Effects of Post-Fire Deadwood Management on Soil Macroarthropod Communities

Round 1

Reviewer 1 Report

This study showed that post-fire deadwood management affected soil macroarthropod communities; such an effect was still manifest ten years after the management. The results shed new light on how post-fire management could shape below-ground processes in forest ecosystems. Overall, this paper is well written. The authors did a thorough analysis of the data.

My major concern is that this study did not have unmanaged controls. The authors explained at great length in the introduction how trunk removal/Salvage logging (SL) could affect soil fauna while such an effect remained poorly understood (L 54-66, also see Abstract). Although the introduction seems to focus on the effects of SL on soil fauna, this study did not provide evidence on how SL would influence soil fauna (since there were no controls). Instead, the authors studied the difference in macroarthropod communities between SL and another procedure, partial cutting (PC), without providing context for this comparison in the introduction. Therefore, I consider the present introduction section a bit misleading. Please explain why you think comparing SL and PC is important. I understand you chose SL because it is one of the most commonly used post-fire management. I may be wrong, but the treatment of PC seems peculiar (i.e., cut down most of the trees, cut the logs in pieces which are then spread evenly over the ground) and not very common.  There is no context for PC treatment in the introduction. We need more information about why you chose PC as one of your major treatments to assess the significance of the difference you observed between SL and PC.

In addition, because you don’t have controls, some conclusions seem inappropriate. e.g., Abstract L30-31 states that this study suggests SL can affect soil macroarthropod recuperation even a decade after management, which is based on the observation that the abundance and richness under SL were lower than those under PC. However, this pattern may result from the stimulation of PC on macroarthropod communities while SL had no effects or even slightly stimulated macroarthropod communities. Please edit the manuscript so the introduction, discussion and conclusion are more in line with the observation.

I also have some minor comments.

It looks the overall abundance and diversity observed in this study were quite low compared to other similar ecosystems (L 285-286). How does your sampling method, one-time soil core sampling compare to other common methods for soil arthropods, e.g., traps? You mentioned that the ants were analyzed separately for mixed effects models (L 164-165). Did you exclude ants in Table 2 and Table 3? If so, please state as so explicitly in these two tables. Also, where is the result for the separate analysis of ants? L 185-186. The interpretation of ANOSIM R values seems not in line with the reference (also see Clarke 1993). In the reference, R=-1 does not indicate no separation (i.e. null hypothesis) as stated here but corresponds to similarities across different treatments being higher than those within.

Author Response

Please see the attachment.

Author Response File: Author Response.docx

Reviewer 2 Report

The authors make a compelling case for the need to study the effects of post-fire management on soil macroarthropod communities and present results from a well-designed experiment. The data collected and presented are valuable and would be of interest to science and management communities. However, there were three areas in particular where there is room for improvement or greater explanation or justification.

1) From figure 1, it appears that the original experiment included an uncut control treatment. Why were no data collected or presented from this treatment? There should be some justification for this absence.

2) Other than a statement in the methods about the approximate ground coverage, there are no data presented on surface fuel. To me this is the weakest part of the paper. If the authors are attributing changes in macroarthropod abundance and richness to surface fuel attributes, than some data on these attributes should be presented and ideally analyzed along with data on macroarthropod communities. If such data are available, they should be presented. If not, this should be justified or presented as a study weakness. 

3) In the introduction and discussion there is much written about the effects of wood removal, but really no wood was removed in this study. It seems to me that the study is really comparing a mastication treatment to a lop and scatter treatment. I would suggest the authors review and include literature on mastication and edit the introduction and discussion to reflect the fact that this study really addresses the effects of mastication, not wood removal. 

Another minor point - In the discussion you attribute the lower macroarthropod abundance and diversity in this study compared to others to wildfire. Couldn't it also be due to the history of the site? It seems they would have had a history of disturbance (plantations on terraces established with bulldozers) which may or may not be different from sites in other studies. 

Author Response

Please see the attachment.

