the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 04 Apr 2024
Afforestation induced shift in the microbial community explains enhanced decomposition of subsoil organic matter
Abstract. Afforestation on former pastures is widely promoted due to its potential to increase soil organic carbon sequestration while reducing CO2 emission. The establishment of a forest on a former pasture, however, might affect soil microbial community structure due to the alteration in substrate quality and thus impact carbon cycling in soils. To date, it still remains an open question if and how afforestation may alter the soil microbial community structure and related implications for soil organic matter stabilization. In addition, the majority of studies focuses on low altitude regions which results in uncertainties regarding the effects of afforestation on soil microbiology in mountainous regions. In this study, we aimed to investigate the consequences of afforestation of a subalpine pasture with Norway spruce (Picea abies L.) on the soil microbial community structure following 130 years of afforestation. We used a multi-proxy biomarker approach, including phospholipid fatty acids (PLFAs) and glycerol dialkyl glycerol tetraethers (GDGTs), to explore the shift in the microbial community structure following afforestation with increasing forest stand age. We found a significant increase in bacterial communities (Gram- and Gram+ bacteria) with increasing forest stand age compared to the pasture. This trend, however, was reversed with increasing forest age when considering GDGT biomarkers. We thereby conclude that the microbial community in the pasture and forests of different forest stand ages utilize different carbon substrates as food resource, which is a direct consequence of the modification in litter input after the conversion of a pasture to forests. Our data further suggests that an increase in the soil organic matter decomposition results from the alteration in the microbial community structure, which is especially evident in the subsoil of the 130-year-old forest stand ages.
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RC1: 'Comment on egusphere-2024-870', Anonymous Referee #1, 04 Jul 2024
Review for “Afforestation induced shift in the microbial community explains enhanced decomposition of subsoil organic matter”, egusphere-2024-870 by Tatjana C. Speckert, Arnaud Huguet and Guido L.B. Wiesenberg submitted to Biogeosciences.
General comments
The authors use two proxies, PLFAs and GDGTs, to study microbial community composition along a well-characterized forest stand age gradient (land use change from pasture to forest). The manuscript is well written and presents solid data from an interesting study. Most formal criteria in terms of data quality, presentation, statistical evaluation, etc. are met, and all results are presented in an objective way. However, I get the impression that the paper in its recent form confirms what we already knew.
For example, “enhanced decomposition” is in the title, but I can’t see where this is discussed or shown by the authors for these samples. On the other hand, the obvious disagreement between the two proxies is not discussed at all, although this would be the major surprising result. As the authors point out themselves, this might be related to the differences in turnover times of the chosen markers (PLFAs reflect more recent microbial community, GDGTs longer-term community); it would be very interesting to deepen the discussion in that regard. The authors discuss the effect of seasonality but do not discuss the sensitivity of PLFAs and GDGTs to seasonal differences (e.g., [1], or from their own experience). The authors also miss that the studied afforestation sequence may be unique (especially looking at the weak age gradients due to the seemingly “outlying” 55-year old site) and hence miss pointing out that one should study this effect not only using one gradient in future research.
Looking at the paper as a whole, I suggest major revisions. The scope needs to be sharpened and the data need to be presented in a way that answers questions related to clear hypotheses which are not obvious now, besides that vegetation shift equals soil microbiome shift; if the paper is about enhanced decomposition and subsoil, there should be hypotheses related to these processes, or soil horizons. Figures should help to answer the questions related to the hypotheses and not merely present all data in an albeit objective, yet undirected way (“story missing”).
Yours sincerely
Specific comments
- Title seems misleading. Enhanced decomposition of subsoil organic matter is not discussed
- Line 31-44: This framing somehow is misleading as your own data show that there is no SOC sequestration effect; maybe base this section more on the surprising finding of no increased SOC stocks despite 130 years of afforestation in your prior paper, and how SOM quality and lability might still be different
- Line 82: Entering “GDGTs PLFAs” in Google Scholar, I find ~190 results and already among the first five is a study from mountain sites [2] which seems to be excluded because it does not explicitly deal with afforestation gradients; I plead the authors to widen their focus to discuss their data, especially to check whether other authors have found a similar mismatch in total PLFA and GDGT yields
- Lines 91 and after: This section is very confusing as it mixes up labile/ recalcitrant/ pasture/ aged forest stands; I’m also not sure whether the sole evidence of higher C/N ratios justifies the assumption of a higher “recalcitrance”; this should be backed up by short-term incubations or sth. alike. The paragraph should end strong and with clear messages as its purpose is to clearly explain the outset of the manuscript
- Line 168: I do not really see how the GDGT indices help the study. It would make more sense in my view to use the sum of all PLFAs and GDGTs to contrast the patterns observed in their total yields across the gradient and depths; both are proxies of microbial bio/necromass and could help to sort out source contributions to SOM; not sure how pH or temperature-correlated indices help e.g., in line 352 – 358, besides providing reference values to compare with other studies (which may be more relevant to ensure quality of the data?). In short, I would put much more focus on the apparent mismatch between markers of microbial bio/necromass and what could explain this. Some starters are already brought up in the discussion, but this should be deepened (see also point 7).
- Line 287-291: Please deepen this section more. Try to provide some estimate how sensitive PLFAs and GDGTs could be to seasonal variation from others [1] or your own experience, or at least point out that this should be tested in future.
- Conclusions: Disagreement between PLFAs and GDGTs is not mentioned at all. What is the specific community shift that you mean? And how can you be sure that this is solely explained through the changed litter input if you cannot even rule out seasonality effects and state yourself that GDGTs and PLFAs might represent completely different community dynamics based on their turnover? The statements on the link between microbiome shift and SOM decomposability/ quality seem far-fetched to me given what the authors have presented in the MS. Instead of longer afforestation sequences as suggested in line 434, I would rather advise to increase the number of afforestation gradients from 1 to at least 3 in different geologic/ climatic settings, and discuss the uniqueness of the site and why the 55-yr forest stand obviously disagrees with linear changes with forest stand age. It could also be discussed whether today’s pasture is an appropriate “control” as it does not represent the state of the pasture 130 years ago.
- “Subsoil” is not even mentioned in the conclusions despite it being mentioned prominently in the title. Revise the paper accordingly.
Technical corrections
Abstract
Line 24 How was it reversed? Be more specific
Line 25-28 These statements seem unjustified by the information that you provide in the abstract, provide more justification
Introduction
Line 40 “plays” à “play”
Line 41- 44 “potentially”. As this seems to be a central assumption of the paper it would be good to repeat some of the findings that lead to this statement and how it could be tested (and will be tested here, although I must say that I didn’t get the impression that this was shown, see my general points before).
Line 46-48 Link unclear, be more specific why one controls the other
Line 63 Why “even though”?
Line 66 “possibly feeding” – GDGTs do not feed root C. Please use correct wording. This also appears in other places in the MS (Line 347)
Line 82 To the best to our à To the best of our
Line 94 “to the pasture where less easily” this contradicts your prior statement that older sites have a more recalcitrant OM.
Line 96 “with increasing forest stand ages due to the more easily” again, this contradicts with what you stated earlier à clarify what sources of OM you consider easily/ hardly degradable and why (back up with literature), and how this affects allover SOM lability/ stability along afforestation and depth gradients
Methods
Line 113 How much grams of soil were used? how much absolute volume of solvents were used? When were the extractions performed if samples were taken already in 07/2020?
Line 120 The degree of detail for the LC gradient description is much lower than for the GC in the next section. Please provide more method details.
Line 129 How much absolute volume was used?
Line 136, 139 “Was done” à please rephrase.
Line 153 Please explain why p<0.95 is appropriate as a p-level for a Tukey HSD test
Line 154 How can one perform an analysis with one (n=1) replicate? This means to me, there were no replicates.
Line 162 standardized how? Mean=0, SD=+/- 1?
Results
In general, the results section was very heavy to read. Lots of information (good because: objective, but hard to follow because: unfiltered, no story apparent; no obvious finding that jumps at the reader). It might be helpful to generalize the results a bit more (e.g., contrasting total yields of PLFAs vs GDGTs along the sequence as indication of changed turnover of SOM, i.e., fresh biomass vs. older biomass/ necromass, and shifted community composition?). I also cannot see how the sections 4.1 – 4.4 are related to any scientific hypothesis brought up in the introduction (For example: 1 Resolving depth effects. 2 Resolving age effects. 3 Resolving combined depth/ age effect, i.e., decomposition degree effect.)
Discussion
Line 334 AFM à AMF
Line 334 “due” seems misplaced, sentence reads wrong
Line 355 Delete “range value”
Line 380ff Maybe this could be due to fewer but larger roots, i.e., less “homogenous” root system in forests?
Figures
In the results, there is a lot of mentioning of significance tests, but these are not reflected in the figures. Maybe asterisks or letters could be added to indicate significant correlations/ differences (this applies to Fig 02, Fig 05, and all Fig S1-S9)
Fig 03 Please add “depth” as a variable or color the dots according to depth
Fig 07 Same as Fig 03
Fig S1-S9 Think about using symbols for depth and colors for sites; the way it is used now, one is not necessary. Add significance levels to the r values. Only discuss significant correlations in the results
Refs cited
[1] https://www.sciencedirect.com/science/article/pii/S0038071712003252
[2] https://academic.oup.com/ismej/article/14/4/931/7474800
Citation: https://doi.org/10.5194/egusphere-2024-870-RC1 -
AC1: 'Reply on RC1', Tatjana Carina Speckert, 23 Aug 2024
Review for “Afforestation induced shift in the microbial community explains enhanced decomposition of subsoil organic matter”, egusphere-2024-870 by Tatjana C. Speckert, Arnaud Huguet and Guido L.B. Wiesenberg submitted to Biogeosciences.
General comments
The authors use two proxies, PLFAs and GDGTs, to study microbial community composition along a well-characterized forest stand age gradient (land use change from pasture to forest). The manuscript is well written and presents solid data from an interesting study. Most formal criteria in terms of data quality, presentation, statistical evaluation, etc. are met, and all results are presented in an objective way. However, I get the impression that the paper in its recent form confirms what we already knew.
For example, “enhanced decomposition” is in the title, but I can’t see where this is discussed or shown by the authors for these samples. On the other hand, the obvious disagreement between the two proxies is not discussed at all, although this would be the major surprising result. As the authors point out themselves, this might be related to the differences in turnover times of the chosen markers (PLFAs reflect more recent microbial community, GDGTs longer-term community); it would be very interesting to deepen the discussion in that regard. The authors discuss the effect of seasonality but do not discuss the sensitivity of PLFAs and GDGTs to seasonal differences (e.g., [1], or from their own experience). The authors also miss that the studied afforestation sequence may be unique (especially looking at the weak age gradients due to the seemingly “outlying” 55-year old site) and hence miss pointing out that one should study this effect not only using one gradient in future research.
Looking at the paper as a whole, I suggest major revisions. The scope needs to be sharpened and the data need to be presented in a way that answers questions related to clear hypotheses which are not obvious now, besides that vegetation shift equals soil microbiome shift; if the paper is about enhanced decomposition and subsoil, there should be hypotheses related to these processes, or soil horizons. Figures should help to answer the questions related to the hypotheses and not merely present all data in an albeit objective, yet undirected way (“story missing”).
Yours sincerely
Thank you for your feedback and your helpful comments! We do agree that the title emphasizes more on decomposition than is currently reported in this version of the manuscript. We will change the title accordingly and no longer focus only on the decomposition. We will further discuss more on the observed difference between the two proxies in relation to the different land-use types and forest age. We will thereby also highlight in the next version of the manuscript the uniqueness of a 130-year-old afforestation sequence.
Specific comments
- Title seems misleading. Enhanced decomposition of subsoil organic matter is not discussed
Thank you for pointing this out. We agree and we will change this accordingly in the next version of the manuscript.
