Microbial dynamics in a High Arctic glacier forefield: a combined field,
laboratory, and modelling approach

Bradley, James A.; Arndt, Sandra; Šabacká, Marie; Benning, Liane G.; Barker, Gary L.; Blacker, Joshua J.; Yallop, Marian L.; Wright, Katherine E.; Bellas, Christopher M.; Telling, Jonathan; Tranter, Martyn; Anesio, Alexandre M.

doi:https://doi.org/10.5194/bg-13-5677-2016

Articles | Volume 13, issue 19

https://doi.org/10.5194/bg-13-5677-2016

© Author(s) 2016. This work is distributed under
the Creative Commons Attribution 3.0 License.

https://doi.org/10.5194/bg-13-5677-2016

© Author(s) 2016. This work is distributed under
the Creative Commons Attribution 3.0 License.

Articles | Volume 13, issue 19

Research article

|

13 Oct 2016

Research article |

| 13 Oct 2016

Microbial dynamics in a High Arctic glacier forefield: a combined field, laboratory, and modelling approach

James A. Bradley, Sandra Arndt, Marie Šabacká, Liane G. Benning, Gary L. Barker, Joshua J. Blacker, Marian L. Yallop, Katherine E. Wright, Christopher M. Bellas, Jonathan Telling, Martyn Tranter, and Alexandre M. Anesio

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Final revised paper (published on 13 Oct 2016)
Supplement to the final revised paper
Preprint (discussion started on 16 Feb 2016)
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Interactive discussion

Status: closed

AC: Author comment | RC: Referee comment | SC: Short comment | EC: Editor comment

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RC1: 'review: Microbial dynamics in a High-Arctic glacier forefield: a combined field, laboratory, and modelling approach.', Anonymous Referee #1, 16 Mar 2016
RC2: 'Review', Anonymous Referee #2, 22 Mar 2016
AC1: 'Final response to referees', James Bradley, 29 Apr 2016

Peer-review completion

AR: Author's response | RR: Referee report | ED: Editor decision

ED: Reconsider after major revisions (10 May 2016) by Michael Weintraub

AR by James Bradley on behalf of the Authors (18 May 2016) Author's response Manuscript

ED: Referee Nomination & Report Request started (01 Jun 2016) by Michael Weintraub

RR by Anonymous Referee #3 (13 Jun 2016)

Suggestions for revision or reasons for rejection

This is an interesting paper which presents an important step forward by linking field, lab and modelling work to understand the predictability of soil microbial community development within glacier forefields, a "hotspot" of impacts from contemporary environmental change. Nevertheless there are areas which I feel need to be handled carefully in a revision:
1. 16S community sequencing data. A valiant effort to test the biogeochemical model presented at this resolution. Importantly, sequencing data should be made publicly available at a recognized sequence archive such as the short read archive. I understand what the authors are trying to say that studies rarely test sequence data against models, but in a sense sequence data are frequently tested against models in the form of constrained ordination or hypothesis testing. This claim could be clarified or dropped. I believe the manuscript should describe the 16S data more clearly by adopting more conventional forms of expressing community composition and its spatial turnover, even as supplementary data.

2. On the topic of sequence data, I find the authors' assertion that the Betaproteobacteria necessarily represent subglacial taxa without data from subglacial habitats unwarranted. Betaproteobacteria including Comomonadaceae are also present in supraglacial habitats, including snow and ice melt on Svalbard glaciers, as shown by several studies. Perhaps changing "subglacial bacteria" to "glacial bacteria" would be more inclusive and easier to justify on the basis of the data presented here.

3. BGE, growth, respiration and temperature. The authors clearly are aware that 5*C is a "typical field temperature" (L208) for their Svalbard site, but conduct their growth rate determination and the respiration assays for model parameterization at 25*C for comparison with earlier work, and specifically a study of alpine glacier forelands, where a summer temperature of 25*C is not unrealistic. The Q10 data and the respiration data plotted in Fig 2c clearly evidence a considerable degree of temperature dependence in respiration rates. While I appreciate the motivation of the authors to compare their data with earlier alpine studies, I find the use of assay temperatures four degrees Celsius warmer than the record high Svalbard temperature, and twenty degrees Celsisus warmer than what the authors and I seem to agree to be typical of Svalbard summers to estimate parameters pertaining to what is clearly a temperature sensitive community troubling. I believe the authors need to robustly justify why this would not affect their conclusions.

