the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 06 Feb 2023
The marine methane cycle in the Canadian Arctic Archipelago during summer
Abstract. In the Arctic Ocean region, methane concentrations are higher than the global average; high concentrations of dissolved CH4 are detectable especially across many subarctic and Arctic continental shelf margins. Yet the Arctic Ocean appears to emit only minimal methane fluxes to the atmosphere across the air-sea interface, suggesting water column oxidation of methane may be an important process. Here we paired thermohaline, chemical, and biological data collected during the Northwest Passage Project transit through the Canadian Arctic Archipelago (CAA) waters in the Summer of 2019, with in-situ and in-vitro methane data. Our results showed high meltwater (meteoric water + sea ice melt) throughout the Western CAA and Croker Bay in the East, and these surface meltwaters showed methane excess. The meteoric waters showed a strong correlation with chlorophyll-α fluorescence (r=0.63), as well as a correlation between dissolved [CH4] and chlorophyll-α fluorescence (r=0.74). Methane oxidation rate constants were highest in Wellington Channel and Croker Bay surface waters (av. 0.01±0 d-1), characterized by meltwaters and Pacific-origin waters. The average oxidation rates in meteoric and Pacific waters were respectively 24.4 % and 12.6 % higher than the entire survey average. Moreover, Pacific and meteoric waters hosted microbial taxa of Pacific-origin that are associated with methane oxidation, Oleispira (γ-proteobacteria), and Aurantivirga (Flavobacteria). The deeper layers were characterized by low methane concentrations and low methane oxidation rate constants (av. 0.004±0.002 d-1). Sea ice covered much of the Western CAA, in the same region with high sea ice meltwater concentrations. These waters also hosted higher average methane oxidation rates (av. 0.007±0.002 d-1). To the east, open coastal water coincided with methane enrichment, but low chlorophyll fluorescence and weak methane oxidation. These results suggest that methane production in ice-associated Arctic blooms may be quickly oxidized by microbes that are also found in these waters, associated with seasonal biology.
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RC1: 'Comment on egusphere-2023-74', Anonymous Referee #1, 28 Feb 2023
The manuscript presents a dataset including nutrients, methane concentration in seawater and ice, and calculations of methane oxidation rates and constants. The authors investigate the possible source of the methane. They propose that microbes can rapidly oxidize methane produced within the ice during Arctic blooms, and they also conclude that sea ice is oversaturated in methane and that meteoric waters have higher methane oxidation rates than Atlantic waters.
The overall story is not very convincing with many inconsistencies when comparing numbers in the text and figures or tables, and sometimes figures not correctly sited. New information is also mentioned in the discussion or the conclusion with no support from figures or tables (e.g. lines 691, 722, 769, 779). The nutrients results are not presented until the conclusion. Moreover, many instances of plagiarism from Uhlig’s work should be avoided by referring to their papers. I have several issues throughout the text as presented below.
The abstract presents some information from a rejected companion manuscript (D’Angelo et al., 2022, https://doi.org/10.5194/essd-2022-306) and this information is not mentioned in the rest of the manuscript (e.g. chl. A correlation with meteoric waters and methane concentration in the abstract). The simple calculation (lines 25-26) is also not mentioned in the manuscript.
The introduction promises methane budget in the Northwest Passage but this is not calculated. At the beginning of the 1.2, none of the names (line 113) are shown on figure 1. The last paragraph details the different water masses and chemistry, but only ranges of salinity are given. The authors should also indicate ranges for temperature, nutrient and oxygen saturations.
Material and methods: Transects are mentioned in the sampling procedures (2.1), but only one is visible on figure 1 (West of Navy Board Inlet).
Please explain in this section the difference between experimental and discrete samples for methane and why you do this distinction. Why not presenting methane concentrations in seawater in table S1 like shown for sea ice in table S2? Table S1 shows 76 in situ samples, and 27 experimental. Where is the 56 number coming from in table S1? 18 seawater samples were collected for microbial community but only 9 samples are presented in figure 12. Please explain.