Round 2

Reviewer 1 Report

The authors have provided a thorough response to reviews and appear to have incorporated most of the suggestions provided in the prior round. I was pleased with the more explicit and consistent way throughout the manuscript in which they emphasized that this study compared soil macroarthropod communities between different post-fire managements instead of investigating the effect of Salvage logging. My only comment if that the effect of microhabitats on community assemblages seems a little unusual (L 247-249, it looks the differences by microhabitats were significant, yet “greater dissimilarity among samples within a microhabitat than between microhabitats”) and probably need some explanation.

Author Response

Comments from Reviewer 1

The authors have provided a thorough response to reviews and appear to have incorporated most of the suggestions provided in the prior round. I was pleased with the more explicit and consistent way throughout the manuscript in which they emphasized that this study compared soil macroarthropod communities between different post-fire managements instead of investigating the effect of Salvage logging.

Thank you very much!

My only comment if that the effect of microhabitats on community assemblages seems a little unusual (L 247-249, it looks the differences by microhabitats were significant, yet “greater dissimilarity among samples within a microhabitat than between microhabitats”) and probably need some explanation.

Thank you for pointing this out. Following the comment, we went back to re-analyze the dataset. We found that the difference in community composition is indeed non-significant, and that the previous indication of significance resulted from a coding error. We should have spotted this ourselves beforehand, as the magnitude of the “effect” is very small and its direction was counterintuitive, as suggested by the reviewer’s comment. The result, as now shown, indicates that we did not detect differences in community composition across treatments (or across samples of a given treatment, as previously suggested). Of course, due to the lack of an effect we also removed the post-hoc analysis from the manuscript.

Thank you for your time!

Reviewer 2 Report

My original concerns regarding presenting fuel data were not adequately addressed. The authors provide an estimate of fuel loading across the site based on a model, but don't justify use of the model and don't provide actual measures of fuel loading. I believe this is critical if they want to attribute soil community attributes to downed wood. Otherwise, differences in the soil community can only be attributed to treatment differences. It is unfortunate that factors that could drive soil community characteristics (downed wood, soil moisture, temperature, etc) were not measured. 

Author Response

Comments from Reviewer 2

My original concerns regarding presenting fuel data were not adequately addressed. The authors provide an estimate of fuel loading across the site based on a model, but don't justify use of the model and don't provide actual measures of fuel loading. I believe this is critical if they want to attribute soil community attributes to downed wood. Otherwise, differences in the soil community can only be attributed to treatment differences. It is unfortunate that factors that could drive soil community characteristics (downed wood, soil moisture, temperature, etc) were not measured.

We assume that we satisfactorily addressed the other three points initially raised by the reviewer, so we focus solely on the one remaining point.

The reviewer inquiries again about fuel data. We understand that any data offering information about the amount and structure of dead wood across the treatments and the microhabitats could potentially be of interest. However, we insist that this is outside the scope of our study, and that an accurate measurement of the actual amount of wood is not necessary to interpret our results. This is because we are comparing two experimental treatments defined by wood management, and two microsites clearly characterized by the presence of a trunk. Treatments and microsites had proper levels of replication that allow to make statistical inferences from our data. For several reasons (scope, budget, objectives of the study) we did not measure fuel loads at the time of soil sampling for this study (ten years after the fire). However, we do know the initial conditions of the treatments. In this regard, please note that we already incorporated in the previous revision data on wood biomass, modelled from data on tree density, diameter, and height. In any case, and according to the reviewer’s comment, we think we can still improve the precision and clarity of our explanations, so we have rephrased some parts of the text and included further explanations and data. Please find below a point by point explanation.

In relation to the calculation of wood biomass, the reviewer inquires about a justification of the model we used. It is true that there are several models developed to calculate wood biomass in forests, and we had not provided a justification for our choice. We selected CubiFor because this model was developed to calculate wood biomass in pine afforestations and reforestations in the Iberian Peninsula. Afforestations and reforestations with pines are a common landscape in this part of the world, and they have a growth pattern and characteristics that clearly differ from pine forests and reforestations of other regions (e.g. high density, low growth rate compared to other regions such as central Europe, etc.). CubiFor has also been validated, with independent data from the 3rd National Forest Inventory of Spain (Rodríguez et al. 2008, Lizarralde et al. 2017). Given that our study site was a pine afforestation, we trust that the use of this locally-developed model was the best option. We have now included additional clarifications in the legend of Table 1.

