Comments to S. van Grinsven et al. Proglacial wetlands: an overlooked CO2 sink within recently deglaciated landscapes.

This manuscript reports on the effect of moisture status (wetland or dryland) and age-since-deglaciation on either CO2-drawdown of CO2 emission from incipient soils. The used language is OK and understandable, but the organization of the manuscript is messy. The separation of work done by the authors that from other studies is not always clear. I assume the measurements are OK, but explanation of the mechanisms explaining the measurements is a bit too haphazard. Some mechanisms are ignored (e.g. effects of weathering and parent material in this versus other studies), some mechanisms are brought forward that strengthen some measurements but at the the same time weaken results elsewhere (e.g. l.202).

At this moment I would not support publication unless after a major restructuring of the paper including cleaning up some reasoning.

Some comments follow hereunder:

Manuscript organization

The topic is interesting, but is addressed poorly and apparently written down in a hurry. 

A. I found the section order 1. Introduction; 2. Results and discussion very strange, why put all material and methods only in an appendix? In this appendix, essential information seems to be lacking (homogeneity of the parent material, precipitation).

B. Where do I find a research hypothesis, research questions, a research approach and clear conclusions? Why is on l.74 already a conclusion mentioned, in the Introduction?

This manuscript needs major reorganization to avoid the impression of an haphazard investigation. 

Detailed comments

l.74: "We however show": this is a result, not part of an introduction. "show">"suspect"? This could then lead to a research question motivating what was done.

Fig.1: What is a GLIM? Better not put unexplained abbreviations in a figure caption

l.104: Why the Bachfallenferner area? Why is it particular suitable, to address what research question? 

l.116: This sentence is Material&Methods, not Results&Discussion

l.123-125: This sentence is a conclusion.

l.127-142: This appears speculative: the CO2-flux cannot be described by the plant communities (mostly absent), thus it must be the microbial community. Explanation needed! What makes the community drawdown atmospheric CO2? Could not also the composition of the drainage water from the glacier be a factor? Describe the chemoautotrophic pathways. Do these involve weathering? What would be a weathering pathway in the Bachfallenferner area, given the parent material(s)? A vague link to "microbial genes" should be elaborated.

l.148: Apparently, Guelland et al (2013) found an effect of burned allochthonous carbon, releasing CO2. You explain some emission sites by this mechanism. Any evidence? Did you observe incoming allochthonous carbon, e.g. by the color of the water?

l.156-158: Yes, CO2 drawdown can result directly from mineral weathering (e.g. proton consumption by weathering stimulates production of carbonic acid, from atmospheric CO2), and complexation with minerals and weathering products can slow down mineralization. As stated, this can occur in older soils (more weathering), so why do you also find the drawdown in the young wetlands?

Fig. B2: unclear caption. Upper graph=?= left graph, lower graph=?=right graph. Does the site coding make sense, what is 1-S, a soil of 1 year old? What is the soil depth? Rock-stone-fine earth correspond to what color/gray tone? Left graph shows color options no color-light-medium-dark green = 4 options, right graph=gray-green-blue.

l.160-182: more like a literature review than a discussion on your results.

l.183-192: Some speculative hypothesis are formulated here, like effects of erosion/sedimentation. Could be true, but I am not sure this is not just a "pick" of some possible mechanisms. E.g., could wetlands not be a carbon sink because of presence of aquic microbial species and/or carbonate water equilibria which are mostly absent in dryland soil? 

l.202: The wording "indeed" states that microbial activity may be associated with higher water content, but this seems to contradict with your findings on higher CO2 drawdown in wetlands. Explanation?

l.222-231: Environmental covariates: indeed it would be nice to identify environmental covariates explaining the observed fluxes. Guelland et al assigned this to high heterogeneity, how about this argument in your study? Are the parent materials homogeneous? What is the contact time between transported water and the substrate, relating to nutrient concentrations?

l.349: sampling excluded lakes, but in l.352 they are included? 

l.377 etc: fluxes were measured only at daytime. Is it then not possible that, when brought to 24h time span, many sinks become sources? It also makes me wonder how much the sink/source discussion is a function of the measurement season (now: 5 days in August). This should be in the discussion for sure.

van Grinsven et al. report on carbon stock and carbon dioxide flux differences between wet and dry sites in the proglacial area of the Bachfallenferner glacier in the European Alps.  The researchers demonstrated that the wet sites stored more carbon in soil than the dry areas in their space-for-time analysis. They also showed that the wet areas tended to more consistently have CO₂ uptake than the dry areas over their measurement period, regardless of age of the site. Overall, this research demonstrates local hydrological conditions are important for understanding carbon dynamics in proglacial areas and have the potential to store more carbon than would be anticipated by only studying dry sites. I enjoyed reading the article and it is suitable for publication in SOIL pending moderate revisions. My main concerns with the article surround how the total carbon mass in the soils was calculated and whether the study has enough information to justify calling the wet areas carbon dioxide sinks. I also think the paper would benefit from a few additional analyses surrounding the correlations between organic matter content and carbon dioxide fluxes with plant cover. Details are outlined below with associated line numbers.