- Line 31-44: This framing somehow is misleading as your own data show that there is no SOC sequestration effect; maybe base this section more on the surprising finding of no increased SOC stocks despite 130 years of afforestation in your prior paper, and how SOM quality and lability might still be different
Thanks for mentioning this. We will add more citations in the introduction part with studies reporting no increase in SOC stocks following afforestation. Plus, we will add more information on how SOM quality and lability might be different.
- Line 82: Entering “GDGTs PLFAs” in Google Scholar, I find ~190 results and already among the first five is a study from mountain sites [2] which seems to be excluded because it does not explicitly deal with afforestation gradients; I plead the authors to widen their focus to discuss their data, especially to check whether other authors have found a similar mismatch in total PLFA and GDGT yields
Thank you for your suggestion. We will add more literature about afforestation and on alpine environments.
- Lines 91 and after: This section is very confusing as it mixes up labile/ recalcitrant/ pasture/ aged forest stands; I’m also not sure whether the sole evidence of higher C/N ratios justifies the assumption of a higher “recalcitrance”; this should be backed up by short-term incubations or sth. alike. The paragraph should end strong and with clear messages as its purpose is to clearly explain the outset of the manuscript
Thank you for this comment and we agree. We will rephrase this in the next version of the manuscript
- Line 168: I do not really see how the GDGT indices help the study. It would make more sense in my view to use the sum of all PLFAs and GDGTs to contrast the patterns observed in their total yields across the gradient and depths; both are proxies of microbial bio/necromass and could help to sort out source contributions to SOM; not sure how pH or temperature-correlated indices help e.g., in line 352 – 358, besides providing reference values to compare with other studies (which may be more relevant to ensure quality of the data?). In short, I would put much more focus on the apparent mismatch between markers of microbial bio/necromass and what could explain this. Some starters are already brought up in the discussion, but this should be deepened (see also point 7).
Thank you for your suggestions. However, we think that these GDGT indices represent a valuable information for the represented manuscript. On the one hand the GDGTs indices were useful to check their reliability. On the other hand, these indices reflect the distribution of the individual compounds. Therefore, we decided not to focus only on the total concentration as we wanted to provide information in the variation of the GDGTs, which would not be possible if we only report sum values.
- Line 287-291: Please deepen this section more. Try to provide some estimate how sensitive PLFAs and GDGTs could be to seasonal variation from others [1] or your own experience, or at least point out that this should be tested in future.
Thank you for this comment. We are aware that seasonal variation can affect the distribution and concentration of PLFAs and GDGTs. However, we think that seasonality in this study does not play a big role as we collected all the samples at the same time, therefore any comments on the alteration in the investigated PLFA/GDGT composition and concentration would be speculative. But we do agree to add this information and its importance for future studies to include the seasonality in their research.
- Conclusions: Disagreement between PLFAs and GDGTs is not mentioned at all. What is the specific community shift that you mean? And how can you be sure that this is solely explained through the changed litter input if you cannot even rule out seasonality effects and state yourself that GDGTs and PLFAs might represent completely different community dynamics based on their turnover? The statements on the link between microbiome shift and SOM decomposability/ quality seem far-fetched to me given what the authors have presented in the MS. Instead of longer afforestation sequences as suggested in line 434, I would rather advise to increase the number of afforestation gradients from 1 to at least 3 in different geologic/ climatic settings, and discuss the uniqueness of the site and why the 55-yr forest stand obviously disagrees with linear changes with forest stand age. It could also be discussed whether today’s pasture is an appropriate “control” as it does not represent the state of the pasture 130 years ago.
Thanks for your suggestion and we will provide more information in the conclusion on the observed difference between the PLFAs and GDGTs and also focus on the challenges of our afforestation sequence, e.g. whether the 130-year-old forest might represent the state of the pasture or not.
- “Subsoil” is not even mentioned in the conclusions despite it being mentioned prominently in the title. Revise the paper accordingly.
Thanks for this comment and we fully agree and will add the missing information on the subsoil in the conclusion in the next version of the manuscript.
Technical corrections
Abstract
Line 24 How was it reversed? Be more specific
Thanks for the comment. We will add additional information about the observed opposite reversed trend in the next version of the manuscript. E.g., “This trend, however, was reversed with a decreasing bacterial community with increasing forest age when considering GDGT biomarkers”
Line 25-28 These statements seem unjustified by the information that you provide in the abstract, provide more justification
Thanks for pointing this out. We will emphasize more on this in the next version of the manuscript to strengthen our statement.
Introduction
Line 40 “plays” à “play”
Thanks for finding this mistake and we will correct this in the next version of the manuscript.
Line 41- 44 “potentially”. As this seems to be a central assumption of the paper it would be good to repeat some of the findings that lead to this statement and how it could be tested (and will be tested here, although I must say that I didn’t get the impression that this was shown, see my general points before).
Thanks for mentioning this. We agree and will add the findings of the cited paper in the introduction.
Line 46-48 Link unclear, be more specific why one controls the other
Thanks for this comment and we will add more information on this in the introduction to make it clear why the chemical composition of litter inputs affects the soil microbial community.
Line 63 Why “even though”?
Thanks for the comment and we will delete “even though” in the next version of the manuscript.
Line 66 “possibly feeding” – GDGTs do not feed root C. Please use correct wording. This also appears in other places in the MS (Line 347)
Thanks for mentioning this and we change this accordingly. “In contrast with archaeal GDGTs, bacterial GDGTs are constituted of branched alkyl chains instead of isoprenoid ones and are referred as branched GDGTs (brGDGTs). Such brGDGT producing bacteria are known to use root-derived carbon as the preferential food source (Huguet et al., 2012; Gocke et al., 2016).”
Line 82 To the best to our à To the best of our
Thanks for finding this mistake and we change accordingly in the next version of the manuscript.
Line 94 “to the pasture where less easily” this contradicts your prior statement that older sites have a more recalcitrant OM.
Thanks for mentioning this. And we agree that it was not clearly formulated. The statement “where less easily decomposable organic matter predominates” is correct for the forest and not for the pasture. We will rephrase this in the next version of the manuscript: “Due to the already reported alteration in the litter quality towards more recalcitrant (high C:N ratio) litter input in this subalpine afforestation sequence (Hiltbrunner et al., 2013; Speckert et al., 2023), we hypothesize an increase in Gram+ bacteria and in the fungal communities with increasing forest age where less easily decomposable organic matter predominates, in comparison to the pasture.”
Line 96 “with increasing forest stand ages due to the more easily” again, this contradicts with what you stated earlier à clarify what sources of OM you consider easily/ hardly degradable and why (back up with literature), and how this affects allover SOM lability/ stability along afforestation and depth gradients
Thanks for your suggestions and we agree that backing up with literature would strengthen our expectations for the mentioned hypothesis. We will change this accordingly. “Moreover, we hypothesize a larger abundance in core lipid GDGTs in the pasture compared to the forest soils with a decline in their abundance with increasing forest stand ages due to the more easily decomposable organic matter in soils under pasture than under forest use. While the OM input in pastures is dominated by leaf tissues and rhizodeposit (Solly et al.,2013) the OM input in forests usually occurs through leaves, needles and twigs, which accumulates in organic horizons (Nadelhoffer et al., 2004). The different origin (above- vs. belowground plant biomass) of SOM not only results in a different SOM composition, but it can also result in SOM components that differ in their stability (Pisani et al.,2016).”
Methods
Line 113 How much grams of soil were used? how much absolute volume of solvents were used? When were the extractions performed if samples were taken already in 07/2020?
Thanks for mentioning this. For the mineral soil samples 10 – 15 g of dried soil were extracted. Extractions (Soxhlet and GDGT) were performed in 2021. We will add this information in the next version of the manuscript : “ Dried soil samples (10 – 15 g) were extracted using Soxhlet extraction with 100ml of dichloromethane:methanol (DCM:MeOH; 93:7, v/v) and evaporated until constant weight after filtration (Wiesenberg and Gocke, 2017).”
Line 120 The degree of detail for the LC gradient description is much lower than for the GC in the next section. Please provide more method details.
Thanks for pointing this out. We will add more method details: “GDGTs were eluted isocratically for 25 min with 82 % A 18 % B (A is hexane; B is hexane isopropanol), followed by a linear gradient to 65 % A 35 % B in 25 min, a linear gradient to 100 % B in 30 min, and back to 82 % A 18 % B in 4 min, maintained for 50 min.”
Line 129 How much absolute volume was used?
For the extraction of the PLFA approx. 12ml were used for the topsoil (0-10cm) and approx. 20ml were used for the subsoil (15 - 45cm).
Line 136, 139 “Was done” à please rephrase.
Thanks for mentioning this. We rephrase this is the new version of the manuscript: “Compound identification was performed on a gas chromatograph (GC; 6890 Agilent Technologies, Inc.) coupled to a mass selective detector (MSD; 5973N Agilent Technologies, Inc.) equipped with a split/splitless injector. The identification of the individual compounds was carried out by comparison of mass spectra with external standards as well as with the NIST mass spectra library.”
Line 153 Please explain why p<0.95 is appropriate as a p-level for a Tukey HSD test
The higher the standard deviation, the wider the confidence interval. In other words, if the number of samples is increasing, the confidence interval is decreasing. Based on our sample number in this study, we decided to use the commonly used confidence interval of p<0.95.
Line 154 How can one perform an analysis with one (n=1) replicate? This means to me, there were no replicates.
Thanks for mentioning this. And it is right. We will change this in the next version of the manuscript to make it clearer: “The PLFA analysis was performed in duplicates (n = 2) and the GDGT analysis was performed without replicates (n = 1) for each stand age (0 to 130 years).” Because of time and financial constraints, more analyses were not possible in the course of the project.
Line 162 standardized how? Mean=0, SD=+/- 1?
The standardization was performed for the PCA analysis to make the variables comparable – to achieve standard deviation one and mean zero.
When standardizing variables, the data was transformed as follow:
(xi-mean(x))/sd(x)
Where mean(x) is the mean of x values, and sd (x) is the standard deviation (SD).
Results
In general, the results section was very heavy to read. Lots of information (good because: objective, but hard to follow because: unfiltered, no story apparent; no obvious finding that jumps at the reader). It might be helpful to generalize the results a bit more (e.g., contrasting total yields of PLFAs vs GDGTs along the sequence as indication of changed turnover of SOM, i.e., fresh biomass vs. older biomass/ necromass, and shifted community composition?). I also cannot see how the sections 4.1 – 4.4 are related to any scientific hypothesis brought up in the introduction (For example: 1 Resolving depth effects. 2 Resolving age effects. 3 Resolving combined depth/ age effect, i.e., decomposition degree effect.)
Thanks for this comment. We will reduce the text in the result section and focus on the main results necessary for our discussion part.
Discussion
Line 334 AFM à AMF
Thanks for pointing this out and we will fix this typo in the next version of the manuscript.
Line 334 “due” seems misplaced, sentence reads wrong
Thanks for pointing this out and we will replace “due” by “resulting from the presence of”.
Line 355 Delete “range value”
Thanks for mentioning this and we will delete this in the next version of the manuscript. “Also, the IR6Me ratio (Eq. 2) was in the same range for the pasture the 40-year-old forest and significantly higher compared to the 55-year-old and 130-year-old forest.”
Line 380ff Maybe this could be due to fewer but larger roots, i.e., less “homogenous” root system in forests?
Thanks for your suggestions. There are existing data about root frequencies (fine and coarse roots) counted in the field (Speckert et al., 2023) with which we cross-checked to see if the root size has a potential effect. And there was no effect detectable between roots size and the observed maxima of brGDGTs in this study site. Another argument is the lower soil pH in the 130-year-old forest, which is related to a higher abundance of brGDGTs.
Figures
In the results, there is a lot of mentioning of significance tests, but these are not reflected in the figures. Maybe asterisks or letters could be added to indicate significant correlations/ differences (this applies to Fig 02, Fig 05, and all Fig S1-S9)
Thanks for these suggestions and we will add asterisks in the figures to indicate the significance values.
Fig 03 Please add “depth” as a variable or color the dots according to depth
Thanks for this comment. We will add “depth” as a variable and will classify in topsoil (0-5cm; 5-10cm) and into subsoil (10-45cm).