We have also included some additional data and more information about the structure of the Salvage logging treatment at the moment of its implementation and how it was implemented, indicating that the masticated woody material had mostly a diameter between 2 and 5 cm and that it covered 32% of the surface. This has forced to rephrase the paragraph where the Salvage logging treatment is described, reading now as follows: “ 1. Salvage Logging (SL), where all the burnt trees were manually cut and the trunks cleaned of branches with chainsaws. Trunks were manually piled (groups of 10-15 logs), the woody debris was masticated with a tractor, and the slash was spread on the ground. The Forest Service had planned to extract the trunks with a log-forwarder, but the foresters eventually cancelled this step due to difficulties in precisely operating machinery within the spatial arrangement of the plots. Masticated woody material (circa 2-5 cm in diameter) covered 32% of the surface at the moment of treatment implementation [30]. The structure of the habitat was an open landscape with isolated groups of stacked logs covering less than 5% of the treatment area. The most characteristic microhabitat of this treatment was one devoid of dead wood (the logging slash had mostly decomposed by the time of sampling) and with herbs and grasses. Hence, in the SL treatment we sampled soils in this “bare-soil” microhabitat”.

The reviewer points out that without knowing the fuel load, “differences in the soil community can only be attributed to treatment differences”. Well, this is in part the objective of our work, to study how differences in post-fire burnt wood management may create differences in soil macoarthropod communities keeping ceteris paribus conditions. We understand that having data on fuel loads may improve the potential for comparison among studies, and we have done the best we can to incorporate these data, but we feel that the reviewer’s concern is beyond the objective and the relevance of our study. We are testing how burnt-wood management affects soil fauna, we do it with an unusually large and replicated experimental design, and we address a group of organisms that has been largely neglected in the studies on the effect of post-fire forest management. In addition, after the two rounds of revision (and thanks to them) we are providing more accurate information about the dasometric characteristics of the forest, including wood biomass. We honestly do not reach to understand the concern of the reviewer to interpret our results.

Finally, the reviewer considers unfortunate that factors that may drive soil community characteristics, such as downed wood, soil moisture, soil temperature, etc., were not measured. We completely agree with the reviewer that knowledge of these factors (and of many others) is always of interest. However, this does not preclude the interpretation of our results, and in fact such factors are considered in our discussion (341-343 and 372-375). Here, we are using a well planned experimental design that allows us to draw robust conclusions from statistical analysis, and we may conclude in a solid way that post-fire wood management affected soil macroarthropod communities –or not– in the ways that we describe. We are convinced that our study is not in any way flawed by the lack of additional environmental data.

In any case, we have rephrased some parts of the ms (hopefully in line with the reviewer’s concern), besides adding the wood amount resulting from the model in the previous manuscript version. Additionally, we have mentioned in the discussion the potential limitation of not knowing the exact amount of wood available at the time of soil sampling, as requested by the reviewer’s initial comment.

Thank you again for your time, and we hope that we have now solved this point satisfactorily.

References

Lizarralde, I., F. Rodríguez, and F. Bravo. 2017. Innovation in the Value Chain of Wood Products: Data, Equations and Life-Cycle Analysis. Pages 235–249 in F. Bravo, V. LeMay, and R. Jandl, editors. Managing Forest Ecosystems: The Challenge of Climate Change. Springer, Cham.

Rodríguez, F., M. Broto, and I. Lizarralde Torre. 2008. CubiFOR : Herramienta para cubicar , clasificar productos y calcular biomasa y CO 2 en masas forestales de Castilla y León. Revista Montes 95:33–39.

This manuscript is a resubmission of an earlier submission. The following is a list of the peer review reports and author responses from that submission.