The link for Uhlig and Loose 2017 directs towards their data repository in PANGAEA instead of their publication. The manuscript contained several instances of plagiarism from Uhlig and Loose 2017 and Uhlig et al. 2018. The only differences for chemical and biological analyses are the names given to the variables and the in-depth of the analysis. The authors should explain their choice of using αox of 1.007 as a lower bounds when Uhlig and Loose states that this value overestimates the oxidation. Moreover, the correlation using this value is not very convincing. Because the submitted manuscript is primarily a repetition Uhlig’s work, references and brief summary of the majority of the material and method would probably suffice.
The section “Estimating the oxidation rates from mass balance and isotopic fractionation” is unclear (explanation of kox.delta). 28 degrees is not the threshold between warm and cold environments, the authors mean 1 degrees as also mentioned in Uhlig and Loose 2017.
Water mass detection: please give the range for all markers, not only for δ18O.
Results: The authors only show the methane concentration and isotopic signature for one profile at Croker Bay, and figure 6 is the only figure showing all these without giving the location or depth. A general figure showing all data with regard to the longitude would be helpful and might give more indication on the spatial variation. Figure 7 only shows kox average between all profiles. The authors should add all data in this graph (may be instead of table 2), including the average by using a different thickness of line for example. I have the same comment regarding the ice cores, where only 1 and 2 are shown in figure 8. The authors indicate a methane maxima at Westernmost Station of 24nM, but the figure shows a value closer to 21nM. Finally, the summary of the ice core section (isotopic signature in ice cores was between -52 and -33 ‰) is inconsistent with the text and figure 8.
Discussion: Please explain the statement line 561-562 and rephrase the sentence that follows. Table 2 presents kox and rox, and the stations influenced by PW only present shallow water. Please explain how this might influence the conclusions. The authors state that higher microbial oxidation rates correspond to higher methane concentrations from Figure 9 which shows an extremely low (0.03) correlation coefficient, even if the data measured in CB influence the trend. Could this low value be due to the lower bound chosen for αox? There is no labels over the dots in figure 9 as indicated in the caption. The Michaelis-Menten kinetics plot is supposed to confirm that high methane concentrations are associated to low kox, but this is not obvious in the figure. The low methane oxidation rates in ice covered sites is not shown in figure 13.
The authors present the influence of SIM and MW on methane concentration and isotopic signature (figure 11), but the comparison with PW and AW is in the appendix. The authors should present all results in a figure with different panels. They also refer to distribution of methane across the study area from figure 12, but this figure shows kox and not CH4.
Specific comments:
Line 88: typo (inasmuch)
Line 92: define CAA (has only been defined in the abstract)
Line 297: where is the linear correlation of 0.52 coming from? The caption in figure 2 indicates 0.2564.
Line 206-207: “We also tried to identify the outliers through other procedures”: this doesn’t say much.
Line 392: define SA as Absolute salinity
Line 426: where is this number coming from?
Line 435: T and S are used for the first time. Please define.
Line 480: remove
Line 611: inconsistency of the average kox stated here and table 2.
Line 661: Figure 7 and table 2, not figure 10.
Figure 10: The font in the inlet figure is too small, typo in the caption (Forland and not Forlan)Citation: https://doi.org/10.5194/egusphere-2023-74-RC1 -
AC1: 'Reply on RC1', Alessandra D'Angelo, 18 Mar 2023
Dear Referee 1, thanks for the comments. We appreciate the time and effort that you and the reviewers dedicated to providing constructice feedback on our manuscript. Your insightful comments suggested valuable improvements to our paper. Below you can find our replies (Author Comment - AC).
The overall story is not very convincing with many inconsistencies when comparing numbers in the text and figures or tables, and sometimes figures not correctly sited. New information is also mentioned in the discussion or the conclusion with no support from figures or tables (e.g. lines 691, 722, 769, 779).