Fig 07 Same as Fig 03
Fig S1-S9 Think about using symbols for depth and colors for sites; the way it is used now, one is not necessary. Add significance levels to the r values. Only discuss significant correlations in the results
Thanks for this comment and we will add (same as above) depth as a variable to improve the information in our figures.
Refs cited
[1] https://www.sciencedirect.com/science/article/pii/S0038071712003252
[2] https://academic.oup.com/ismej/article/14/4/931/7474800
Thank you.
Citation: https://doi.org/10.5194/egusphere-2024-870-AC1
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RC2: 'Comment on egusphere-2024-870', Anonymous Referee #2, 15 Jul 2024
This manuscript reports on an observational and comparative study of soil microbial groups in grassland and forested soils of different ages. This topic in not without interest and aspects of the research conducted in this study have potential to interest the scientific community. However, the technique chosen to assess the microbial diversity is limited and not the most adequate one for this kind of study. The reason of choosing these methods should be addressed and the limitation of these methods compared to other which are largely used discussed. The manuscript would also improve with a deeper analysis of the data and a clearer discussion, better linked to the hypotheses.
Title: the title of this paper is misleading as decomposition is not assessed. I suggest adapting the title so it describes better the output of the study.
Introduction: The use of PLFA to study the biodiversity and abundance of prokaryotes and fungi in soils is limited from my point of view. It would be essential to explain in the introduction the advantage of using this technique over the nowadays largely used molecular methods such as eDNA metabarcoding (amplicon sequencing) or group specific qPCRs assays to assess microbial diversity and abundance in soils. Similarly, it would be necessary to state why it was useful and judicious to use GDGTs to study archaea and bacteria instead of molecular method such as eDNA metabarcoding or metagenomics. Archaea are relatively rare and not dominant in grassland and forest soils, usually accounting for less than 10% of the prokaryotic community. Why was it important to study them in that study?
Lines 74-78: Fungi are microbes! The expression “soil microbial and fungal communities” is misleading.
Hypotheses: The rationale behind the two hypotheses is not well described in the introduction. Moreover, the second hypothesis is confusing and would need to be rephrased. Also, some additional hypotheses could be formulated. For example: What would be expected according to soil depth? What would be expected regarding the ecology of the fungi assessed (saprotrophic versus mycorrhiza)? …
Methods:
Why were samples collected from 5 soil pits in the pasture whereas only 3 soil pits were used for each forest site? The reason for this unbalanced experimental design needs to be addressed.
In the data analysis: were the n=2 for PLFA and n=1 for GDGT technical replicates? Or these were true replicates? This is not clearly described. Also, the description of the number of data point is confusing (line 160-164). Why are each forest age have a different number of data points?
Paragraph 3.2: please describe the structure for the roman numbers and the letters (a, b, c) for the equations (could also be included in supplementary material).
Results: The data collected could be further explored and analysed according to the hypotheses. For example, the ordination plot presented in figures 3 and 7 would be more informative in my sense if all data points (from pasture and 40, 55 and 130 yo forests) would be presented in a same ordination plot, for a direct comparison of the “community” of the PLFA in the different sites. Then, the correlation with the soil properties and compounds would be done across the different soil and it would potentially become clear which compounds or soil properties would correlate to which soil type.
Discussion: The discussion is rather long and difficult to follow. It would merit a complete re-structuration. I would suggest structuring the discussion according to a newly formulated set of hypotheses. Then the discussion could be more focussed and easier to follow for the reader. For example, a large part of the discussion is discussed the pasture and the forest soils separately (paragraphs 5.1 and 5.2), whereas the goal of the paper is to compare these types of soils.
Some paragraphs of the discussion also do not place the findings into a larger ecological context, such as in the 2nd and 4th paragraphs of the discussion, which essentially try to explain why certain type of GDGTs are more prominent in certain soils but does not address what it would potentially mean for the functioning of the ecosystems, especially when comparing pasture and forest of different ages.
On the other hand, in some parts, the discussion is quite speculative, and several argumentations should be moderated. For example: “The change in the soil microbial community following afforestation on a subalpine pasture is a direct consequence of the alteration in organic matter input…” (line 414). This statement should be put in the context of the limitation of the available data in that study, in which “only” microbial groups with similar traits (G+, G-, etc) or different ecology (saprotrophs, AMF) were assessed and not the entire microbial diversity, and only C and N were measured in the organic matter (or did I miss something?).
Citation: https://doi.org/10.5194/egusphere-2024-870-RC2 -
AC2: 'Reply on RC2', Tatjana Carina Speckert, 23 Aug 2024
This manuscript reports on an observational and comparative study of soil microbial groups in grassland and forested soils of different ages. This topic in not without interest and aspects of the research conducted in this study have potential to interest the scientific community. However, the technique chosen to assess the microbial diversity is limited and not the most adequate one for this kind of study. The reason of choosing these methods should be addressed and the limitation of these methods compared to other which are largely used discussed. The manuscript would also improve with a deeper analysis of the data and a clearer discussion, better linked to the hypotheses.
Thanks for your feedback and comments. We are aware that the proxies used in this study have limitations (e.g. seasonality and short turnover times for the PLFAs). However, the used PLFA method in this paper is well documented and has been proven useful in assessing the composition of the soil microbial community (Frostegard et al., 2010; doi:10.1016/j.soilbio.2010.11.021), especially in terms of land-use change (Gocke et al., 2017 https://doi.org/10.1016/j.scitotenv.2016.09.184; Zong et al., 2020 https://doi.org/10.1016/j.soilbio.2020.108048; Chen et al., 2022 https://doi.org/10.1016/j.ecolind.2022.108852). Additionally, we agree to better connect the discussion part with the formulated hypotheses. We will do so in the next version of the manuscript.
Title: the title of this paper is misleading as decomposition is not assessed. I suggest adapting the title so it describes better the output of the study.
Thanks for this comment and we fully agree. We will change the title accordingly with a focus on the alteration in the microbial community in a long-term afforestation sequence in the next version of the manuscript.
Introduction: The use of PLFA to study the biodiversity and abundance of prokaryotes and fungi in soils is limited from my point of view. It would be essential to explain in the introduction the advantage of using this technique over the nowadays largely used molecular methods such as eDNA metabarcoding (amplicon sequencing) or group specific qPCRs assays to assess microbial diversity and abundance in soils. Similarly, it would be necessary to state why it was useful and judicious to use GDGTs to study archaea and bacteria instead of molecular method such as eDNA metabarcoding or metagenomics. Archaea are relatively rare and not dominant in grassland and forest soils, usually accounting for less than 10% of the prokaryotic community. Why was it important to study them in that study?
Thanks for this comment. We chose the well-established methods like PLFA and GDGT to have a quantitative value, which we do not achieve with methods such as eDNA. We will add a statement in the next version of the manuscript why we selected these methods for our manuscript.
Lines 74-78: Fungi are microbes! The expression “soil microbial and fungal communities” is misleading.
Thanks for this comment and we will rephrase this and simply write soil microbial communities, including both, fungi and microbes.
Hypotheses: The rationale behind the two hypotheses is not well described in the introduction. Moreover, the second hypothesis is confusing and would need to be rephrased. Also, some additional hypotheses could be formulated. For example: What would be expected according to soil depth? What would be expected regarding the ecology of the fungi assessed (saprotrophic versus mycorrhiza)? …
Thanks for your suggestions. We agree and we will add a third hypothesis including the soil depth as a variable.
Methods:
Why were samples collected from 5 soil pits in the pasture whereas only 3 soil pits were used for each forest site? The reason for this unbalanced experimental design needs to be addressed.
Thanks for pointing this out. The number of soil pits was 5 in the pasture to have an adequate number of control samples and 3 in the forest due to time constraints during the sampling campaign.
In the data analysis: were the n=2 for PLFA and n=1 for GDGT technical replicates? Or these were true replicates? This is not clearly described. Also, the description of the number of data point is confusing (line 160-164). Why are each forest age have a different number of data points?
Thanks for mentioning this. The replicates for the PLFA analysis are field replicates. We will change this accordingly in the next version of the manuscript: “The PLFA analysis was performed in duplicates (field replicates with n = 2) and the GDGT analysis was performed without replicates (n = 1) for each stand age (0 to 130 years).”The different number of data points is due to the field replicates as for example in some soil pits the rock material was already present at 35cm instead of 45cm (see Speckert et al., 2023 for the details). Therefore, the different number of data points lies in the nature of field replicates.
Paragraph 3.2: please describe the structure for the roman numbers and the letters (a, b, c) for the equations (could also be included in supplementary material).
Thanks for pointing this out. We agree and we will include the respective structures in the supplement material.
Results: The data collected could be further explored and analysed according to the hypotheses. For example, the ordination plot presented in figures 3 and 7 would be more informative in my sense if all data points (from pasture and 40, 55 and 130 yo forests) would be presented in a same ordination plot, for a direct comparison of the “community” of the PLFA in the different sites. Then, the correlation with the soil properties and compounds would be done across the different soil and it would potentially become clear which compounds or soil properties would correlate to which soil type.
Thanks for your suggestions. We will combine figure 3 and figure 7 in one figure to improve the content of the figure and to have a better comparison between the different land-use types. Additionally, as suggested by reviewer1 we will add “depth” as a variable in our figure to better see the observed differences between top- and subsoil.
Discussion: The discussion is rather long and difficult to follow. It would merit a complete re-structuration. I would suggest structuring the discussion according to a newly formulated set of hypotheses. Then the discussion could be more focussed and easier to follow for the reader. For example, a large part of the discussion is discussed the pasture and the forest soils separately (paragraphs 5.1 and 5.2), whereas the goal of the paper is to compare these types of soils.
Thank you for this comment. We agree and will better connect the discussion part with our formulated hypotheses and focus more on the difference between the two investigated land-use types.
Some paragraphs of the discussion also do not place the findings into a larger ecological context, such as in the 2nd and 4th paragraphs of the discussion, which essentially try to explain why certain type of GDGTs are more prominent in certain soils but does not address what it would potentially mean for the functioning of the ecosystems, especially when comparing pasture and forest of different ages.
Thank you for your suggestion. With the used microbial markers in this manuscript, it is not possible to give a general statement on ecosystem functioning. We will highlight the differences within the GDGT composition in the two observed ecosystems – alpine forests and pastures- clearer in the next version of the manuscript to make it easier for the reader to follow and to understand how these observed ecosystems differ in their microbial community.
On the other hand, in some parts, the discussion is quite speculative, and several argumentations should be moderated. For example: “The change in the soil microbial community following afforestation on a subalpine pasture is a direct consequence of the alteration in organic matter input…” (line 414). This statement should be put in the context of the limitation of the available data in that study, in which “only” microbial groups with similar traits (G+, G-, etc) or different ecology (saprotrophs, AMF) were assessed and not the entire microbial diversity, and only C and N were measured in the organic matter (or did I miss something?).
Thanks for this comment. We will rephrase this statement in the context of the limitations of such a case study.
Thank you.
Citation: https://doi.org/10.5194/egusphere-2024-870-AC2
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AC2: 'Reply on RC2', Tatjana Carina Speckert, 23 Aug 2024
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RC3: 'Comment on egusphere-2024-870', Anonymous Referee #3, 26 Jul 2024
This paper investigates changes in soil microbial communities during afforestation using a space-for-time approach ranging from pastures to a 130-year-old coniferous forest. The authors investigated microbial phospholipid fatty acids (PLFAs) and glycerol dialkyl glycerol tetraethers (GDGTs) in each vegetation type and to a depth of 45 cm in 5 cm increments (0-5 cm, 5-10 cm etc.). PLFAs allow for the quantification of microbial biomass of fungal (arbuscular mycorrhizal fungi and saprotrophic fungi) and bacterial groups (gram+ and gram- bacteria), while GDGTs allow for the quantification of archaeal (isoprenoid GDGTs) and a yet poorly described bacterial group most likely part of the phylum acidobacteria (brGDGTs).