Round 1

Reviewer 1 Report

The present study assesses the impacts of two different types of deadwood removal treatments in severely burned areas on soil macroinvertebrates at two different elevations. The study finds an interaction between the influence of elevation and treatment type on soil macroinvertebrate abundance. There was no influence of microhabitat on soil invertebrates.

Overall, I found this manuscript to be a rather frustrating read. Though I commend the author’s effort in writing a manuscript that clearly contains a number of moving parts, I don’t think they succeeded in properly portraying nor providing reasoning for all aspects of their study design. The author’s objectives and methods section needs substantial clarification. As it currently stands, I don’t feel comfortable assessing the appropriateness of the analyses of this manuscript until the study design has been clarified. Moreover, the discussion is confusing and begins with conclusions that simply cannot be drawn from this study without an untreated control. Substantial re-organisation and clarification in writing will be required before this paper would be acceptable for publication. I summarise major comments below as well as some line-by-line comments, though I stopped line-by-line comments in the results section.

Major comments:

1)      The authors study design focuses on plots at two different elevations that they subsequently compare in their analysis. Although they mention elevation in their abstract, they don’t discuss anything about the potential relevance of elevation in altering the impacts of deadwood treatments in the introduction, nor do they discuss elevation in the hypotheses stated in the introduction. It is unclear reading their manuscript why they are utilising information from two different elevations and why elevation is important to their study question. This is particularly frustrating when elevation came out to be a prominent driver of patterns they found in their results.

2)      The methods section is confusing and currently unrepeatable. I have highlighted a number of issues in the line-by-line comment section below. To summarise, the authors need to clarify what constitutes a plot, subplot, and sampling point. Also, clarify treatment type from microhabitat and elevation in regards to plots, subplots and sampling points. Was a single core taken at each sampling point? How were sampling points distributed? How many sampling points were there per subplot, per treatment, per plot? Most importantly, how did the authors get from having 12 treatment plots to having 360 soil samples?

3)      The analytical approach in the methods is framed under 3 hypotheses which were outlined in the introduction. There are a lot of components in this study which make it difficult to follow. Why not frame the statistical analyses section and results under those same hypotheses, seeing as the authors specifically state they had to conduct analyses for each hypothesis separately? It could clarify some of their analysis.

4)      The authors make conclusions in the first paragraph of their discussion centered around the impacts of deadwood management on post-fire arthropod abundance, however, they can’t infer anything about the general impacts of deadwood management because they don’t have a control site that was not treated with deadwood management. The only thing that they can discuss are differences in the types of deadwood management applied. The second paragraph discusses the impacts of fire on arthropods, but they didn’t study sites that were burned compared to those that were unburned, so this also seems irrelevant.

Line-by-Line Comments:

Line 23-24: Did arthropod abundance and richness decrease or macroinvertebrate community?

Line 26-27: No significant effect of microhabitat on what?

Line 35: What is ‘it’?

Line 35-40: The authors should provide more specific details in this paragraph about how invertebrate diversity can influence things like human health and ecosystem functioning.

Line 54: Salvage logging and other post-fire management treatments have been found to increase fine woody debris in a number of studies (e.g. Donato et al. 2006, Science; McIver & Ottmar 2007, Forest Ecology and Management; Donovan et al. 2019, Forests).

Line 56-58: Do you have any literature to support this statement?

Line 80-81: Please state the type of pine forest and shrublands.

Line 82-83: This statement makes it sounds as though this was a homogenous wildfire. I assume that not every inch of the wildfire consumed ‘all leaves, twigs, and litter’. Was this the general case for the two plots that the authors studied? Also, it appears that this sentence was copied word for word from another published manuscript.

Line 104: Were there 12 subplots per plot? Per treatment within each plot?

Line 105: What was considered ‘bare soil’? Just not covered by a log? Could it have vegetation?

Line 106: What was considered ‘under-log’. Did woody debris have to be a certain diameter to be classified as a log? Was it always paced under the center of the log? Did the log have to be a certain height off the ground? How did you select a log under which to sample? Randomly?

Line 108-109: It is unclear why it is important to measure across treatments and microhabitats.

