Effects of Land Use on the Community Structure of Aquatic Invertebrate in Subtropical Streams

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The paper is very interesting since the presentacion of the differences between sites with different influences are of importance. Mostly since the landscape is constantly changing due to human impact and changes in land use. 

I have few comments

In lines 165 and 166 it is stated that organisms were identified at family level and then accounted for. Since indexes are used for species I think it should be clearly stated why family level was ok for the analysis such as species richness, abundance and so on. The descriptions in the manuscript talk about species changes and abundances, so could the authors clarify why do they refer to species when the lowest taxonomic level was for families?

And as an edition comment tables should only show one decimal position.

I do not have comments on the document, therefore I am not attaching any pdf.

Author Response

Comments 1: In lines 165 and 166 it is stated that organisms were identified at family level and then accounted for. Since indexes are used for species I think it should be clearly stated why family level was ok for the analysis such as species richness, abundance and so on.

Response 1: Thank you for pointing this out. We should clarify that for the study of benthic macroinvertebrates, identification at the family level is sufficient to discriminate between communities, since the presence or absence of these taxa indicates the ecological integrity of the site, which is the aim of this study. According to Jones (2008), "Although few question the value of species-level data, there is also near consensus that species taxonomy is not always required for bioassessments. That is, bioassessments are special studies in applied ecology that require only sufficient information to distinguish sites impaired by human activities from those in their natural or near-natural state. Where we disagree, is on the optimal amount of detail". This information can be ratified in the reference below and was added to the manuscript in the material and methods section (section 2.3, second paragraph) to make clear taxonomic sufficiency at the family level. And, Kokesh et al (2022) “the use of family-level data generally preserves the detection of spatial and temporal gradients in wastewater contamination. This means that even with this broader taxonomic resolution, significant pollution-related changes in macrobenthic composition can still be identified”.

 

• Jones, F.C. Taxonomic sufficiency: the influence of taxonomic resolution on freshwater bioassessments using benthic macroinvertebrates. Environmental Reviews 2008, 16, 45-69. https://doi.org/10.1139/A07-010

 

• Kokesh, B.S.; Kidwell, S.M.; Walther, S.M. Detecting strong spatial and temporal variation in macrobenthic composition on an urban shelf using taxonomic surrogates. Marine Ecology Progress Series 2022, 682, 13-30. https://doi.org/10.3354/meps13932

 

Comments 2: The descriptions in the manuscript talk about species changes and abundances, so could the authors clarify why do they refer to species when the lowest taxonomic level was for families?

Response 2: Thank you for pointing this out. We justify the use of the taxonomic level when expressing diversity indices. The specific term in the literature is "species" for this biota (macroinvertebrates). The small size makes it difficult to identify at a lower taxonomic level, and family is sufficient (taxonomic sufficiency discussed in comment 1), even when applying the index for species. This information can be found in the book referenced below, chapter 6, which defines the criteria and indices for assessing the integrity of an environment. Also, other articles cited as references throughout the work apply the same methodology.

• Davis, W. S., & Simon, T. P. (Eds.). (1995). Biological assessment and criteria: tools for water resource planning and decision making. CRC Press.

 

 

Comments 3: And as an edition comment tables should only show one decimal position.

Response 3: Thank you for pointing this out. We would like to justify the use of three decimal places in the tables, because the values of the environmental variables of the water, as well as the statistical results, would only be in exponential or non-existent values, which would generate doubts and/or misinterpretation of the results. We consulted other papers published in this journal and found that up to three decimal places were used in the manuscripts. We therefore ask that the configuration presented be maintained.

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

Comments for author File: Comments.pdf

Comments on the Quality of English Language

Author Response

Comments 1: “Effects of land use and occupation on the taxonomic structure of aquatic invertebrate communities”. However, this title is confusing and misinforms a reader. Neither occupation effects (whatever it means), nor taxonomic structure were considered directly. A few univariate metrics only (i.e., diversity & total abundance) were analyzed. 
Response 1: Land use and occupation refers to the way we use and occupy the landscape, and is an official term used in Brazil. We acknowledge that the direct translation might cause misleading interpretation in English, and because of that we removed “occupation” from the title, as it was redundant. The use of “taxonomic structure” in our title was not meant to be misleading because our metrics (diversity and abundance) were all calculated based on the family’s identity, not their functional or genetic features. Since stream macroinvertebrate research explicitly refers to this ecological separation, we included in the title. However, since it causes confusion to the reviewer, we changed it. The title now reads: “Effects of land use on the community structure of aquatic invertebrates in Subtropical Streams.