4. Bacterial growth efficiency. Equation 1 defines BGE as the inter-relationship of bacterial production and respiration. Leaving aside the temperature dependence of respiration addressed in 3., the estimation of BGE here is troubling. While carbon production by the heterotrophic bacterial community is appropriately measured via leucine incorporation assays, the authors seem to define "bacterial"/"microbial" rather loosely for respiration. For bacterial respiration data, the authors present CO2 gas exchange rates in section 2.4. This will include non-bacterial microbial respiration (e.g. fungi, protozoa, archaea...) and potentially meiofaunal respiration within their soil samples. No data on these taxonomic groups normally found in soils and protosoils is presented to exclude their potential contribution. As such, bacterial respiration is but one (potentially major, admittedly) component of the CO2 gas exchange rates, but not the totality, and this may change along their chronosequence in response to changes in fungal/bacterial ratio apparent in forefield soils. The authors should carefully address the uncertainty engendered by the non-equivalency of bacterial and total community respiration.

5. Line 695. The invocation of SHIMMER as a tool for examining microbial populations in the ice free regions of Antarctica seems a non sequitur as a major conclusion of this study of community development in a High Arctic forefield soil. Perhaps this is intended to address a reviewer's comment about the broad applicability of the study, but it seems a leap. It would be probably more sensible to discuss the increasing importance of glacier forefields as novel terrestrial habitats responsive to contemporary climatic warming rather than elevating this aside to a main conclusion.
Minor comments/presentational issues:
L155: how long between sampling and freezing? Were the samples transported frozen to the UK, and how?
L181: How much sample was used (mg) for each extraction and how much template was used for each PCR. Provide a reference for the primers.
L191: "Non barcoded"? How were the samples demultiplexed?
L194-: More detail on sequence processing is required here. This would be a good place to provide accession numbers for the sequence archive.
L405: chemolithotrophs
L405 and throughout. Microbial genera need to be italicized consistently.
L487: If Midtre Lovenbreen is referred to as such, East Brogger Glacier should be referred to as Austre Broggerbreen for consistency.
L617-L622: Here the authors invoke caveats to their DNA data. A thought: How might dormancy or death affect their insights? Differentiating between dead or dormant cells on DNA data is challenging, and only some of these taxa may be metabolically active.
Figure 5: Less accessible to readers with colour vision perception difficulties.

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RR by Anonymous Referee #2 (29 Jun 2016)

Suggestions for revision or reasons for rejection

I appreciate the many revisions made by the authors to their manuscript in response to comments from both reviewers. The current version is much improved. I still think that the introduction (first paragraph) predisposes the reader to anticipate that glacial fore-fields will generate positive feedback between net CO2 efflux, atmospheric CO2, and global warming, despite explanations. I suggest omitting lines 46-53, which are mostly tangential to this study, and focus specifically on glacial retreat and the newly exposed soil communities. The rest of the paragraph also raises points about methane production, P-cycles, and downstream productivity that have nothing to do with this study. I suggest focusing the introduction clearly on the primary elements of this study (mostly found in the second paragraph).

Line 27: Word choice -- models are not usually considered to validate observations, but rather observations validate models. Perhaps a better word would be simulated?

Lines 104-105: Again, the authors explained that these sorts of plant-free sites are common both in the high arctic and Antarctic, so it would help readers to make that statement herein. As worded, I had the impression that this was a unique feature of the study site rather than representative one.

Lines 209-201: I suspect that the selection of the highest microbial biomass site for these determinations was more a matter of practicality than appropriateness. Practicality can be demonstrated via measurements of microbial mass, activity, etc… whereas appropriateness cannot be defined.

I agree with the reviewer 1 that only using 2 temperatures to derive a Q10, including one at 25C (very high for these systems), particularly when it’s such an important parameter, is a weakness in the study design. The detailed sensitivity analysis compensates to some extent, although a high Q10 coupled to low BGE do explain low biomass. The authors discuss this interaction, but it is key to simulated C dynamics and I recommend reiterating it in the conclusions.

It was fascinating that there was essentially no nutrient response in experiments, but as the authors noted, such a low BGE reduces nutrient limitations. Again, this point should be reiterated in the conclusions as it is a key outcome of the model.

Line 376: ImaxH is a growth rate coefficient (units = 1/day), not a growth rate (mass/day), the latter being the product of ImaxH x biomass. This was confusing until the authors explained it in their responses.

Lines 500-501: Because both source and fate of allochthonous C inputs are uncertain, if these sites remained frozen, would these C inputs simply be partly processed downstream? The argument for these newly thawed sites being C sources to the atmosphere is probably more uncertain than stated. Maximum simulated loss rate is 4 ugC/g/yr (table 3), which would be 400 ugC/g over a century, which is a small amount generated by uncertain parameters. I suggest placing some estimates of variability around these estimates.

This version of this manuscript has a much better discussion of community structure (16S data) and comparison with biomass (microscopy) data. As the authors noted, this work is among the first to compare simulations with observations and indeed ought to spark discussion.

