM structure, rather than a direct path to biomass. Or try both causal structures and see what variance in results you get.
144-149: Your text here and the details in Table A1 make it sound like you put all the raw traits as predictors in a single random forest model. This is a big problem, as your trait predictors are very correlated – if they weren’t, trait PC1 wouldn’t explain 91% of the variation in plot-level trait CWMs. This is bad news for the model predictions. I suggest you follow my suggestions above in major comment (6).
149-150: You would be better off describing these bivariate models in terms of plant strategies rather than raw traits, given how correlated they are. Use the PC axes as suggested above, and it will simplify your results and discussion.
Figure 4: Figures should be interpretable independent from the main text. The acronyms for functional traits should be listed in the caption. Stylistically, this figure should be styled like the others in the manuscript. Specifically, the 3D-styled bars and drop shadows should be removed, and the x-axis needs tick marks.
174-175: What is a ‘biodiversity attribute’?
175-177: Poorly worded sentence. Also, citation needed for the claim that understanding BEF relationships, and specifically biomass, may improve restoration success.
182: Across vegetation types? As far as I could tell, you didn’t explicitly test your four forest categories, instead using taxonomic and functional diversity to compare them.
182-184: You’re implying mechanisms from your study which only captures patterns. The link between pattern and mechanism relies on the idea that increased FD = greater resource capture and lower niche overlap. You don’t test these assumptions, you are identifying patterns that fit within the assumptions. Also important to note that functional dispersion/divergence only captures the spread of species traits from trait centroid – they might still be very clustered together in trait space! If you wanted to capture whether species are spread out across occupied trait space (i.e. whether there are species present in all combinations of traits within the community), you should have measured functional evenness as well.
185-186: Again you’re presenting your results as if you uncovered mechanistic relationships. You didn’t.
187-188: You cite these studies as evidence of ‘positive linkage with above-ground biomass production’, which is mostly correct. Only [4] is suitable for citing as a comparison to this study, as it is the only one that includes ‘above-ground biomass’, not some metric of productivity, as a response variable.
194-195: Do you mean from your results, or are you just citing the conclusions of [29]?
204-228: This entire section is much longer than it needs to be, because it treats each of the bivariate trait CWM relationships as if they were unique and mechanistic. We know from the PCA that a lot of these traits correlated with each other. The discussion should be formed around this, discussing plant strategies as combinations of traits, rather than each individual trait axis.
217: Eucalyptus is a genus, it needs to be captialized and in italics.
258: So all plots were 33 years old? And they were cleared land (no woody biomass) prior to this point? How does the immature state of these forests link with the results? These forests were likely still in a biomass acquisition phase (non-mature).
270-271: You can’t assume this without explicitly testing for a spatial autocorrelation signal. Two ways to do this would be by incorporating random effects into your model to account for nested study design (plots within sites within plantations?) or conducing residual tests, such as Moran’s I.
344-345: This reads like soil properties and traits were combined together into a single PCA, rather than a separate soil PCA and trait PCA.
370: Again, you don’t have any evidence of mechanisms, just of patterns.
Table A4: What are the four table categories (“AM”, “EE”, “MC” and “NS”). They are not described in the table caption.
Table A6: This table is difficult to interpret. I’m assuming these are the PCA scores for each plot (sum of loadings multiplied by raw scores on each variable)? I would also like to see the loadings of the PCA, especially for the traits. Knowing what a high/low score on each axis means is integral to understanding your SEM results.
References
Díaz S et al. (2016) The global spectrum of plant form and function. Nature 529:167–171
Jung S (2013) Structural equation modeling with small sample sizes using two-stage ridge least-squares estimation. Behavior Research Methods 45:75–81
McDonald T et al. (2016) International standards for the practice of ecological restoration - including principles and key concepts. Society for Ecological Restoration, Washington D.C.
Author Response
"Please see the attachment"
Author Response File: Author Response.pdf
Round 2
Reviewer 2 Report
Generally you have adequately addressed my comments on my review of the original manuscript. However, the following points remain:
Point #1: I'm pleased to see the results of the ANCOVA testing for a plantation effect (Table A1). Where this is significant, what does it mean for your interpretation? Report this interpretation in the manuscript. Your report of this test on lines 120-122 and 167-170 appear contradictory.
Point #2: It is good that you've done a phylogenetic analysis of these data. Surely the results of this analysis published in Yu et al 2019 are relevant for your interpretation of the analyses presented here?
Point #3: I don't understand your response to my point #3 about testing just species richness and functional diversity. The paper by Fotis et al that you mention as justification in fact tested taxonomic richness and evenness and functional richness and evenness - in other words a balanced test. I still believe that your finding of the greater 'value' of FD compared to taxonomic richness is because FD incorporates species abundance values.
