the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
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
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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 -
RC2: 'Comment on egusphere-2024-870', Anonymous Referee #2, 15 Jul 2024
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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
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