 
Comments 2: Taxonomic composition is only briefly mentioned in Results (L 274-278) but not discussed properly. The authors briefly stated that “dominant species in the sampled streams remained consistent over time” (L 378-379) but no one species was mentioned, only few higher taxa, such as Chironomidae or Oligochaeta, without providing any numerical data. 
Response 2: We appreciate the comment. The use of “taxonomic structure” does not imply in the discussion of all family’s identity (or higher level of identification, as pointed out). Since we calculated community indices based on the taxonomic composition of invertebrates, our discussion is focused on the main patterns. The reference of “taxonomic” features is important to clarify that our paper is not dealing with functional nor genetic community assembly. Because this was identified by the reviewer, we included a proper explanation on the methods, please see lines 146-147. We agree with the reviewer that the use of “species” was not correct. In macroinvertebrate research, taxonomic identification is mostly restricted to families or higher classification because of difficulties in defining species (we would need to match larvae with their adult – and this is not feasible in community ecology studies with multiple streams. Not only for us, but globally), and this is not a problem for our inferences nor to our discussion. The identification of families is recognized as sufficient to discuss main ecological patterns. According to Jones (2008), "Although few question the value of species-level data, there is also near consensus that species taxonomy is not always required for bioassessments. That is, bioassessments are special studies in applied ecology that require only sufficient information to distinguish sites impaired by human activities from those in their natural or near-natural state. Where we disagree, is on the optimal amount of detail". And, Kokesh et al (2022) “the use of family-level data generally preserves the detection of spatial and temporal gradients in wastewater contamination. This means that even with this broader taxonomic resolution, significant pollution-related changes in macrobenthic composition can still be identified”.

This approach has been detailed in our Material and Methods section and the reference has been added to make clear the taxonomic sufficiency at family level:

 

·         Jones, F.C. Taxonomic sufficiency: the influence of taxonomic resolution on freshwater bioassessments using benthic macroinvertebrates. Environmental Reviews 2008, 16, 45-69. https://doi.org/10.1139/A07-010

·         Kokesh, B.S.; Kidwell, S.M.; Walther, S.M. Detecting strong spatial and temporal variation in macrobenthic composition on an urban shelf using taxonomic surrogates. Marine Ecology Progress Series 2022, 682, 13-30. https://doi.org/10.3354/meps13932

 

We recognize the importance of reviewer’s comment , but our methodology is in line with accepted and appropriate practices for this research area.

 

Comments 3: I also wander why the authors called their metrics “species diversity” and “species richness”, though only the family-level (at best) taxa are listed in Appenix table? As regards the “occupation” (occupancy?), this term occurred in the title only and nowhere else. 

Response 3: Accordingly, we have replaced "species" with "family" whenever necessary to make our results clear. However, when using the taxonomic level to express diversity indices, the specific term in the literature is "species" for this biota. Its small size makes it difficult to identify at a lower taxonomic level, and family is sufficient, even when applying the index for species. This information can be found in the book referenced below, chapter 6.

 

•          Davis, W. S., & Simon, T. P. (Eds.). (1995). Biological assessment and criteria: tools for water resource planning and decision making. CRC Press.

 

 The term "occupation" refers to how human beings occupy the territory along the Itajaí-mirim river basin. The term has been added to the topic "Material and methods", item 2.1 Study of the area, second paragraph, in the section "Discussion", last paragraph and also in the topic "Conclusions".