AC: The numbers in the text are averaged values, while the numbers in the tables show the individual values. Thank you for pointing this out, we will report the maximum in the averages, rather than reporting the maximum from the individual samples, to be consistent with the figures. If the readers want to explore the methane data, they can download the source data from the Arctic Data Center (https://doi.org/10.18739/A2BN9X45M); whereas the table with the Spearman’s correlation will be added in the supplemental material.
The nutrients results are not presented until the conclusion. Moreover, many instances of plagiarism from Uhlig’s work should be avoided by referring to their papers. I have several issues throughout the text as presented below.
AC: Nutrients results are shown in 3.1 and mentioned in 4.2 prior conclusions. We have followed the method that Uhlig and Loose and Uhlig et al. describe, and we have endeavored to strike a balance between citing that work and reproducing key equations here, in order to make it easy for the reader to follow the method. We take the reviewers critique that this reads like some material has been copied verbatim and we will revise the methods to avoid that.
The abstract presents some information from a rejected companion manuscript (D’Angelo et al., 2022, https://doi.org/10.5194/essd-2022-306) and this information is not mentioned in the rest of the manuscript (e.g. chl. A correlation with meteoric waters and methane concentration in the abstract).
AC: The reference to the rejected manuscript referred to a “preprint” DOI (lines 206, 402), while the sentence that the reviewer is highlighting refers to the DOI of the published dataset (see lines 648 and 653). We will remove references to the ESSD manuscript that is in the process of resubmission, and simply cite the dataset DOI.
The simple calculation (lines 25-26) is also not mentioned in the manuscript.
AC: A description will be added.
The introduction promises methane budget in the Northwest Passage but this is not calculated.
AC: True, the term “budget” is misleading. We will refer to “quantifying oxidation” as one important term in the methane budget.
At the beginning of the 1.2, none of the names (line 113) are shown on figure 1.
AC: The locations will be added on the map.
The last paragraph details the different water masses and chemistry, but only ranges of salinity are given. The authors should also indicate ranges for temperature, nutrient and oxygen saturations.
AC: Values of temperature, nutrient and oxygen saturations will be added from literature.
Material and methods: Transects are mentioned in the sampling procedures (2.1), but only one is visible on figure 1 (West of Navy Board Inlet).
AC: In Fig.1, we showed only the stations where methane was investigated.
Please explain in this section the difference between experimental and discrete samples for methane and why you do this distinction. Why not presenting methane concentrations in seawater in table S1 like shown for sea ice in table S2?
AC: A clarification about why we implemented different treatments for in-situ and in-vitro samples will be added in the text. The seawater methane data are shown in the Arctic Data Center (https://doi.org/10.18739/A2BN9X45M), cited in the text.
Table S1 shows 76 in situ samples, and 27 experimental. Where is the 56 number coming from in table S1?
AC: We collected duplicated samples for the incubations in order to have a better reproducibility; hence, the samples were 56 (28x2) in total. One sample was leaking, so we took it off (27x2). We acknowledge that the text lacks information and we will add it.
18 seawater samples were collected for microbial community but only 9 samples are presented in figure 12. Please explain.
AC: Same as before. In the plot we show the averaged samples of the replicates (9x2), as explained in the caption.
The link for Uhlig and Loose 2017 directs towards their data repository in PANGAEA instead of their publication.
AC: Thanks for noticing it, it will be fixed.
The manuscript contained several instances of plagiarism from Uhlig and Loose 2017 and Uhlig et al. 2018. The only differences for chemical and biological analyses are the names given to the variables and the in-depth of the analysis.
AC: As aforementioned, we have followed the method that Uhlig and Loose and Uhlig et al. describe, and we have endeavored to strike a balance between citing that work and reproducing key equations here, to make it easy for the reader to follow the method. We take the reviewers critique that this reads like some material has been copied verbatim and we will revise the methods to avoid that.