Abstract:

Line 21: “key locations of CO₂ uptake and a significant role in carbon storage in the proglacial valley” – based on the study design I think it can be justified that these areas generally have more uptake of CO₂ than the dry areas in the summer, but because the study does not have fluxes outside of August it may be a bit misleading to say they are key locations of CO₂ uptake generally. Same goes for the title of the article.

Line 22: “despite their small surface area” – can a rough percent estimate for the area of the wetlands within the proglacial area be given? This will help to give further context to their relative importance in proglacial areas.

Line 22: “Loss-on-ignition” – I think these results should be presented somewhere in the paper, so that the reader can evaluate how many of the sites have high organic matter content. I suggested Table S2 below.

Figures:

Figure 1: Should the yellow border be visible around the entire proglacial area like the orange and blue perimeters? Write out the acronym GLIMS and provide the reference (12 in the reference list). Add an inset map showing where the study site is within Austria.

Figures 2/3: I suggest adding mean plant and moss cover for each age in these graphs to clearly demonstrate when vegetation appears in the wet and dry areas in the main text. This is one of your key datasets and you should showcase it!

Results and Discussion:

Line 124: “quantify the surface area of wetlands” – as mentioned in my comments for the abstract (Line 22), can an approximate percentage for wetland area be provided based on field observations?

Line 132: “plant community is limited” – when looking at Figure B2, it seems like almost all the sites do have some amount of plant cover, which would presumably contribute to CO₂ uptake. I suggest investigating whether there is a correlation between percentage plant and moss cover and carbon dioxide flux/carbon mass. This would either support or refute the hypothesis is this study that CO₂ uptake is microbially derived. For example, if the correlation was not strong in younger sites vs. older sites, then it would support that the microbial community is playing an important role at the younger sites. The correlations may also be different for the dry vs. wet sites. This analysis would also support the discussion starting at line 195.

Line 156: One could also perform fluxes when the chamber is shaded or clip the vegetation prior to measurement in the field.

Line 160: This paragraph is related to Figures B3 and B4. I would add a sentence here before discussing the age relationships to draw the attention of the reader to them.

Line 172: “linear increase in soil organic carbon content” – does the data from this study (i.e., LOI and age of site) also have this same pattern? Is it different for dry vs. wet soils?

Line 184: “significantly higher CO₂ uptake rates” – was this tested statistically? Please provide the statistical summary.

Line 193: “Supplemental File 2” – I don’t see the LOI results in the supplementary file (see comment for Table S2).

Line 195: Figure A should be Figure B1?

Line 219: “consistent uptake” – keep in mind that this study records consistent uptake spatially but not temporally, especially since, as mentioned in the discussion here, glacial meltwater does not have a consistent flux through time. Also, I am not sure that having consistent uptake means that allochthonous CO₂ production is limited, as the net CO₂ flux was measured in this study. Please provide more details on the reasoning for this discussion point.

Line 222: As stated above (Line 132), looking at correlations to vegetation cover is missing in this list.

Appendices:

Line 411: The description of the conversion to µM m^-2 hr^-1 is consistent with the text, but in Figure 2 and Table S1 the values are in mg C m^-2 hr^-1. Make the units consistent across the text and figures.

Line 436: Is assuming 1500 kg m^-3 across wet and dry soil types for all ages of site appropriate? Where does this bulk density value come from? Please provide a reference and more justification. The density of organic soils is typically much lower than 1500 kg m^-3. For example, the average bulk density of peat in northern peatlands is 118 kg m^-3 (Table 1; Loisel et al. 2014 Holocene). Even if the sites are not peat forming, I would expect the bulk density to decrease as organic matter from soil formation is incorporated. By using a high bulk density across all the site locations, you may be overestimating the amount of soil carbon mass.

Figure B1: Also include pictures of a representative dry area for comparison?

Fig B2: upper and lower should be left and right. I suggest adding labels to the plots (A and B) and describing each under those labels in the figure caption.

Figure B3/B4: display the equations and the 95% confidence intervals?

Table S1: add the R2 values for each flux.

Table S2: Is there a reason the loss-on-ignition results not been listed here? It would allow readers to better understand how the organic carbon stock was calculated. Maybe this is the Supplemental File 2 mentioned in the text? (Line 193).