 
Comments 4: Second, the applied methods of data analysis seem to be inappropriate. The effects of the two main groups of predictors (first, land use and season; the second are environmental and spatial) were analyzed separately. This approach is undoubtedly incorrect, since these groups are closely intercorrelated (see table 2), but the separate analysis disables to discriminate the effects of land use and environmental conditions. In Abstract, the authors claimed (L 24-25): “The proximity of the streams generates similarity in the dominance of species”. However, the studied sites belonging the same type of land use were spatially clustered (the rural and urban ones in particular), and both biological and environmental parameters are spatially structured. Therefore, the combined analysis is necessary to discriminate the effects of land use from these of geographical distance. Next, the choice of analytical methods is questionable. Generalized linear models are generally used to relate, via some link function, a response variable of any type (e.g. continuous, binary, or count) to a predictor variables, which are assumed to be continuous. Here, however, the situation is just reverse: response variables are continuous (diversity indexes) or count (richness, abundance) BUT predictors are order (season) or categorial (land use). Furthermore, “Shannon and Simpson diversity indices were evaluated with generalized linear models, with Poisson distribution” (L 181-182). The Poisson regression is used to model count data, i.e. the response variable has to be a positive integer. Diversity indexes are evidently not the case!

Response 4: We kindly disagree. There are no conceptual mistakes in separating this analysis because we were first interested in understanding the patterns (are there spatial temporal differences of invertebrate diversity?). Because we identified significant differences of invertebrate’s diversity between streams with distinct land uses, our second approach was to investigate the processes behind it and identify which environmental variables, including the spatial dependence, might be leading to such diversity patterns. Land use differences is expressed in local and spatial influences over the community, that was properly assessed. It is not mandatory to include all variables in the same analysis. And we did separate the analysis because of our limited observation number (12 streams). We are aware that it is a small sample size, but again, it is sufficient to answer our research questions, and it is a classical approach. 

Our statistical approach is appropriate for this research design. There is no limitation in using GLMs with categorical variables. You can find multiple examples in Zuur et a., 2009 or Crawley, 2015 – just to point textbooks). There is also no limitation in using Poisson distribution to continuous variables as states by Zuur et al., 2009, and there is no diversity index with negative values in our dataset. The most important assumption when choosing a distribution model regards the relationship between variance and mean of the response variable, which we choose carefully. We performed a detailed and careful exploratory analysis that allows us to use this approach robustly. We could have used distinct statistical approaches, but our choice is not incorrect, and we choose to maintain it.   

 

·         Crawley, M.J. 2015. Statistics: an introduction using R. 

·         Zuur et al., 2009. Mixed effects models and extensions in Ecology with R

 

Comments 5: The presentation of the results is not full enough. No estimate of explanatory power of the models are presented (e.g., adjusted R2). What percentage of total variance is explained by the whole model and by each particular term? In addition, only the raw effect values are presented in the tables for regression results. These values are incompatible and therefore not informative, since all variables measured in different units, so the actual effect sizes are unclear. Please provide the standardized regression coefficients (beta’s).

Response 5: We used Generalized Linear Models, that uses maximum likelihood estimator. This method does not minimize the squared error (ordinary least squares). Since the coefficient of determination (R2) is calculated by ordinary least squares and not maximum likelihood, there is no coefficient of determination to show. However, to respect the reviewer’s suggestion, we calculated the Deviance based R2 as R2 = 1 – Deviance/Null Deviance. Then the adjusted R2 was computed as 1 – ((n-1)/(n-p))*(1-R2), where p is the number of parameters in the linear predictor and n in the sample size. All Adjusted R2 were included in the table legends and in the text. The effect of each level of categorical variables or the continuous variables is evaluated by the coefficient estimate, provided in each of the regression tables. All explanatory variables were standardized (mean 0, unit std) prior to regression analysis, no raw values were used, and so, all coefficient estimates are already standardized. We added a proper explanation on the methods, because they were missing and caused confusion.

 

Comments 6: DISCUSSION is imperfect and superficial. Several environmental factors are listed as important in the tables (Results section), but their particular effects on certain taxa are not discussed.

Response 6: We appreciate the feedback. We recognize that the comment did not specify where exactly the discussion was lacking, but after a detailed re-evaluation, we have identified specific points that can be improved. In response to this suggestion, we will revise our discussion to include a more in-depth analysis of the specific effects of the environmental factors listed in the tables in the results section on certain taxa. 

The specific points reviewed are:

·         Reference [51], importance of indices for environmental assessment - second paragraph;

·         Inclusion of EPT analysis in the land use gradient, references [3;25] - third paragraph;

·         Inclusion of the analysis of families with environmental components, references [3;52;53;54] - third paragraph;

·         Inclusion of the analysis of families exclusive to rural environments, references [44;56;57;58] - fourth paragraph;

·         Inclusion of the Simuliidae family, reference [3] - sixth paragraph;

·         Inclusion of the analysis of the family Calamoceratidae (Trichoptera), references [44;60] - eighth paragraph.