The authors should explain their choice of using αox of 1.007 as a lower bounds when Uhlig and Loose states that this value overestimates the oxidation. Moreover, the correlation using this value is not very convincing. Because the submitted manuscript is primarily a repetition Uhlig’s work, references and brief summary of the majority of the material and method would probably suffice.
AC: We are sorry, in the text is reported the wrong information. Based on values that matched with the mass balance oxidation rate constant (kox.mass.balance), we decided to use the αox = 1.025 for our estimation of kox.isotope.ratio. We’d like to thank the referee for bringing up this concern and we will certainly update the text in the revised manuscript.
The section “Estimating the oxidation rates from mass balance and isotopic fractionation” is unclear (explanation of kox.delta).
AC: In this section, we described the procedure for calculating the methane oxidation rate constants. We followed published methods; hence we will remove the redundant text and cite the existing literature.
28 degrees is not the threshold between warm and cold environments, the authors mean 1 degrees as also mentioned in Uhlig and Loose 2017.
AC: This was a typo, it was 2⁰C, as in Uhlig and Loose (2017).
Water mass detection: please give the range for all markers, not only for δ18O.
AC: The endmembers for the multivariate analysis will be all collected in a table.
Results: The authors only show the methane concentration and isotopic signature for one profile at Croker Bay
AC: All of the methane concentration data is shown as saturation anomalies in Figure 4. We decided to show only one site for a visual purpose. The choice of Croker Bay was motivated by the highest methane concentration coupled to the lowest isotopic signature. To fill out the picture of in-situ methane concentrations, we will add all station profiles to a multi-panel figure in Supplemental material.
figure 6 is the only figure showing all these without giving the location or depth. A general figure showing all data with regard to the longitude would be helpful and might give more indication on the spatial variation.
AC: Figure 4 also shows all the methane concentrations expressed as saturation anomalies. It is challenging to depict the spatial variations in Lat/Lon/Depth in one figure, so we have attempted to make other depictions. Figure 6 had the purpose of providing information about the general trend of the in-situ methane samples. The aim of plotting the data using a color scale showing the seawater absolute salinity was to highlight the influence of the freshwater on the methane cycle. Nevertheless, we will add a plot showing all the profiles of methane concentration and isotope ratio by station in the supplemental material.
Figure 7 only shows kox average between all profiles. The authors should add all data in this graph (may be instead of table 2), including the average by using a different thickness of line for example.
AC: Figure 7 and Table 2 show averages between the duplicate in-vitro samples. If the reader wants to examine the values of the duplicates, they can download the source data from the Arctic Data Center. We don't have profiles of methane oxidation at each station and can only assemble a profile by providing oxidation rates from all the stations.
I have the same comment regarding the ice cores, where only 1 and 2 are shown in figure 8.
AC: We usually prefer to show few panels per figure in the manuscript, for a better visualization. We can certainly add all cores data in the supplemental material.
The authors indicate a methane maxima at Westernmost Station of 24nM, but the figure shows a value closer to 21nM.
AC: Thank you for pointing this out, we will report the maximum in the averages, rather than reporting the maximum from the individual samples, to be consistent with the figure.
Finally, the summary of the ice core section (isotopic signature in ice cores was between -52 and -33 ‰) is inconsistent with the text and figure 8.
AC: In the summary we showed the range of the values, while in the text and figure we showed the averaged values. We will make sure that a revised manuscript uses values that are consistent with the figures, to reinforce these points, and avoid creating confusion. We will do this in the text related to Figure 8 and throughout the manuscript.
Discussion: Please explain the statement line 561-562 and rephrase the sentence that follows. Table 2 presents kox and rox, and the stations influenced by PW only present shallow water. Please explain how this might influence the conclusions.