Point #8: Your response document indicated a parallel test of the CWM PCA to justify interpretation of PCA1 - the results of this test needs to be included in the manuscript. In addition, the results of the same test on the SOIL PCA need reporting.
Point #10: Table A6 - your response to my question about how you define a common species was to tell me the names of the common species. Again, what are the criteria you used to define a common species?
There are numerous English language issues throughout, especially in the new text. I encourage language editing by a professional native-English speaking editor.
Author Response
"Please see the attachment"
Author Response File: 
Author Response.docx
Reviewer 3 Report
The authors have addressed some of my initial concerns, particularly their description of their results as mechanisms rather than patterns. Despite this, several of my concerns were not addressed sufficiently.
Spatially-nested design
My major concern still remains. The authors have not satisfactorily shown that their spatially-nested design did not impact their results. Reviewer 2 also raised this concern during the last review. The authors conducted an ANCOVA, but did not provide the F-ratio for the plantation type variable. This means we still do now know whether ABG differs systematically across plantation type. The authors need to consider this, as well as other aspects of spatial nestedness as well, which would be hill position within plantation type, and the three sites of each plantation type (as study plots are nested within sites).
The authors should see my line comment for 152-153. Table A1 is insufficient as evidence that plantation type does not affect results. We need to see the three F-ratios (continuous predictor, categorical ‘plantation type’, and interaction of the two) to judge its importance.
The authors could conduct a similar ANCOVA for hill position. For study plots nested within each of the 3 plantation sites, they should consider a nested ANOVA with random intercepts. If their random intercepts explain > 0 variation in AGB, they have spatial autocorrelation and must consider this in all analyses.
The primary results may not change after considering this, but the manuscript should not be published until these questions are satisfactorily addressed.
Incongruous results
The authors have re-run some analyses, and now the main results are confusing. The authors state that FD explained 3x more variation in biomass than species richness (from bivariate regressions in Fig. 2), but in the SEM, the difference is 9x, as, despite a similar strength beta value, species richness explains very little variation of AGB in the SEM. In the discussion, the text reads as if the FD and trait CWM correlations with AGB were similar, when FD explained 9x more variation than the trait CWMs as well.
Authors should also see my comment for lines 377-378. We still do not know how the authors went from raw species-level trait estimates to a trait PCA CWMs at the plot-scale. There are two pathways which will give vastly different values for each plot and mean very different things ecologically. We also need to ensure that traits were equally weighted in the PCA.
Language and readability
Despite the author’s statement that the manuscript has been professionally edited, I found it littered with fragmented sentences and poor grammar. This is particularly apparent in the newly-added text.
Line comments:
34-35: carbon is stored as above- and below-ground biomass, not just above-ground.
35-36: sentence fragment, doesn’t make sense.
36-38: That’s a big call with no citations to back it up, and I would heartily disagree. We have a very good idea of how biomass is produced in restored systems, but finding generalities across systems is the difficult part.
42-43: You should explain what you mean by ‘functional diversity’ here, especially as your diversity metric is functional dispersion, which is only one aspect of diversity.
50: “niche space”, not “niche spaces”
53-54: this definition of functional diversity needs to be where you first use the term. Also this is a sentence fragment and doesn’t make sense.
55-56: ungrammatical sentence, doesn’t make sense.
56-58: what is the point of this sentence? What does it say that isn’t already said in this section?
61-63: ungrammatical sentence, should be “has” not “have”.
56-70: I’m assuming this is supposed to be a separate paragraph from the above? Regardless, it is poorly organised, and flips between discussing mass ratio and complementarity hypotheses in a confusing manner. It needs reorganizing.
78: You don’t have long-term evidence either. Don’t confuse the age of your forests with ‘long-term’, you have single snapshot of the biomass and diversity of these forests. To be ‘long-term’ you would need to have multiple time-steps, and show whether the biomass-FD relationship was consistent or changed over time (such as (Roscher et al. 2013) did in experimental grasslands).
80-81: Not necessarily. You could argue some artifically managed landscapes have much higher diversity than natural systems (botanical gardens are an obvious example), simply because humans eliminate environmental filters and competitive exclusion. You need to be careful making these sorts of sweeping statements that are not supported by evidence.
92: do you mean “and” instead of “or” here?
96-98: The “were” here makes it sound like your results. Use “have been” instead, which sounds more like your discussing past research.