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ED: Reconsider after major revisions (30 Jun 2016) by Michael Weintraub

AR by James Bradley on behalf of the Authors (27 Jul 2016) Author's response Manuscript

ED: Referee Nomination & Report Request started (04 Aug 2016) by Michael Weintraub

RR by Arwyn Edwards (05 Aug 2016)

Suggestions for revision or reasons for rejection

The authors have made a sincere and detailed effort to improve the manuscript by addressing comments made in the earlier reviews. I am still wary about the use of measurements at 25*C with soils conditioned to 5*C, but can accept its necessity for the present study. The open nature of the review process offers readers with the inclination an opportunity to view the arguments for and against the use of 25*C temperatures.
Sequencing 16S rRNA genes to parameterize the model. I still have problems here. It is assumed that shifts in the absolute quantities of different functional/taxonomic groups are meaningfully represented by DNA extracted from varying quantities of samples, amplified and sequenced to an unstated but incomplete depth, used to generate relative abundance profiles of sequence libraries which may differ in read number, and in any case are based upon sequences from a locus which has variable numbers of copies per bacterial genome, a source of variation which is known to be related to ecological traits important in glacier forefield successional processes and itself recapitulated within the data. Specifically:
A. L179: Thanks for updating the details here, but I have concerns over “5-10 grams of sample” being used for DNA extraction.
1. If this is the case, the statement DNA was extracted by “MoBio PowerSoil® DNA Isolation Kit and by following the instruction manual cannot be the case. This kit processes samples in 2 mL tubes for bead beating. The standard recommendation from the manufacturer is for 250 mg samples (and I have had no problems with getting enough DNA from forefield soils for amplicon sequencing from 250 mg using the standard protocol.) The key point is that 5-10 grams would not fit, and any more than 250-500 mg clogs the bead beating tube to the point that extraction efficiency is reduced, making using more sample counterproductive, so I think there’s a mistake here. Did the authors actually use a PowerMax kit which can process up to 10 g of sample in a very different format, or modify the powersoil protocol to pool extracts from multiple 250 mg extracts? This may seem a trivial detail, but establishing how you extracted the DNA is important to establish whether the sequencing data have any relation to the soil community.
2. So, some of your samples were 5 grams and some were 10 grams? How did you account for up to two fold variation in sample mass, with the implications for the total biomass in the tube, and furthermore the extractable biomass as a result of variation in extraction efficiency from the consequently variable ratios and mixing in volumes of sample, beads, buffer and tube during bead beating?
B. L193-200: To establish the depth of sequencing and how many reads were there per barcode, and was the depth of sequencing? In other words, how can the reader be assured that your sequencing effort meaningfully describes the community, and that your relative abundance profiles are from roughly equivalent (or rarefied) numbers of reads. This matters because you are using proportional data from sequencing libraries to make estimations of absolute contributions to the soil community your model describes.
C. From the taxonomic profiles I see important changes in the community’s composition and configuration which mirror other work on transitions between oligotrophic and copiotrophic taxa in a variety of glacier chronosequences. That transition is associated with changes in ribosomal RNA gene copy number per genome. There are bioinformatic means of normalising this variation in rRNA copy number, for example CopyRighter (DOI: 10.1186/2049-2618-2-11).
I would hope the authors can state succinctly the measures taken to address problems A and B, and caveat their discussion to address concern C. This would serve to improve this paper, and perhaps consideration of these issues will help the other paper mentioned in their response which will probably rely on this 16S data a central pillar. As a general thought, for future endeavours and considering the broad taxonomic resolution desired by the authors to inform their model, I feel there are more appropriate tools for this job. If DNA based analyses were needed, qPCR or FISH would have provided data more closely linked to microbial abundance. Otherwise, PLFA would have provided taxonomically-informed estimates of contributions to biomass.

Minor comments.

L180: At this point it is not isolated rDNA; it will be community genomic DNA, from which you will specifically amplify bacterial 16S ribosomal RNA genes (rDNA itself is a common misnomer too, by the way: the gene product is rRNA, hence rRNA gene)
L183: dNTPs

Accession numbers: Hopefully NCBI will have returned the numbers soon.

Response: “ Assuming that predation rates and dormancy are the same on all functional groups (as is defined in SHIMMER),” I advise caution in making that assumption as these traits are varied across the breadth of soil microbiota.

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ED: Publish subject to minor revisions (Editor review) (05 Aug 2016) by Michael Weintraub

AR by James Bradley on behalf of the Authors (14 Sep 2016) Author's response Manuscript

ED: Publish as is (26 Sep 2016) by Michael Weintraub

AR by James Bradley on behalf of the Authors (26 Sep 2016) Author's response Manuscript

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Short summary

Soil development following glacier retreat was characterized using a novel integrated field, laboratory and modelling approach in Svalbard. We found community shifts in bacteria, which were responsible for driving cycles in carbon and nutrients. Allochthonous inputs were also important in sustaining bacterial production. This study shows how an integrated model–data approach can improve understanding and obtain a more holistic picture of soil development in an increasingly ice-free future world.