The authors do a good job of explaining the importance of the topic and its relevance for global carbon sequestration.Title
It is advisable to change the title to better fit the results of the study. Currently, the title is misleading since decomposition rates are not estimated. Subsoils are mentioned in the title and partially in the discussion but are not really emphasized nor mentioned at all in the conclusion.
Abstract
The topic and its significance in the global context are well explained and highlight its novelty (focusing on alpine pastures) compared to similar studies.
The findings are presented well, however are not necessarily backed up by data and are therefore potentially misleading. For example, the sentence “Our data further suggests that an increase in soil organic matter decomposition results from the alteration in the microbial community structure, which is especially evident in the subsoil of the 130-year-old forest stand ages.” suggests the authors measured in situ decomposition rates of plant litter, which is not the case.Introduction
The introduction must state the current state of literature more concisely in regard to microbial communities and how they are shaped by their environment and vice versa in context of this study (pastures vs. coniferous forests).
The role of GDGTs has to be explained in more detail.- Only the core GDGT abundance is measured in this study. Conversely, the measured values correspond to the necromass of archaea (isoGDGTs) or (acido)bacteria (brGDGTs). It seems though as the authors interpret the measured values as microbial biomass. If this is the case this needs to be changed or addressed how you can use the coreGDGTs as an indicator of microbial biomass since the authors mention themselves that the cleaving of the polar head group is analogous to the cleaving of the polar phosphate group in PLFAs to NLFAs.
- How exactly are GDGTs superior to PLFAs (or NLFAs, see above)? It is mentioned in two different sections of the paper that GDGTS offer an improved time resolution of microbial biomass measurements to commonly used fatty acid biomarkers. At least to this reader the argumentation is not easily understood.
- The reliability of using brGDGTs as a biomarker for acidobacteria that prefer labile carbon is a bit obscure and could benefit from a more in-depth explanation. Is there conclusive evidence that bacteria producing brGDGTs are more likely to decompose labile carbon substrates?
- Archaea are mentioned to be of great importance in biogeochemical cycling in soils (the authors mention their importance in the buildup of necromass). Many studies report a drastically lower abundance of archaea in soils compared to bacteria and fungi. It would be good to add at least a brief explanation why the authors emphasize the role of archaea in soil organic matter buildup.
The aim of the study is stated to be investigating changes in microbial community structure by using a multi-proxy approach (i.e. PLFAs and GDGTs) to infer effects on decomposition and soil organic matter stability. While the microbial community drives microbial decomposition and affects soil organic matter stability, the study is not designed to assess changes in decomposition rates nor soil organic matter stability. The aim should be rephrased to focus on microbial community changes regarding afforestation. Possible implication of the alteration of soil microbial communities can be put into the discussion. Additionally, the aims of the study could include depth since the study in its current form uses subsoils in the title.
Material and Methods
Please explain the reason for the uneven sampling design (5 replicates for pastures and 3 for forest stands).
The replication for PLFAs is very small (2 replicates) and non-existent for GDGTs. This makes most of the discussion highly speculative and/or random since no reliable conclusions can be drawn from one data point.
A possible solution could be to widen the intervals of the sampling (0-10 cm, 20-30 cm etc.) which would result in 4 replicates for PLFAs and 2 for GDGTs.
Some of the parameters measured seem to be missing (e.g. fine root biomass). Please include how this data was obtained.
A brief explanation for the logic behind the nomenclature of the GDGTs is needed (e.g. roman numbers, letters and accents)Results
The results section would benefit of a clearer structure. Maybe an adaption could be to start with briefly describing the soil characteristics (e.g. soil C/N, pH etc.) of each vegetation type before diving deeper into PLFAs.
Interactive effects of depth and vegetation are often mentioned in the same sentence (e.g. line 185), which can become difficult to report and subsequently for the reader to understand. Depth has a well-studied correlation on soil microbial biomass and root mass, soil carbon and nitrogen concentrations and the effect of depth could therefore be reported separately (e.g. if there is a general decrease of all soil microorganisms in all vegetation types, this can be summed up, so the reader knows what to expect). Then a focus could be put on data that defers from this pattern (if there is any) or if vegetation types differed in the slope of the decrease or altered the depth distribution (e.g. C concentration more evenly distributed in one vegetation type than in the other vegetation types).
The results section is elongated a lot by reporting differences among the abundance of GDGT-subgroups between vegetation types. While in the material and methods section the usage of indices and their reasoning is stated, they are not used to full effect in the results. This could simplify reporting relative abundances of GDGTs subgroups (e.g. IIa and IIa’), as one could simply reference the indices themselves (given they are well explained in the materials and methods section).Discussion
The discussion could benefit from a restructuring. Currently, the discussion starts with describing the pasture in length and then discussing the forest stands separately. Since the aim of the study focuses more on the microbial communities in response to afforestation, it would be advisable to start discussing differences (or the absence of such) in PLFAs between pastures and forest stands right away. Depth needs to be discussed more (particularly if it is mentioned in the title) by highlighting differences among pastures and forest stands or the absence of such with depth. If differences occur only in subsoils, then this might be even discussed in a subsection or highlighted in the conclusion.
GDGTs (only worth including in this study if replication can be increased) could be discussed separately in a subsection but the point remains how they can be used to estimate microbial biomass since the core molecule seems to translate to microbial necromass rather than living biomass.
The general applicability of GDGTs in this study needs to be reevaluated. Particularly, the usage of brGDGT subgroups and the subsequently calculated indices are mentioned but add little information to the conclusion. For example, the lines 397-403 “The significant lower CBT5Me ratio in the old forest stand ages (55-year-old and 130-year-old) compared to the pasture and the 40-year-old forest reveals a different bacterial community towards bacteria who preferentially synthesize brGDGT with more cyclopentane moieties. Additionally, the IR6ME ratio was significantly higher in the pasture and in the 40-year-old forest compared to the older forest stand ages (Fig. 05b) indicating a higher relative abundance of 6-methyl over 5-methyl brGDGTs (De Jonge et al., 2024).” more or less reiterate the way these indices are calculated, however in what way these variations add information to the overall conclusion is not clear.
Additionally, there are many explanations for the variation in microbial communities with depth or among vegetation types that are vague and do not necessarily reflect current knowledge, (e.g. line 266 “particularly in bacterial biomarkers with increasing soil depth”, line 286 ”This might suggest a possible competition between AMF and saprotrophic fungi or Gram- bacteria”, see technical comments for explanation to why this seems counterintuitive).
There is a strong need to strengthen the discussion in general and revising some of the argumentations for variations in microbial communities (see technical comments for more detailed information).Conclusion
The conclusion focuses on differences in litter quality as the driving force of microbial community composition (PLFAs and GDGTs). Litter quality is not mentioned in the material and methods of this study but was assessed by the authors in another study in 2023. If this in fact is the main driving force of variation in microbial community composition, then the data must be included in the results and the methods.
Technical comments
26-29 please specify what kind of increase; with age? general? Only in subsoil?
41-44 it is difficult to follow the argumentation here, please explain how organic matter decomposition in deeper soil layers is enhanced by lower inputs of carbon
45-50 please give some more detail how litter quality shapes microbial communities
63-64 unknown or Acidobacteria? Please rephrase for clarification if this is a yet unknown species belonging to the phylum acidobacteria or only some of them are Acidobacteria but others are unknown etc.
64-67 “possibly feeding on root carbon sources” is probably meant to describe the organisms producing brGDGTs. Please rephrase for clarification, also mentioned the same way in 347
68 in a similar vein to in a similar way to
71-73 not sure if the turnover time refers to the total GDGT molecule (polar head and apolar core) or just the core. Likely for the core in which case this can’t be used as a biomarker for living biomass; needs clarification that this is a (archaeal necromass biomarker only) ; it is unclear how this is improves the time-integrated signal of soil microbial abundance compared to PLFAs
86 fungi are part of the soil microbiome
94-95 pastures mentioned here to contain less easily decomposable organic matter, but this is countering the overall argumentation
95-97 overall GDGTs or only branched ones? There is no argumentation found above for a preference of archaea for labile carbon sources
146-148 actinobacteria are also gram+ bacteria, labelling of gram+ bacteria must be changed to address this (e.g. rename gram+ to firmicutes, consult literature), interpretations in the discussion and report in the result section need to be addressed accordingly
150-151 One replicate per stand age can’t be used to interpret differences among forest stand ages and pastures, two replicates is also highly questionable
165-168 the F:B ratio is calculated by fungal PLFAs divided by bacterial PLFAs
177 would help understanding (and referencing later one) if the abbreviation IR6Me is mentioned in full length above.
185-187 pasture has a higher mean value than the 55-year-old forests for the 0-5 cm
210-213 “which was not observed in the pasture, the 40-year-old or 130-year-old forest” maybe this additional information is not needed since it is mentioned already that this is specific to 55-year-old forest
213-215 “common to all areas” but then mentioning 40-year-old forest specifically (in regard to what?) please rephrase, it would probably also be worth to mention the overall effect on fungi since relative effects of pH on bacteria and fungi are predicted to differ
217 Unfortunately I must strongly advise against using this data since one data point can’t be statistically evaluated; section was still reviewed for the sake of completeness
221-222 this is only true for the 130-year old forests which needs to be mentioned in this sentence to avoid confusion
224 it should say IIa instead of IIb
227-229 mentioned are only IIb’ and IIIb’ but not IIa’ and IIIa’, the concentrations only spike in 35-40 cm but besides that the major groups seem to follow the same trajectory then all other compounds (decreasing with depth)
264-266 fungi are often described to be decreasing stronger with depth since they are more associated with roots, the citations also don’t match the described observations (one of them focuses on microarthropods and neither focus on depth)
please add citations describing depth related distribution patterns of fungi and bacteria278 if still comparing to Francisco et al. (2016) then both investigate grass vegetations with grass species. Difficult to understand the point here
280-284 not clear to understand, root exudates are present in all soils only relative amounts vary, r2 instead of r
299-300 however you found an overall effect irrespective of the cyclisation ratio
308 the definition of substrate quality is questionable, soil pH does not describe substrate quality and vegetation cover may explain the amount of substrate available (although this has to be confirmed experimentally) but does not reflect on litter quality, carbon concentration of substrate is always organic and quality is therefore described through the C:N ratio already
314-315 the C:N ratio is known, right? Could be explored in the scope of this study
316-319 does this only apply to bacteria though? Citations seem again out of place (no bacteria studied in the first mentioned citation)
330 what do you mean by increased decomposition of old organic matter? Where is this reported
333-336 AFM to AMF; organic matter decomposition is seldomly seen in AMF, the cited paper reports much higher AMF values in pastures
346 the organisms producing brGDGTs not the molecule
384-397 highly speculative, there is little explanation why this should apply to the 40-year-old and 55-year old forests as well since temperature differences are only reported for pastures, if this can’t be backed up by further data it is advisable to drop this explanation
408-410 isoGDGTs are the only type of GDGT that is elevated in pastures, so archaea (additionally this means only an increase in archaeal necromass) is increased but they are not described here to be specifically associated to roots or labile carbon in comparison to other microbial groups, brGDGTs show not really a difference between pastures and 40 year and 55 year old forests according to the data presented
Figures
Information in the subtext should describe the unit, the meaning of the data points (e.g. mean) and the replication number
Supplementary
Table S1.
pH value and variation are exactly the same for 55-year-old forest and 130-year-old forest
Table S3.
NA value in 40-year-old forest in the wrong cell (35-40 missing AMF)
Citation: https://doi.org/10.5194/egusphere-2024-870-RC3 -
AC3: 'Reply on RC3', Tatjana Carina Speckert, 23 Aug 2024
This paper investigates changes in soil microbial communities during afforestation using a space-for-time approach ranging from pastures to a 130-year-old coniferous forest. The authors investigated microbial phospholipid fatty acids (PLFAs) and glycerol dialkyl glycerol tetraethers (GDGTs) in each vegetation type and to a depth of 45 cm in 5 cm increments (0-5 cm, 5-10 cm etc.). PLFAs allow for the quantification of microbial biomass of fungal (arbuscular mycorrhizal fungi and saprotrophic fungi) and bacterial groups (gram+ and gram- bacteria), while GDGTs allow for the quantification of archaeal (isoprenoid GDGTs) and a yet poorly described bacterial group most likely part of the phylum acidobacteria (brGDGTs).