Results: You should start with a paragraph of what your PC1 of Soil nutrients and traits mean here (what sort of communities/soils are high PC1 values and what are low values?). Otherwise your results in Fig. 2 for these variables don’t mean anything.
Figure 3: Okay so this is important to discuss – when considered separately, it looks like high CWM PC1 values mean greater biomass, but this is not the case when considering everything together in your SEM. There’s a positive relationship, sure, but very little variance is explained by that relationship.
152-153: Table A1 does not show that “other bivariate relationships did not differ among plantation types (Table A1), as it appears that only the F-ratio for the continuous variable is shown. A full ANCOVA contains three terms, the continuous predictor, the categorical predictor, and the interaction between them, each with an F-ratio. We would need all three to interpret each model correctly (a non-significant continuous predictor is interpreted compeltely differently if the continuous x categorical interaction effect is significant).
171-173: this sentence makes no sense, it is a sentence fragment.
Figure 4: The authors have responded to my initial comment, that Figure 4 could not be interpreted without a legend describing the acronyms, with a legend that contains only the acronyms. I felt I was sufficiently clear. Table 1 and Figure 4 both contain the acronyms with no explanation of the full term. Readers are forced to read the main text to find these. Please ensure both captions and/or table/figure contain the full term for each acronym.
202-203: be clear this is ‘plot-level biomass’. Also, your SEM results suggest species richness has a marginal, if any, impact on biomass.
205-206: Restoration treatments contained almost no diversity component. You’re conflating the subsequent blow-in diversity with initial treatment, which is ingenuine to your study design. Be clear that most of the diversity was NOT part of the initial treatments.
208-209: unnecessary statement.
209-210: You were just talking about functional diversity, now you’ve switched to species richness. Which do you mean? In this paragraph you should be discussing what the add-on positive effect of species richness on AGB is, after accounting for functional dispersion. Why do you see the modest effect of species richness in the SEM?
217: Though only 3% of variation in biomass once you consider FD and soil nutrients. Keep this in mind.
218-220: This is strong language for trait CWMs explaining 3% of the variance in biomass.
221-226: Put these in context. FD seems to be a 9x stronger correlate of biomass than trait CWMs, but your statements here make it seem like it is 50:50.
246: Eucalyptus is not italicized, despite my previous comment.
260-262: You don’t show us any results separated by plantation type, so you cannot make this statement. Table A1 doesn’t count, as you don’t use RN as a response variable split by plantation type.
282: A map of the study region with plot locations would be a useful supplementary figure, given the complex sampling design of the study.
377-378: The authors don’t explain how they go from raw trait values to a plot-level trait PCA. This is especially important because traits are on different scales, so we need to know that they used the correlation matrix to derive eigenvectors, not the covariance matrix (the covariance matrix is the default in the princomp function in R, which would be incorrect results if traits were not scaled). The same is true for the soil nutrients, also likely on different scales.
377-378: As well as, the authors don’t tell us whether their trait PCA was conducted before or after the CWM calculation. A PCA of plot-level trait CWMs is very different to a PCA of species-level trait values, where the axes are ‘strategy axes’ that were subsequently summed per plot as ‘strategy CWMs’. The authors need to be explicit, and justify their decisions. I favour the latter approach, as I don’t know what a PCA of trait CWMs would even mean. Surely we want to account for trait correlations at a species-level first, then work out the dominant trait-combination (using a PCA axis) in each plot.
389-390: If this refers to Fig 5, this is incorrect. In these figures, the models use AGB as the dependent variable and the trait CWMs as the independent variable. Also the caption for Fig 5 uses ‘endogenous’ and ‘exogenous’. Be consistent with terminology.
401-403: Aren’t these goals mutually exclusive? If you have high numbers of species with diverse functional traits, you no longer have dominant species, you have an even community with diverse traits, and the CWM no longer reflect the ‘dominant’ species, but the average of the even community.
403-404: Your study does not suggest the existence of these spectrums. They have been exhaustively studied over thousands of plant species and hundreds of ecologists. It is disingenuous to make this statement, with no citations, as it sounds like you are trying to claim these discoveries as your own.
410-411: I disagree. Your study includes almost no discussion of restoration strategy, and very little of your study actually had anything to do with restoration design, given your study sites were mostly monocultures or two-species mixes of exotic species! You spent two sentences in this paragraph giving, to be blunt, largely meaningless advice for restoration design.
Table A1: I also can’t understand exactly what your ANCOVA is. I’m guessing each row constitutes a separate model, with AGB as the response and the other variable as the continuous predictor. This needs to be in the figure caption for Table A1.