 

Comments 7: Some results seem questionable. For instance, water velocity is indicated as having highly significant effect on abundance in linear regression model (Table 7); but plot on the Fig. 3c clearly indicated the non-linear (unimodal) response.

Response 7: The relation of water velocity was, indeed, not linear. Following the reviewers inquire, we performed more models’ explorations. The gam model, with a smooth for velocity (to account for nonlinear relationship), provided a left skewed residual pattern (deviance and Pearson). Not valid for interpretation. We then performed a Negative Binomial GLM without velocity and got an AIC value higher (787.58) than the model with velocity (778.80). So, we choose to maintain our model (abund ~ Phosphorus + Conductivity + Velocity), but we adjusted our interpretation. Please see section 3.3 “Relationship between Macrobenthic Invertebrates and Environment”, first paragraph.

 

Comments 8: It is unclear, what “the intermediate disorder Theory” mentioned in L 369 is? The authors referred to Mwaijengo et al. (2020) [49]; but I cannot find any mentioning of this theory neither in the cited paper nor in other relevant ecological literature.

Response 8: We agree that the concept of Intermediate Disturbance Theory needs to be discussed, however the reference [49] in the article is not Mwaijengo et al. (2020), but Connell (1978) author of the theory (now reference [55]). I believe there has been some mistake. For a better understanding and applicability of the concept, another reference was added in the discussion topic, fourth paragraph (below is the reference) and compared with similar results in a study carried out in the Czech Republic (de Donnová et al 2022).

·         Wilkinson, D.M. The Disturbing History of Intermediate Disturbance. Oikos 1999, 84, 145-147. https://doi.org/10.2307/3546874

 

Comments 9: MINOR COMMENTS

- Misprint in Table 3: “Florest” instead of “Forest” 

- There are sentence fragments in the text, e.g. “Results diagnosed in other studies [6,25,30].” (L 430); “Dissonant factor to other studies in streams [15,51].” (L 406); etc. 

- “Hirudinida” is unaccepted name, there is Hirudinidae (Family) in Hirudiniformes (Suborder) in Arhynchobdellida (Order). 

- Many misprints in taxonomic names in Appendix (Table 11, mistakenly numbered as 9 in the text): “Nematode” = (Nematoda); Lepdoptera (=Lepidoptera); “Shaeniida” (= Sphaeriidae); etc.

Response 9:

-          Misprint in Table 3 “Forest”, corrected. 

-          The textual fragments are small expressions, but they point to other studies that ratify the results of this study or have presented different results. It's a way of minimizing space, making reading more dynamic and if the reader is interested, they will know where to find other studies, as they are included in the references.Family “Hirudinidae”, corrected.

-          Table 11, mistakenly numbered as 9 in the text, corrected. Taxonomic revision carried out. Only the comment about Shaeniida was not considered, as it represents the order of the Sphaeriidae family.

 

Comments 10: Summarizing, the fundamental major revision is necessary before the paper could be reevaluated. Authors should more carefully choose the most appropriate statistical methods. Thay also need either to re-formulate the title and objectives of their study, or (preferably) involve the data on communities’ structure and composition in the analysis. There are many suitable methods in ecology, e.g., a set on nonparametric distance-based analogs of variance (PERMANOVA) and regression (DistLM) analyses, ordination methods (dbRDA, CCA, etc.). I also suggest careful text check-up for syntax, language and taxonomy.

Response 10: We appreciate all of the comments that helped improve our manuscript. We included more detailed explanation on the methods to make it clearer. Our statistical approach is adequate and provide robust responses of community structure responses to land use, reflected in local and spatial influences over stream biota. The proposed statistical analysis are more adequate to investigate invertebrate composition, which we were not primarily interested in.

Author Response File: Author Response.pdf

Round 2

Reviewer 2 Report

Comments and Suggestions for Authors

The authors have made considerable efforts to improve the text. In particular, they added some necessary points in methods description and presentation of their results, added some biologically sounding information in discussion, and corrected many mistakes in the text. To my view, the article is now considerably better and close to state sufficient for publication.