The authors do a good job of explaining the importance of the topic and its relevance for global carbon sequestration.Thank you for your feedback and your helpful comments!
Title
It is advisable to change the title to better fit the results of the study. Currently, the title is misleading since decomposition rates are not estimated. Subsoils are mentioned in the title and partially in the discussion but are not really emphasized nor mentioned at all in the conclusion.
Thanks for mentioning this. We do agree and we will change the title accordingly in the next version of the manuscript:
Abstract
The topic and its significance in the global context are well explained and highlight its novelty (focusing on alpine pastures) compared to similar studies.
Thanks!
The findings are presented well, however are not necessarily backed up by data and are therefore potentially misleading. For example, the sentence “Our data further suggests that an increase in soil organic matter decomposition results from the alteration in the microbial community structure, which is especially evident in the subsoil of the 130-year-old forest stand ages.” suggests the authors measured in situ decomposition rates of plant litter, which is not the case.Thank you for this comment. We do agree that this statement suggests that the measurement of decomposition is in the scope of this study. We will rephrase this in the next version of the manuscript to make it clear for the reader which information was obtained in which study and we therefore will focus less on the decomposition in the next version.
Introduction
The introduction must state the current state of literature more concisely in regard to microbial communities and how they are shaped by their environment and vice versa in context of this study (pastures vs. coniferous forests).
Thanks for this comment. We agree and will provide more information in the introduction part on how the environment shapes the soil microbial community.
The role of GDGTs has to be explained in more detail.- Only the core GDGT abundance is measured in this study. Conversely, the measured values correspond to the necromass of archaea (isoGDGTs) or (acido)bacteria (brGDGTs). It seems though as the authors interpret the measured values as microbial biomass. If this is the case this needs to be changed or addressed how you can use the coreGDGTs as an indicator of microbial biomass since the authors mention themselves that the cleaving of the polar head group is analogous to the cleaving of the polar phosphate group in PLFAs to NLFAs.
Thanks for this comment. We analysed core lipid GDGTs, which represent the necromass, in contrast to the IPL GDGTs referring to the biomass. We, however, consider the core lipid GDGTs as a good indicator of the microbial biomass, especially as most of them are presented as core lipid GDGTs in soils (generally >80% of GDGTs are present as core lipids in soils (Peterse et al., 2011 https://doi.org/10.1016/j.orggeochem.2011.07.006; Huguet et al., 2017 https://doi.org/10.1016/j.gca.2017.01.012) ). We will state this clear in the next version of the manuscript why we consider the core lipid GDGT as microbial biomass in this study.
- How exactly are GDGTs superior to PLFAs (or NLFAs, see above)? It is mentioned in two different sections of the paper that GDGTS offer an improved time resolution of microbial biomass measurements to commonly used fatty acid biomarkers. At least to this reader the argumentation is not easily understood.
Thank you for this comment. BrGDGTs represent a more time- and spatially integrated signal than the PLFAs as they have a typical turnover time in soils in the range of multiple decades (Weijers et al., 2010, doi: 10.5194/bg-7-2959-2010). We will explain this clear in the next version of the manuscript and provide more examples from literature to improve the understanding of the difference in the time resolution of these biomarkers.
The reliability of using brGDGTs as a biomarker for acidobacteria that prefer labile carbon is a bit obscure and could benefit from a more in-depth explanation. Is there conclusive evidence that bacteria producing brGDGTs are more likely to decompose labile carbon substrates?
Thanks for your comment. We will explain this in the next version of the manuscript. Additionally, we will add one or two references related to the fact that brGDGTs are more abundant at lower pH (in line with the fact that one of their producers is Acidobacteria)
- Archaea are mentioned to be of great importance in biogeochemical cycling in soils (the authors mention their importance in the buildup of necromass). Many studies report a drastically lower abundance of archaea in soils compared to bacteria and fungi. It would be good to add at least a brief explanation why the authors emphasize the role of archaea in soil organic matter buildup.
Thanks for this comment. Even though there is a lower abundance of archaea compared to bacteria and fungi it does not exclude their role in the cycling of soil organic matter. But we will explain the role of archaea in the context of soil organic matter build up more clearly in the next version of the manuscript.
The aim of the study is stated to be investigating changes in microbial community structure by using a multi-proxy approach (i.e. PLFAs and GDGTs) to infer effects on decomposition and soil organic matter stability. While the microbial community drives microbial decomposition and affects soil organic matter stability, the study is not designed to assess changes in decomposition rates nor soil organic matter stability. The aim should be rephrased to focus on microbial community changes regarding afforestation. Possible implication of the alteration of soil microbial communities can be put into the discussion. Additionally, the aims of the study could include depth since the study in its current form uses subsoils in the title.
Thanks for this comment. We agree and we will rephrase the focus of our story in the next version of the manuscript while focusing less on soil organic matter decomposition and more on the difference in the soil microbial community between alpine forests and pastures.
Material and Methods
Please explain the reason for the uneven sampling design (5 replicates for pastures and 3 for forest stands).
Thanks for pointing this out. The number of soil pits was 5 in the pasture to have an adequate number of control samples and 3 in the forest due to time constraints during the sampling campaign.The replication for PLFAs is very small (2 replicates) and non-existent for GDGTs. This makes most of the discussion highly speculative and/or random since no reliable conclusions can be drawn from one data point.
A possible solution could be to widen the intervals of the sampling (0-10 cm, 20-30 cm etc.) which would result in 4 replicates for PLFAs and 2 for GDGTs.Thanks for your comment. However, we do not agree to averaging our values, which would result in loss of information. Indeed, in our samples, most of the changes occur in the topsoil 0-5cm. The information on how soil microbial community differs in the upper soil horizons especially in the two observed land-use types is important for our story and would be lost if we average our results.
Some of the parameters measured seem to be missing (e.g. fine root biomass). Please include how this data was obtained.Thanks for pointing this out. We described this in detail in Speckert et al. 2023 and we will add the missing information in the next version of the manuscript in the supplement.
A brief explanation for the logic behind the nomenclature of the GDGTs is needed (e.g. roman numbers, letters and accents)We agree and we will add this information in the supplementary Material in the next version of the manuscript.
Results
The results section would benefit of a clearer structure. Maybe an adaption could be to start with briefly describing the soil characteristics (e.g. soil C/N, pH etc.) of each vegetation type before diving deeper into PLFAs.
Thanks for this comment. We will add an additional short paragraph in the result section for presenting the bulk results before we dive deeper into the results of the molecular proxies.
Interactive effects of depth and vegetation are often mentioned in the same sentence (e.g. line 185), which can become difficult to report and subsequently for the reader to understand. Depth has a well-studied correlation on soil microbial biomass and root mass, soil carbon and nitrogen concentrations and the effect of depth could therefore be reported separately (e.g. if there is a general decrease of all soil microorganisms in all vegetation types, this can be summed up, so the reader knows what to expect). Then a focus could be put on data that defers from this pattern (if there is any) or if vegetation types differed in the slope of the decrease or altered the depth distribution (e.g. C concentration more evenly distributed in one vegetation type than in the other vegetation types).
The results section is elongated a lot by reporting differences among the abundance of GDGT-subgroups between vegetation types. While in the material and methods section the usage of indices and their reasoning is stated, they are not used to full effect in the results. This could simplify reporting relative abundances of GDGTs subgroups (e.g. IIa and IIa’), as one could simply reference the indices themselves (given they are well explained in the materials and methods section).Thanks for your suggestions. We will shorten the result part and focus on the observed difference in the subgroups and not detailing the individual compounds.
Discussion
The discussion could benefit from a restructuring. Currently, the discussion starts with describing the pasture in length and then discussing the forest stands separately. Since the aim of the study focuses more on the microbial communities in response to afforestation, it would be advisable to start discussing differences (or the absence of such) in PLFAs between pastures and forest stands right away. Depth needs to be discussed more (particularly if it is mentioned in the title) by highlighting differences among pastures and forest stands or the absence of such with depth. If differences occur only in subsoils, then this might be even discussed in a subsection or highlighted in the conclusion.
Thanks for your suggestions. We agree and will restructure the discussion part in the next version of the manuscript. We will start with the difference between pasture and forest areas first and then explain more about the observed differences with increasing soil depth.
GDGTs (only worth including in this study if replication can be increased) could be discussed separately in a subsection but the point remains how they can be used to estimate microbial biomass since the core molecule seems to translate to microbial necromass rather than living biomass.Thanks for this comment. We agree that CLs represent the fossil biomass and the IPLs (not measured for GDGTs here) the living biomass. But this does not prevent comparing the different depths and conditions in terms of biomass. The interest of GDGTs is to have access to the archaeal biomass, which cannot be investigated through PLFAs.
The general applicability of GDGTs in this study needs to be reevaluated. Particularly, the usage of brGDGT subgroups and the subsequently calculated indices are mentioned but add little information to the conclusion. For example, the lines 397-403 “The significant lower CBT5Me ratio in the old forest stand ages (55-year-old and 130-year-old) compared to the pasture and the 40-year-old forest reveals a different bacterial community towards bacteria who preferentially synthesize brGDGT with more cyclopentane moieties. Additionally, the IR6ME ratio was significantly higher in the pasture and in the 40-year-old forest compared to the older forest stand ages (Fig. 05b) indicating a higher relative abundance of 6-methyl over 5-methyl brGDGTs (De Jonge et al., 2024).” more or less reiterate the way these indices are calculated, however in what way these variations add information to the overall conclusion is not clear.Thanks for pointing this out. And we will add more information what the value is for our observed results for this study, and we will explain our conclusion more clearly and focus on the results necessary for the discussion part.
Additionally, there are many explanations for the variation in microbial communities with depth or among vegetation types that are vague and do not necessarily reflect current knowledge, (e.g. line 266 “particularly in bacterial biomarkers with increasing soil depth”, line 286 ”This might suggest a possible competition between AMF and saprotrophic fungi or Gram- bacteria”, see technical comments for explanation to why this seems counterintuitive).We agree that using terminology such as “particularly” or “might suggest” is not precise. We removed the qualitative judgments and stated clear if a change is significant or not.
There is a strong need to strengthen the discussion in general and revising some of the argumentations for variations in microbial communities (see technical comments for more detailed information).Thanks for this comment. We do agree and will revise the discussion part accordingly in the next version of the manuscript.
Conclusion
The conclusion focuses on differences in litter quality as the driving force of microbial community composition (PLFAs and GDGTs). Litter quality is not mentioned in the material and methods of this study but was assessed by the authors in another study in 2023. If this in fact is the main driving force of variation in microbial community composition, then the data must be included in the results and the methods.
Thanks for your suggestion. We agree and will include this information in the M&M section and in the newly added paragraph in the result section, where we will report the missing information for the bulk parameters.
Technical comments
26-29 please specify what kind of increase; with age? general? Only in subsoil?
Thanks for your comment. We will specify this increase in the next version of the manuscript. “This trend, however, was reversed with a decreasing bacterial community over the entire soil depth of 45cm with increasing forest age when considering GDGT biomarkers”.
41-44 it is difficult to follow the argumentation here, please explain how organic matter decomposition in deeper soil layers is enhanced by lower inputs of carbon
Thanks for mentioning this and we agree with it and will explain in more detail how the OM decomposition in deeper soil horizons is enhanced by lower carbon inputs.
45-50 please give some more detail how litter quality shapes microbial communities
Thanks for this comment. We will provide some examples in the introduction section on how litter quality shapes the soil microbial community.
63-64 unknown or Acidobacteria? Please rephrase for clarification if this is a yet unknown species belonging to the phylum acidobacteria or only some of them are Acidobacteria but others are unknown etc.