References
Roscher C et al. (2013) A functional trait-based approach to understand community assembly and diversity–productivity relationships over 7 years in experimental grasslands. Perspectives in Plant Ecology, Evolution and Systematics 15:139–149
Author Response
"Please see the attachment"
Author Response File: Author Response.docx
Round 3
Reviewer 2 Report
The term "variations" used in presenting the leadings of the PCA axes should be "variabililty", i.e., lines 60, 125, 127, 128, 129, 134, 180, 438.
Author Response
"Please see the attachment"
Author Response File: Author Response.pdf
Reviewer 3 Report
The authors have addressed the majority of my minor comments, and I appreciate them clarifying some of their statistical protocols, particularly their trait CWM PCA protocol.
I am still not satisfied with the author’s efforts to show their study design has not impacted their results. Their additional analyses, rather that justifying their main text analyses, actually highlight my point. I will attempt to highlight the problem, show the authors how their results highlight my point, and suggest solutions. This is not something that can be hand-waved away by running a few ANOVAs and looking for small p-values. This is a fundamental violation of the assumption of independence in their dataset. Every decent ecological statistics textbook has a section on nested design, mixed-effects models, and how to test for autocorrelation.
The problem
The problem is that you have two levels of spatial nesting. There are clusters of plots in four different plantation types, which are each in different places in the study region (Fig A3). Plots in each plantation type cannot be considered independent replicates because they are closer in space and share an initial planting regime. The effect of these things may not be captured in your soil, diversity and trait variables.
Within each plantation type you have three slope positions. Plots at each slope position are closer in space, and also share a variety of microclimate effects not captured by your soil nutrients. They are also not independent replicates.
Accounting for your nested design MAY NOT affect the results of the manuscript. But you still need to do it. I’m primarily concerned from a statistical point of view, that non-independence of data points is a violation of the general linear model. I’m also concerned given the small sample size in this study.
The evidence
Table A2 highlights that for some predictors, plantation type is a significant predictor of AGB (including taxonomic diversity, which is a core part of the study). These tables are still incomplete. A full ANCOVA, with an interaction effect, should have 3 p-values: one for the continuous predictor (which we have), one for the variance explained by intercept shifts of the categorical predictor (which we might have?) and a final one for the variance explained by slope shifts for each level of the categorical predictor. I’m not sure which one the “plantation type” refers to. The conclusion still, is that AGB differs systematically across plantation type, which is not accounted for in any of the main analyses.
The ANOVA comparing variables over hill slopes doesn’t find any significant differences. I only care about AGB, as that’s the response variable used throughout the manuscript. It doesn’t find a significant result, but slope does explain a fairly large proportion of variation. Above, I mention that this is the smaller level of spatial nesting, as hill slopes are within plantation types. This means that each ‘hill slope’ group in the ANOVA comprises plots across each of the four plantation types. We know from the ANCOVA that AGB differs across plantation type, and even without considering that effect, the authors find hill slope explains a lot of variation.
The solution
Plantation type and hill slope MUST be accounted for in the SEM and main regression analyses. Any time the authors use AGB as a response variable, they must account for their spatially nested design. This could be done by either including these two categorical variables as fixed effects in their models. Given that these are ‘nuisance’ variables rather than variables of interest, the authors may prefer to have them as nested random intercepts using a mixed-effects model. This allows intercept shifts for each plantation type (to account for systematic variation in AGB due to each plantation, and then each hill slope within each plantation type (to account for systematic variation in AGB due to hill slope).
Other points
I will also respond to some of the authors responses to my past review and text from the manuscript on this point:
“We did not find the effect of the slope position on the predictor variables.” - this was never the concern, the concern was that slope position or plantation type affected the RESPONSE variable, AGB.
“The sites should not have any impacts on results” - this is an assumption that must be tested, which is my entire point. You have not satisfied me that this is the case. In fact your ANCOVA and ANOVA results make me more concerned about the results of your main analyses.
“Moreover, we have considered the effect of hill positions on our result” - Yes you have, but not in the analyses you use to draw your conclusions.
Manuscript 428-430: “Moreover, analysis of variance (ANOVA) test was performed and revealed, AGB and other predicting variables were not significantly influenced by the slopes of the hill (Table A9)”. Significance is not the test here. Hill position still explained a lot of variation, especially when you didn’t consider plantation type at the same time (which we know from the ANCOVA does systematically explain AGB).
Other line comments
Figure A3: It looks like the four ‘plots’ here in this map are actually the different treatment types. The acronyms are not explained in the figure caption, so readers cannot tell which is which. In addition, the position of the 36 plots is not shown.
Author Response
"Please see the attachment"
Author Response File: Author Response.pdf