Some points, however, remain and need to be improved before publication.

1) The authors claim that they “have replaced "species" with "family" whenever necessary”. However, the replacements have not been made, e.g., in Methods section (L. 145-147), results (L 269) and in table captions (L 205). Please be consistent in avoiding mention the “species” in presenting your results; use “family richness/diversity”, or “taxonomic…”, or just simply “richness/diversity” – but not “species”.

2) I still have some doubts about statistical analysis, in particular about robustness of GLM on the categorical data, but leave this issue to the discretion of authors. I’m glad to hear that the explanatory variables were standardized prior to regression analysis; some results remain to seem vague for me – and, I believe, for any careful reader.  For instance, according the Table 7, flow velocity has thousandfold stronger effect on abundance than conductivity, though Fig. 3 clearly shows that the effect appears owing to few urban streams with very high conductivity (NOT velocity) and remarkably abundant fauna. Another example: depth has 600-fold stronger effect on diversity than conductivity (both effect significant, Table 8), though Fig. 4 demonstrates clear relationship with conductivity but no correlation with depth at all… These (and other) discrepancies need to be explained (or, at least, commented) in Discussion.

3) The authors wrote: “…The comment about Shaeniida was not considered, as it represents the order of the Sphaeriidae family”. “Shaeniida” order does not exist, Sphaeriidae belongs to ord. Veneroida.

Author Response

 

1. Summary
 
 
Dear reviewer, 

Thank you for taking the time to correct this manuscript. All the revisions have been accepted by the authors. Below we describe each change made point-by-point. We will be happy to answer any questions you may have.

 
2. Point-by-point response to Comments and Suggestions for Authors

 
Comments 1: The authors claim that they “have replaced "species" with "family" whenever necessary”. However, the replacements have not been made, e.g., in Methods section (L. 145-147), results (L 269) and in table captions (L 205). Please be consistent in avoiding mention the “species” in presenting your results; use “family richness/diversity”, or “taxonomic…”, or just simply “richness/diversity” – but not “species.

 
Response 1: We thank you and accept your corrections. The changes have been made. We only kept the term “species” when it was included in references.

 
Comments 2: I still have some doubts about statistical analysis, in particular about robustness of GLM on the categorical data, but leave this issue to the discretion of authors. I’m glad to hear that the explanatory variables were standardized prior to regression analysis; some results remain to seem vague for me – and, I believe, for any careful reader.  For instance, according the Table 7, flow velocity has thousandfold stronger effect on abundance than conductivity, though Fig. 3 clearly shows that the effect appears owing to few urban streams with very high conductivity (NOT velocity) and remarkably abundant fauna. Another example: depth has 600-fold stronger effect on diversity than conductivity (both effect significant, Table 8), though Fig. 4 demonstrates clear relationship with conductivity but no correlation with depth at all… These (and other) discrepancies need to be explained (or, at least, commented) in Discussion.
 

Response 2: We appreciate the comment and emphasize that the GLM has no restrictions on the use of categorical predictors, as can be seen at https://doi.org/10.1002/1097-0258(20000715)19:13<1771::AID-SIM485>3.0.CO;2-P. We acknowledge that some variables, such as speed (Table 7) and depth (Table 8), have larger coefficient estimates, although they do not directly influence the response variables, as can be observed in the graphs. We tested alternative models with different probability distributions and compared all candidate models before making our final choice. The regression coefficients are interpreted as the effect of each variable on our response, assuming all other explanatory variables are held constant. This generally adjusts for other explanatory variables. Because of this, the regression coefficient for a given predictor may change when other predictors are included or removed from the analysis. When removing some of the non-influential predictors from our model, residual validation is not met and AIC values are higher. We included appropriate explanations in the results section to make it clear that we do not consider the influence of speed or depth on our responses. 

 

Comments 3: The authors wrote: “…The comment about Shaeniida was not considered, as it represents the order of the Sphaeriidae family”. “Shaeniida” order does not exist, Sphaeriidae belongs to ord. Veneroida.

Response 3: The authors apologize for the misunderstanding regarding the classified taxonomic order. We accept and appreciate the reviewer’s correction. The order "Shaeniida" has been removed from Table 11 and classified under the order "Veneroida".

Author Response File: Author Response.pdf