They are produced by unknown bacteria but some of them might belong to the phylum Acidobacteria. But we agree with your comment, and we will rephrase this clearly in the next version of the manuscript.
64-67 “possibly feeding on root carbon sources” is probably meant to describe the organisms producing brGDGTs. Please rephrase for clarification, also mentioned the same way in 347
Thanks for mentioning this and we will change accordingly. “In contrast with archaeal GDGTs, bacterial GDGTs are constituted of branched alkyl chains instead of isoprenoid ones and are referred as branched GDGTs (brGDGTs). Such brGDGT producing bacteria are known to use root-derived carbon as a potential food resource (Huguet et al., 2012; Gocke et al., 2016).”
68 in a similar vein to in a similar way to
We will change this accordingly in the next version of the manuscript. “In a similar way to the PLFA analysis, intact GDGTs still being attached to a polar headgroup are attributed to the living biomass, while core lipid GDGTs without any polar headgroup are attributed to the bacterial necromass (Gocke et al., 2017).”
71-73 not sure if the turnover time refers to the total GDGT molecule (polar head and apolar core) or just the core. Likely for the core in which case this can’t be used as a biomarker for living biomass; needs clarification that this is a (archaeal necromass biomarker only) ; it is unclear how this is improves the time-integrated signal of soil microbial abundance compared to PLFAs
Thanks for pointing this out. And we agree. The turnover times refer to the necromass. We will therefore clarify this in the next version of the manuscript.
86 fungi are part of the soil microbiome
Thanks for your comment. We agree and we will rephrase this accordingly in the next version of the manuscript and will write soil microbial community, which is used for both fungi and microbes.
94-95 pastures mentioned here to contain less easily decomposable organic matter, but this is countering the overall argumentation
Thanks for mentioning this. And we agree that it was not so clearly formulated. The statement “where less easily decomposable organic matter predominates” is correct for the forest and not for the pasture. We will rephrase this accordingly in the next version of the manuscript. “Due to the already reported alteration in the litter quality towards more recalcitrant (high C:N ratio) litter input in this subalpine afforestation sequence(Hiltbrunner et al., 2013; Speckert et al., 2023), we hypothesize an increase in Gram+ bacteria and in the fungal communities with increasing forest age where less easily decomposable organic matter predominates, in comparison to the pasture”
95-97 overall GDGTs or only branched ones? There is no argumentation found above for a preference of archaea for labile carbon sources
Thanks for pointing this out. We hypothesized this for brGDGTs and isoGDGTs, the latter is more abundant in pasture than in forest, and so also their source microorganisms.
146-148 actinobacteria are also gram+ bacteria, labelling of gram+ bacteria must be changed to address this (e.g. rename gram+ to firmicutes, consult literature), interpretations in the discussion and report in the result section need to be addressed accordingly
Thanks for this comment. For this manuscript we used the common classification according to literature (Macdonald et al., 2009 https://doi.org/10.1016/j.soilbio.2009.05.003; Willers et al., 2015 https://doi.org/10.1111/jam.12902) and to preexisting studies (e.g. Hiltbrunner et al., 2012 https://doi.org/10.1016/j.geoderma.2011.11.026) in the same study site to achieve comparability.
150-151 One replicate per stand age can’t be used to interpret differences among forest stand ages and pastures, two replicates is also highly questionable
Thanks for this comment. For both of our proxies we have measurements in duplicates (analytical replicates) and references with certified external standards as control. Additionally, also with one sample for GDGTs and two replicates for the PLFAs, we are able to show differences in depth trends and difference in the variability between alpine forests and pastures. Further our goal was to have a look at both the bacterial and archaeal communities, which is not possible if we only consider PLFAs. Although it would have been great to have more replicates, we were limited by monetary and time restrictions to conduct a more comprehensive study.
165-168 the F:B ratio is calculated by fungal PLFAs divided by bacterial PLFAs
Thanks for mentioning this. And we will change this mistake accordingly in the next version of the manuscript. “The F:B ratio was calculated by PLFA-derived fungal biomass (saprotrophic fungi and AMF) divided by PLFA-derived bacterial biomass (Gram+, Gram- bacteria and actinobacteria).”
177 would help understanding (and referencing later one) if the abbreviation IR6Me is mentioned in full length above.
Thanks for this comment and we agree with this. We will add this information in the next version. “The relative abundance of 6-methyl over 5-methyl brGDGTs was calculated using the isomerization ratio (IR) according to De Jonge et al.(2014; Eq. 2), which compares the relative abundance of 6- and 5-methyl homologues among brGDGT-II and brGDGT-III groups.”
185-187 pasture has a higher mean value than the 55-year-old forests for the 0-5 cm
Thanks for pointing this out. We will rephrase this accordingly in the next version of the manuscript.
210-213 “which was not observed in the pasture, the 40-year-old or 130-year-old forest” maybe this additional information is not needed since it is mentioned already that this is specific to 55-year-old forest
Thanks for mentioning this. We agree with your comment, and we will remove the unnecessary information in the next version of the manuscript. “The fine root biomass correlated strongly with all individual PLFA compounds with the exception of the actinobacteria in the 55-year-old forest (Fig. A4a to e).”
213-215 “common to all areas” but then mentioning 40-year-old forest specifically (in regard to what?) please rephrase, it would probably also be worth to mention the overall effect on fungi since relative effects of pH on bacteria and fungi are predicted to differ
Thanks for this comment. We wanted to highlight that this negative correlation was most prominent in the 40-year-old forest, even though it was observed in all areas. We also agree that it would be worth to mention the correlation between soil pH and fungi and we added this additional information in the next version of the manuscript.
217 Unfortunately I must strongly advise against using this data since one data point can’t be statistically evaluated; section was still reviewed for the sake of completeness
Thanks for this comment. However, we have a slightly different opinion on this. Although there is only one sampling point for the GDGT proxy we can still retrieve valuable information as well as comparison between the data. Additionally, part of these sampling points was measured in duplicates with additional reference samples included in the analytical sequence to control the reliability of the results.
221-222 this is only true for the 130-year old forests which needs to be mentioned in this sentence to avoid confusion
Thank you for this comment and we will clearly state in the next version of the manuscript, that this is only true for the130-year-old forest.
224 it should say IIa instead of IIb
Thanks for pointing this out and we corrected this mistake in the next version. “The brGDGTs Ia, IIa, and Ib represented altogether approximately 50% of all brGDGTs in all soils. In the 130-year-old forest, the brGDGTs Ia, IIa, and Ib altogether account for 60 – 70% of all brGDGTs (Table B4).”
227-229 mentioned are only IIb’ and IIIb’ but not IIa’ and IIIa’, the concentrations only spike in 35-40 cm but besides that the major groups seem to follow the same trajectory then all other compounds (decreasing with depth)
Thanks for this comment. It is true that also the concentrations in IIa’ and IIIa’ increase in that particular soil depth. We will also add this information in the brackets in the next version of the manuscript.
264-266 fungi are often described to be decreasing stronger with depth since they are more associated with roots, the citations also don’t match the described observations (one of them focuses on microarthropods and neither focus on depth) please add citations describing depth related distribution patterns of fungi and bacteria
Thanks for your suggestions and we agree to elaborate more about the depth related distribution patterns of bacteria and fungi in the next version of the manuscript. We will also check the citations again and will remove those citations, which are not suitable.
278 if still comparing to Francisco et al. (2016) then both investigate grass vegetations with grass species. Difficult to understand the point here
Thanks for your comment. We apologize for the misunderstanding, but we do not clearly understand what we are supposed to change here.
280-284 not clear to understand, root exudates are present in all soils only relative amounts vary, r2 instead of r
Thanks for your suggestion. We will change from r into r2 in the next version of the manuscript.
299-300 however you found an overall effect irrespective of the cyclisation ratio
Thank you for this comment. And we will rephrase this in the next version of the manuscript.
308 the definition of substrate quality is questionable, soil pH does not describe substrate quality and vegetation cover may explain the amount of substrate available (although this has to be confirmed experimentally) but does not reflect on litter quality, carbon concentration of substrate is always organic and quality is therefore described through the C:N ratio already
Thanks for mentioning this. We do agree and will delete soil pH in the brackets in the next version of the manuscript.
314-315 the C:N ratio is known, right? Could be explored in the scope of this study
Thanks for your comment. Yes, the C:N ratio is known, and we will add this information with the respective citation in the discussion part in the next version of the manuscript. “This might suggest a low C:N ratio as well as a lower carbon and nitrogen availability, which might explain the constantly lower bacterial and fungal abundance in the 55-year-old forest (C:N 54.7±3.9) compared to the 40-year-old (C:N 57.1±2.6) and 130-year-old forest (61.2±2.9; Speckert et al., 2023)”
316-319 does this only apply to bacteria though? Citations seem again out of place (no bacteria studied in the first mentioned citation)
Thanks for mentioning this. And yes, this still applies for the bacterial community. We will add this missing information in the next version of the manuscript. “The key role of organic carbon and particularly nitrogen for soil bacterial abundance was observed in numerous studies (Fierer, 2017) and was further supported by the positive correlation between organic carbon and nitrogen concentrations and the bacterial community in older forest stand ages in this study (Fig. A2 and A3).
330 what do you mean by increased decomposition of old organic matter? Where is this reported
Thanks for your comment. Old organic matter is used in this manuscript as more microbially processed OM, which is more often located in the subsoil (Rumpel and Kögel-Knabner, 2011). The decomposition of OM located in the subsoil in this specific study site, especially in the oldest forest stand, was previously reported in other studies on this specific afforestation sequence (Hiltbrunner et al., 2013; Speckert and Wiesenberg, 2023), which is now further supported by the reported higher concentration of Gram+ bacteria. We will restrict to “microbial processed” to avoid further confusion.
333-336 AFM to AMF; organic matter decomposition is seldomly seen in AMF, the cited paper reports much higher AMF values in pastures
Thanks for mentioning this and we will correct this typo in the next version. The respective paper was used due to their statement that the presence of lignin decomposing fungi might be one explanation for a higher fungal concentration. But we do understand that it might be confusing for the reader ad so we will therefore replace this by a more suitable citation.
346 the organisms producing brGDGTs not the molecule
Thanks for this comment and yes, we agree, and we will rephrase this sentence in the next version of the manuscript. “A possible explanation might be the preference of brGDGT producing organisms for root carbon as a food source (Ayari et al., 2013; Huguet et al., 2013).”
384-397 highly speculative, there is little explanation why this should apply to the 40-year-old and 55-year old forests as well since temperature differences are only reported for pastures, if this can’t be backed up by further data it is advisable to drop this explanation
Thanks for your suggestions. And we will drop this explanation in the next version of the manuscript.
408-410 isoGDGTs are the only type of GDGT that is elevated in pastures, so archaea (additionally this means only an increase in archaeal necromass) is increased but they are not described here to be specifically associated to roots or labile carbon in comparison to other microbial groups, brGDGTs show not really a difference between pastures and 40 year and 55 year old forests according to the data presented
Thanks for mentioning this and we will add additional information about the relationship between fine root biomass and isoGDGT, especially in the pasture.
Figures
Information in the subtext should describe the unit, the meaning of the data points (e.g. mean) and the replication number
Thanks for pointing this out and we agree. We will add the units and the description of the data points including the number of replications in the caption of all figures.
Supplementary
Table S1.
pH value and variation are exactly the same for 55-year-old forest and 130-year-old forest
Thanks for pointing this out. We will correct this mistake in the next version of the manuscript.
Table S3.
NA value in 40-year-old forest in the wrong cell (35-40 missing AMF)
Thanks for mentioning this. We will correct this mistake in the next version of the manuscript.
Thank you.