Line 112-113: What is a sampling point? When did these come into the design? I thought that cores needed to be 50 cm apart (Line 107)? Where does 10 m come into play?

Line 133-135: I am unclear what “effect of deadwood treatment encompassing the greater variety of microhabitats in the PC treatment” means. You need to clarify this and keep your phrasing similar to the questions/hypotheses outlined in the introduction.

Line 143: Why exclude ants? Move Line 156-158 up so that this is clear from the beginning.

Line 215: What does ‘simpler analysis’ mean?

Reviewer 2 Report

The study could have a high value and novelty as few studies have analysed the effects of post-fire deadwood management on soil macroinvertebrate communities. Yet, it has some points that should be carefully revised.

MAJOR COMMENTS

1. Although the aim of the study was to assess post-fire effects of deadwood management, the study was conducted 10 yrs after the fire event. This is an extraordinary time lag for a Mediterranean-type ecosystem as they are known to show a fast recovery after fire. Therefore, there may be a lot of confounding effects: e.g. differences caused by type of vegetation recovered rather than by the presence of deadwood. Unfortunately, no information about the current vegetation is provided. Any possibility to get it?

2- The number of specimens sampled is extremely reduced for a study on soil macroinvertebrates (Line 181: ….360 soil samples yielded 525 macroinvertebrate individuals belonging to 13 orders). Moreover almost no individuals were captured in some of the experimental situations (i.e. bare soil- salvage logging at high altitude or dead-wood and partial cutting at high altitude, Table A1). This should be acknowledged  as a potential limitation for the conclusions drawn from the study.

3- By far, two of the more abundant groups of macroinvertebrate found were Hemiptera and Lepidoptera (Table A1). By no means, can these two groups be considered as members of the “soil macroinvertebrate community”. Moreover, their presence in the plots is probably more determined by the vegetation type rather than by the presence of deadwood per se, as they do not feed on this resource. Some comments on this should be included in the Discussion section.

MINOR COMMENTS

Lines 93-94: Notice that leaving the branches “mechanically masticated and the slash spread on the ground” may represent a large amount of wood. Any idea? A comment on that should be included as this is not “bare soil” properly speaking.

Lines 114-116. Why did you focus in macroartropods? This should be clarified… Similarly, the method selected to collect the samples should be better justified. Probably, this is not the best method when the interest of the study are the diversity and abundance  of macroarthropods. See Edwards C.A. 1991. The assessment of populations of soil inhabiting invertebrates). Why not several methods? Tullgren funnels, pitfall traps, etc.

Lines 257-260.  At least, concerning the study by Mateos et al. (2011), fire cannot be invoked as the cause of differences in the abundance of macroarthropods as post-fire conditions were also studied there.

Lines 257-260. Differences among studies could also arise from differences in the sampling methods. E.g.  One of the studies cited used Tullgren funnels (Jabin et al. 2004). This should be acknowledged.

Lines 272-277. Even though the authors claim that “the timing of sampling considered the difference in phenology across the two plots” (Lines 110-111), the lower values in the plot at a greater altitude might be influenced by the sampling procedure. At least, this limitation of the study should be acknowledged.

Lines 302-303. I am afraid I do not fully understand the explanation based on the “low overall abundance of organisms”

Table 2/Table 3 There are some titles in bold and others in plain text. Why?

Reviewer 3 Report

I added some corrections and suggestions on the attached pdf file.

Just a couple of suggestions for future research:

1) a low cost Berlese-Tullgren system would allow you to evaluate also the fire effects on soil mesoinvertebrates which are much more abundant and results could be more robust than those based on marcoinvertebrates only. I'd like to know how "my" proturans react to fire and postfire management.

2) it could be interesting to select also a couple of unburnt plots with the same environmental-ecological characteristics of the studied plots to compare the assemblages on unburnt and burnt areas. Another interesting experiment could be to make an agreement with the authority responsible of forest management to let one or more small plots unmanaged after fire to assess how biodiversity is influenced by burnt deadwood abundance.

Comments for author File: Comments.pdf