Citation: https://doi.org/10.5194/egusphere-2024-870-AC3 -
AC4: 'Reply on RC3', Tatjana Carina Speckert, 23 Aug 2024
This paper investigates changes in soil microbial communities during afforestation using a space-for-time approach ranging from pastures to a 130-year-old coniferous forest. The authors investigated microbial phospholipid fatty acids (PLFAs) and glycerol dialkyl glycerol tetraethers (GDGTs) in each vegetation type and to a depth of 45 cm in 5 cm increments (0-5 cm, 5-10 cm etc.). PLFAs allow for the quantification of microbial biomass of fungal (arbuscular mycorrhizal fungi and saprotrophic fungi) and bacterial groups (gram+ and gram- bacteria), while GDGTs allow for the quantification of archaeal (isoprenoid GDGTs) and a yet poorly described bacterial group most likely part of the phylum acidobacteria (brGDGTs).
The authors do a good job of explaining the importance of the topic and its relevance for global carbon sequestration.Thank you for your feedback and your helpful comments!
Title
It is advisable to change the title to better fit the results of the study. Currently, the title is misleading since decomposition rates are not estimated. Subsoils are mentioned in the title and partially in the discussion but are not really emphasized nor mentioned at all in the conclusion.
Thanks for mentioning this. We do agree and we will change the title accordingly in the next version of the manuscript:
Abstract
The topic and its significance in the global context are well explained and highlight its novelty (focusing on alpine pastures) compared to similar studies.
Thanks!
The findings are presented well, however are not necessarily backed up by data and are therefore potentially misleading. For example, the sentence “Our data further suggests that an increase in soil organic matter decomposition results from the alteration in the microbial community structure, which is especially evident in the subsoil of the 130-year-old forest stand ages.” suggests the authors measured in situ decomposition rates of plant litter, which is not the case.Thank you for this comment. We do agree that this statement suggests that the measurement of decomposition is in the scope of this study. We will rephrase this in the next version of the manuscript to make it clear for the reader which information was obtained in which study and we therefore will focus less on the decomposition in the next version.
Introduction
The introduction must state the current state of literature more concisely in regard to microbial communities and how they are shaped by their environment and vice versa in context of this study (pastures vs. coniferous forests).
Thanks for this comment. We agree and will provide more information in the introduction part on how the environment shapes the soil microbial community.
The role of GDGTs has to be explained in more detail.- Only the core GDGT abundance is measured in this study. Conversely, the measured values correspond to the necromass of archaea (isoGDGTs) or (acido)bacteria (brGDGTs). It seems though as the authors interpret the measured values as microbial biomass. If this is the case this needs to be changed or addressed how you can use the coreGDGTs as an indicator of microbial biomass since the authors mention themselves that the cleaving of the polar head group is analogous to the cleaving of the polar phosphate group in PLFAs to NLFAs.
Thanks for this comment. We analysed core lipid GDGTs, which represent the necromass, in contrast to the IPL GDGTs referring to the biomass. We, however, consider the core lipid GDGTs as a good indicator of the microbial biomass, especially as most of them are presented as core lipid GDGTs in soils (generally >80% of GDGTs are present as core lipids in soils (Peterse et al., 2011 https://doi.org/10.1016/j.orggeochem.2011.07.006; Huguet et al., 2017 https://doi.org/10.1016/j.gca.2017.01.012) ). We will state this clear in the next version of the manuscript why we consider the core lipid GDGT as microbial biomass in this study.
- How exactly are GDGTs superior to PLFAs (or NLFAs, see above)? It is mentioned in two different sections of the paper that GDGTS offer an improved time resolution of microbial biomass measurements to commonly used fatty acid biomarkers. At least to this reader the argumentation is not easily understood.
Thank you for this comment. BrGDGTs represent a more time- and spatially integrated signal than the PLFAs as they have a typical turnover time in soils in the range of multiple decades (Weijers et al., 2010, doi: 10.5194/bg-7-2959-2010). We will explain this clear in the next version of the manuscript and provide more examples from literature to improve the understanding of the difference in the time resolution of these biomarkers.
The reliability of using brGDGTs as a biomarker for acidobacteria that prefer labile carbon is a bit obscure and could benefit from a more in-depth explanation. Is there conclusive evidence that bacteria producing brGDGTs are more likely to decompose labile carbon substrates?
Thanks for your comment. We will explain this in the next version of the manuscript. Additionally, we will add one or two references related to the fact that brGDGTs are more abundant at lower pH (in line with the fact that one of their producers is Acidobacteria)
- Archaea are mentioned to be of great importance in biogeochemical cycling in soils (the authors mention their importance in the buildup of necromass). Many studies report a drastically lower abundance of archaea in soils compared to bacteria and fungi. It would be good to add at least a brief explanation why the authors emphasize the role of archaea in soil organic matter buildup.
Thanks for this comment. Even though there is a lower abundance of archaea compared to bacteria and fungi it does not exclude their role in the cycling of soil organic matter. But we will explain the role of archaea in the context of soil organic matter build up more clearly in the next version of the manuscript.
The aim of the study is stated to be investigating changes in microbial community structure by using a multi-proxy approach (i.e. PLFAs and GDGTs) to infer effects on decomposition and soil organic matter stability. While the microbial community drives microbial decomposition and affects soil organic matter stability, the study is not designed to assess changes in decomposition rates nor soil organic matter stability. The aim should be rephrased to focus on microbial community changes regarding afforestation. Possible implication of the alteration of soil microbial communities can be put into the discussion. Additionally, the aims of the study could include depth since the study in its current form uses subsoils in the title.
Thanks for this comment. We agree and we will rephrase the focus of our story in the next version of the manuscript while focusing less on soil organic matter decomposition and more on the difference in the soil microbial community between alpine forests and pastures.
Material and Methods
Please explain the reason for the uneven sampling design (5 replicates for pastures and 3 for forest stands).
Thanks for pointing this out. The number of soil pits was 5 in the pasture to have an adequate number of control samples and 3 in the forest due to time constraints during the sampling campaign.The replication for PLFAs is very small (2 replicates) and non-existent for GDGTs. This makes most of the discussion highly speculative and/or random since no reliable conclusions can be drawn from one data point.
A possible solution could be to widen the intervals of the sampling (0-10 cm, 20-30 cm etc.) which would result in 4 replicates for PLFAs and 2 for GDGTs.Thanks for your comment. However, we do not agree to averaging our values, which would result in loss of information. Indeed, in our samples, most of the changes occur in the topsoil 0-5cm. The information on how soil microbial community differs in the upper soil horizons especially in the two observed land-use types is important for our story and would be lost if we average our results.
Some of the parameters measured seem to be missing (e.g. fine root biomass). Please include how this data was obtained.Thanks for pointing this out. We described this in detail in Speckert et al. 2023 and we will add the missing information in the next version of the manuscript in the supplement.
A brief explanation for the logic behind the nomenclature of the GDGTs is needed (e.g. roman numbers, letters and accents)We agree and we will add this information in the supplementary Material in the next version of the manuscript.
Results
The results section would benefit of a clearer structure. Maybe an adaption could be to start with briefly describing the soil characteristics (e.g. soil C/N, pH etc.) of each vegetation type before diving deeper into PLFAs.
Thanks for this comment. We will add an additional short paragraph in the result section for presenting the bulk results before we dive deeper into the results of the molecular proxies.
Interactive effects of depth and vegetation are often mentioned in the same sentence (e.g. line 185), which can become difficult to report and subsequently for the reader to understand. Depth has a well-studied correlation on soil microbial biomass and root mass, soil carbon and nitrogen concentrations and the effect of depth could therefore be reported separately (e.g. if there is a general decrease of all soil microorganisms in all vegetation types, this can be summed up, so the reader knows what to expect). Then a focus could be put on data that defers from this pattern (if there is any) or if vegetation types differed in the slope of the decrease or altered the depth distribution (e.g. C concentration more evenly distributed in one vegetation type than in the other vegetation types).
The results section is elongated a lot by reporting differences among the abundance of GDGT-subgroups between vegetation types. While in the material and methods section the usage of indices and their reasoning is stated, they are not used to full effect in the results. This could simplify reporting relative abundances of GDGTs subgroups (e.g. IIa and IIa’), as one could simply reference the indices themselves (given they are well explained in the materials and methods section).Thanks for your suggestions. We will shorten the result part and focus on the observed difference in the subgroups and not detailing the individual compounds.
Discussion
The discussion could benefit from a restructuring. Currently, the discussion starts with describing the pasture in length and then discussing the forest stands separately. Since the aim of the study focuses more on the microbial communities in response to afforestation, it would be advisable to start discussing differences (or the absence of such) in PLFAs between pastures and forest stands right away. Depth needs to be discussed more (particularly if it is mentioned in the title) by highlighting differences among pastures and forest stands or the absence of such with depth. If differences occur only in subsoils, then this might be even discussed in a subsection or highlighted in the conclusion.
Thanks for your suggestions. We agree and will restructure the discussion part in the next version of the manuscript. We will start with the difference between pasture and forest areas first and then explain more about the observed differences with increasing soil depth.
GDGTs (only worth including in this study if replication can be increased) could be discussed separately in a subsection but the point remains how they can be used to estimate microbial biomass since the core molecule seems to translate to microbial necromass rather than living biomass.Thanks for this comment. We agree that CLs represent the fossil biomass and the IPLs (not measured for GDGTs here) the living biomass. But this does not prevent comparing the different depths and conditions in terms of biomass. The interest of GDGTs is to have access to the archaeal biomass, which cannot be investigated through PLFAs.
The general applicability of GDGTs in this study needs to be reevaluated. Particularly, the usage of brGDGT subgroups and the subsequently calculated indices are mentioned but add little information to the conclusion. For example, the lines 397-403 “The significant lower CBT5Me ratio in the old forest stand ages (55-year-old and 130-year-old) compared to the pasture and the 40-year-old forest reveals a different bacterial community towards bacteria who preferentially synthesize brGDGT with more cyclopentane moieties. Additionally, the IR6ME ratio was significantly higher in the pasture and in the 40-year-old forest compared to the older forest stand ages (Fig. 05b) indicating a higher relative abundance of 6-methyl over 5-methyl brGDGTs (De Jonge et al., 2024).” more or less reiterate the way these indices are calculated, however in what way these variations add information to the overall conclusion is not clear.Thanks for pointing this out. And we will add more information what the value is for our observed results for this study, and we will explain our conclusion more clearly and focus on the results necessary for the discussion part.
Additionally, there are many explanations for the variation in microbial communities with depth or among vegetation types that are vague and do not necessarily reflect current knowledge, (e.g. line 266 “particularly in bacterial biomarkers with increasing soil depth”, line 286 ”This might suggest a possible competition between AMF and saprotrophic fungi or Gram- bacteria”, see technical comments for explanation to why this seems counterintuitive).We agree that using terminology such as “particularly” or “might suggest” is not precise. We removed the qualitative judgments and stated clear if a change is significant or not.
There is a strong need to strengthen the discussion in general and revising some of the argumentations for variations in microbial communities (see technical comments for more detailed information).Thanks for this comment. We do agree and will revise the discussion part accordingly in the next version of the manuscript.
Conclusion
The conclusion focuses on differences in litter quality as the driving force of microbial community composition (PLFAs and GDGTs). Litter quality is not mentioned in the material and methods of this study but was assessed by the authors in another study in 2023. If this in fact is the main driving force of variation in microbial community composition, then the data must be included in the results and the methods.
Thanks for your suggestion. We agree and will include this information in the M&M section and in the newly added paragraph in the result section, where we will report the missing information for the bulk parameters.
Technical comments
26-29 please specify what kind of increase; with age? general? Only in subsoil?
Thanks for your comment. We will specify this increase in the next version of the manuscript. “This trend, however, was reversed with a decreasing bacterial community over the entire soil depth of 45cm with increasing forest age when considering GDGT biomarkers”.
41-44 it is difficult to follow the argumentation here, please explain how organic matter decomposition in deeper soil layers is enhanced by lower inputs of carbon
Thanks for mentioning this and we agree with it and will explain in more detail how the OM decomposition in deeper soil horizons is enhanced by lower carbon inputs.
45-50 please give some more detail how litter quality shapes microbial communities
Thanks for this comment. We will provide some examples in the introduction section on how litter quality shapes the soil microbial community.
63-64 unknown or Acidobacteria? Please rephrase for clarification if this is a yet unknown species belonging to the phylum acidobacteria or only some of them are Acidobacteria but others are unknown etc.
They are produced by unknown bacteria but some of them might belong to the phylum Acidobacteria. But we agree with your comment, and we will rephrase this clearly in the next version of the manuscript.
64-67 “possibly feeding on root carbon sources” is probably meant to describe the organisms producing brGDGTs. Please rephrase for clarification, also mentioned the same way in 347
Thanks for mentioning this and we will change accordingly. “In contrast with archaeal GDGTs, bacterial GDGTs are constituted of branched alkyl chains instead of isoprenoid ones and are referred as branched GDGTs (brGDGTs). Such brGDGT producing bacteria are known to use root-derived carbon as a potential food resource (Huguet et al., 2012; Gocke et al., 2016).”
68 in a similar vein to in a similar way to
We will change this accordingly in the next version of the manuscript. “In a similar way to the PLFA analysis, intact GDGTs still being attached to a polar headgroup are attributed to the living biomass, while core lipid GDGTs without any polar headgroup are attributed to the bacterial necromass (Gocke et al., 2017).”
71-73 not sure if the turnover time refers to the total GDGT molecule (polar head and apolar core) or just the core. Likely for the core in which case this can’t be used as a biomarker for living biomass; needs clarification that this is a (archaeal necromass biomarker only) ; it is unclear how this is improves the time-integrated signal of soil microbial abundance compared to PLFAs
Thanks for pointing this out. And we agree. The turnover times refer to the necromass. We will therefore clarify this in the next version of the manuscript.
86 fungi are part of the soil microbiome
Thanks for your comment. We agree and we will rephrase this accordingly in the next version of the manuscript and will write soil microbial community, which is used for both fungi and microbes.
94-95 pastures mentioned here to contain less easily decomposable organic matter, but this is countering the overall argumentation
Thanks for mentioning this. And we agree that it was not so clearly formulated. The statement “where less easily decomposable organic matter predominates” is correct for the forest and not for the pasture. We will rephrase this accordingly in the next version of the manuscript. “Due to the already reported alteration in the litter quality towards more recalcitrant (high C:N ratio) litter input in this subalpine afforestation sequence(Hiltbrunner et al., 2013; Speckert et al., 2023), we hypothesize an increase in Gram+ bacteria and in the fungal communities with increasing forest age where less easily decomposable organic matter predominates, in comparison to the pasture”
95-97 overall GDGTs or only branched ones? There is no argumentation found above for a preference of archaea for labile carbon sources
Thanks for pointing this out. We hypothesized this for brGDGTs and isoGDGTs, the latter is more abundant in pasture than in forest, and so also their source microorganisms.
146-148 actinobacteria are also gram+ bacteria, labelling of gram+ bacteria must be changed to address this (e.g. rename gram+ to firmicutes, consult literature), interpretations in the discussion and report in the result section need to be addressed accordingly
Thanks for this comment. For this manuscript we used the common classification according to literature (Macdonald et al., 2009 https://doi.org/10.1016/j.soilbio.2009.05.003; Willers et al., 2015 https://doi.org/10.1111/jam.12902) and to preexisting studies (e.g. Hiltbrunner et al., 2012 https://doi.org/10.1016/j.geoderma.2011.11.026) in the same study site to achieve comparability.
150-151 One replicate per stand age can’t be used to interpret differences among forest stand ages and pastures, two replicates is also highly questionable
Thanks for this comment. For both of our proxies we have measurements in duplicates (analytical replicates) and references with certified external standards as control. Additionally, also with one sample for GDGTs and two replicates for the PLFAs, we are able to show differences in depth trends and difference in the variability between alpine forests and pastures. Further our goal was to have a look at both the bacterial and archaeal communities, which is not possible if we only consider PLFAs. Although it would have been great to have more replicates, we were limited by monetary and time restrictions to conduct a more comprehensive study.
165-168 the F:B ratio is calculated by fungal PLFAs divided by bacterial PLFAs
Thanks for mentioning this. And we will change this mistake accordingly in the next version of the manuscript. “The F:B ratio was calculated by PLFA-derived fungal biomass (saprotrophic fungi and AMF) divided by PLFA-derived bacterial biomass (Gram+, Gram- bacteria and actinobacteria).”
177 would help understanding (and referencing later one) if the abbreviation IR6Me is mentioned in full length above.
Thanks for this comment and we agree with this. We will add this information in the next version. “The relative abundance of 6-methyl over 5-methyl brGDGTs was calculated using the isomerization ratio (IR) according to De Jonge et al.(2014; Eq. 2), which compares the relative abundance of 6- and 5-methyl homologues among brGDGT-II and brGDGT-III groups.”
185-187 pasture has a higher mean value than the 55-year-old forests for the 0-5 cm
Thanks for pointing this out. We will rephrase this accordingly in the next version of the manuscript.
210-213 “which was not observed in the pasture, the 40-year-old or 130-year-old forest” maybe this additional information is not needed since it is mentioned already that this is specific to 55-year-old forest
Thanks for mentioning this. We agree with your comment, and we will remove the unnecessary information in the next version of the manuscript. “The fine root biomass correlated strongly with all individual PLFA compounds with the exception of the actinobacteria in the 55-year-old forest (Fig. A4a to e).”
213-215 “common to all areas” but then mentioning 40-year-old forest specifically (in regard to what?) please rephrase, it would probably also be worth to mention the overall effect on fungi since relative effects of pH on bacteria and fungi are predicted to differ
Thanks for this comment. We wanted to highlight that this negative correlation was most prominent in the 40-year-old forest, even though it was observed in all areas. We also agree that it would be worth to mention the correlation between soil pH and fungi and we added this additional information in the next version of the manuscript.
217 Unfortunately I must strongly advise against using this data since one data point can’t be statistically evaluated; section was still reviewed for the sake of completeness
Thanks for this comment. However, we have a slightly different opinion on this. Although there is only one sampling point for the GDGT proxy we can still retrieve valuable information as well as comparison between the data. Additionally, part of these sampling points was measured in duplicates with additional reference samples included in the analytical sequence to control the reliability of the results.
221-222 this is only true for the 130-year old forests which needs to be mentioned in this sentence to avoid confusion
Thank you for this comment and we will clearly state in the next version of the manuscript, that this is only true for the130-year-old forest.
224 it should say IIa instead of IIb
Thanks for pointing this out and we corrected this mistake in the next version. “The brGDGTs Ia, IIa, and Ib represented altogether approximately 50% of all brGDGTs in all soils. In the 130-year-old forest, the brGDGTs Ia, IIa, and Ib altogether account for 60 – 70% of all brGDGTs (Table B4).”
227-229 mentioned are only IIb’ and IIIb’ but not IIa’ and IIIa’, the concentrations only spike in 35-40 cm but besides that the major groups seem to follow the same trajectory then all other compounds (decreasing with depth)
Thanks for this comment. It is true that also the concentrations in IIa’ and IIIa’ increase in that particular soil depth. We will also add this information in the brackets in the next version of the manuscript.
264-266 fungi are often described to be decreasing stronger with depth since they are more associated with roots, the citations also don’t match the described observations (one of them focuses on microarthropods and neither focus on depth) please add citations describing depth related distribution patterns of fungi and bacteria
Thanks for your suggestions and we agree to elaborate more about the depth related distribution patterns of bacteria and fungi in the next version of the manuscript. We will also check the citations again and will remove those citations, which are not suitable.
278 if still comparing to Francisco et al. (2016) then both investigate grass vegetations with grass species. Difficult to understand the point here
Thanks for your comment. We apologize for the misunderstanding, but we do not clearly understand what we are supposed to change here.
280-284 not clear to understand, root exudates are present in all soils only relative amounts vary, r2 instead of r
Thanks for your suggestion. We will change from r into r2 in the next version of the manuscript.
299-300 however you found an overall effect irrespective of the cyclisation ratio
Thank you for this comment. And we will rephrase this in the next version of the manuscript.
308 the definition of substrate quality is questionable, soil pH does not describe substrate quality and vegetation cover may explain the amount of substrate available (although this has to be confirmed experimentally) but does not reflect on litter quality, carbon concentration of substrate is always organic and quality is therefore described through the C:N ratio already
Thanks for mentioning this. We do agree and will delete soil pH in the brackets in the next version of the manuscript.
314-315 the C:N ratio is known, right? Could be explored in the scope of this study
Thanks for your comment. Yes, the C:N ratio is known, and we will add this information with the respective citation in the discussion part in the next version of the manuscript. “This might suggest a low C:N ratio as well as a lower carbon and nitrogen availability, which might explain the constantly lower bacterial and fungal abundance in the 55-year-old forest (C:N 54.7±3.9) compared to the 40-year-old (C:N 57.1±2.6) and 130-year-old forest (61.2±2.9; Speckert et al., 2023)”
316-319 does this only apply to bacteria though? Citations seem again out of place (no bacteria studied in the first mentioned citation)
Thanks for mentioning this. And yes, this still applies for the bacterial community. We will add this missing information in the next version of the manuscript. “The key role of organic carbon and particularly nitrogen for soil bacterial abundance was observed in numerous studies (Fierer, 2017) and was further supported by the positive correlation between organic carbon and nitrogen concentrations and the bacterial community in older forest stand ages in this study (Fig. A2 and A3).
330 what do you mean by increased decomposition of old organic matter? Where is this reported
Thanks for your comment. Old organic matter is used in this manuscript as more microbially processed OM, which is more often located in the subsoil (Rumpel and Kögel-Knabner, 2011). The decomposition of OM located in the subsoil in this specific study site, especially in the oldest forest stand, was previously reported in other studies on this specific afforestation sequence (Hiltbrunner et al., 2013; Speckert and Wiesenberg, 2023), which is now further supported by the reported higher concentration of Gram+ bacteria. We will restrict to “microbial processed” to avoid further confusion.
333-336 AFM to AMF; organic matter decomposition is seldomly seen in AMF, the cited paper reports much higher AMF values in pastures
Thanks for mentioning this and we will correct this typo in the next version. The respective paper was used due to their statement that the presence of lignin decomposing fungi might be one explanation for a higher fungal concentration. But we do understand that it might be confusing for the reader ad so we will therefore replace this by a more suitable citation.
346 the organisms producing brGDGTs not the molecule
Thanks for this comment and yes, we agree, and we will rephrase this sentence in the next version of the manuscript. “A possible explanation might be the preference of brGDGT producing organisms for root carbon as a food source (Ayari et al., 2013; Huguet et al., 2013).”
384-397 highly speculative, there is little explanation why this should apply to the 40-year-old and 55-year old forests as well since temperature differences are only reported for pastures, if this can’t be backed up by further data it is advisable to drop this explanation
Thanks for your suggestions. And we will drop this explanation in the next version of the manuscript.
408-410 isoGDGTs are the only type of GDGT that is elevated in pastures, so archaea (additionally this means only an increase in archaeal necromass) is increased but they are not described here to be specifically associated to roots or labile carbon in comparison to other microbial groups, brGDGTs show not really a difference between pastures and 40 year and 55 year old forests according to the data presented
Thanks for mentioning this and we will add additional information about the relationship between fine root biomass and isoGDGT, especially in the pasture.
Figures
Information in the subtext should describe the unit, the meaning of the data points (e.g. mean) and the replication number
Thanks for pointing this out and we agree. We will add the units and the description of the data points including the number of replications in the caption of all figures.
Supplementary
Table S1.
pH value and variation are exactly the same for 55-year-old forest and 130-year-old forest
Thanks for pointing this out. We will correct this mistake in the next version of the manuscript.
Table S3.
NA value in 40-year-old forest in the wrong cell (35-40 missing AMF)
Thanks for mentioning this. We will correct this mistake in the next version of the manuscript.
Thank you.
Citation: https://doi.org/10.5194/egusphere-2024-870-AC4
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