AC: We acknowledge that the sentence is incomplete as written, and we will revise the manuscript with “Pacific Water (PW) was present at fractions greater than 50% in the waters above 200 m, which also coincided with the regions of high methane oxidation. Moreover, in samples collected from deeper layers we recorded lower oxidation rates, suggesting that the AW-origin layers did not support present methane microbial metabolism.”. This will also answer the second comment.
The authors state that higher microbial oxidation rates correspond to higher methane concentrations from Figure 9 which shows an extremely low (0.03) correlation coefficient, even if the data measured in CB influence the trend. Could this low value be due to the lower bound chosen for αox?
AC: We chose the αox upper bound for calculating the kox.isotope.ratio, and this decreased the order of magnitude of the averaged kox.Yes, the choice of the fractionation coefficient influences the magnitude of the oxidation rate constant, that is the reason why it is important to observe both isotope ratio and mass balance oxidation rate constants. In this study, the kox.isotope.ratio data were consistent with the mass balance data (kox.mass.balance), as shown in Figure 2.
There is no labels over the dots in figure 9 as indicated in the caption.
AC: This will be fixed.
The Michaelis-Menten kinetics plot is supposed to confirm that high methane concentrations are associated to low kox, but this is not obvious in the figure.
AC: The aim of this plot is to show the reaction velocity as a function of substrate concentration. However, we acknowledge that the little amount of data does not highlight the outcome, hence we will remove Figure 10 and qualitatively discuss the Michaelis-Menten kinetics related to the Figure 9.
The low methane oxidation rates in ice covered sites is not shown in figure 13.
AC: The color scale shows the methane oxidation rate constant, and the light green indicates the lower values. We can work on making it clearer for the reader.
The authors present the influence of SIM and MW on methane concentration and isotopic signature (figure 11), but the comparison with PW and AW is in the appendix. The authors should present all results in a figure with different panels.
AC: For a better visualization we did not show all the data, but we can add it as suggested.
They also refer to distribution of methane across the study area from figure 12, but this figure shows kox and not CH4.
AC: It will be fixed.
Line 611: inconsistency of the average kox stated here and table 2.
AC: In Table 2 we showed all the values of the averaged methane oxidation rate constant (kox.av), including the 0s. In the calculation for the average, we only took into account the values of kox.av >0 (suggesting methane oxidation). We recognize that this information was missing in the text, and we will add it.
Line 88: typo (inasmuch)
AC: We will fix it.
Line 92: define CAA (has only been defined in the abstract)
AC: We will fix it.
Line 297: where is the linear correlation of 0.52 coming from? The caption in figure 2 indicates 0.2564.
AC: We will add the Spearman’s correlation and linear regression information in the supplemental material.
Line 206-207: “We also tried to identify the outliers through other procedures”: this doesn’t say much.
AC: More details will be added.
Line 392: define SA as Absolute salinity
AC: We will fix it.
Line 426: where is this number coming from?
AC: More details will be added.
Line 435: T and S are used for the first time. Please define.
AC: We will fix it.
Line 480: remove
AC: We will fix it.
Line 661: Figure 7 and table 2, not figure 10.
AC: We will fix it.
Figure 10: The font in the inlet figure is too small, typo in the caption (Forland and not Forlan)
AC: We will fix it.
Citation: https://doi.org/10.5194/egusphere-2023-74-AC1
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AC1: 'Reply on RC1', Alessandra D'Angelo, 18 Mar 2023
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RC2: 'Comment on egusphere-2023-74', Anonymous Referee #2, 07 Mar 2023
The study of D’Angelo et al. describes the methane concentrations and oxidation rates in Canadian Arctic Sea. This is certainly a valuable data set and area with few investigations. However, the study is rather lengthy and confusing. The result section is presented in messy way. The aspects of the discussion are not supported by the result section.
Please see my comments below and additional remarks in the text.
L 232 ff: The Method for MOX used is not the standard one, i.e. 3H or 14C tracer, a direct comparison of the method would be useful
If this method is published the respective section should be shortened and moved to the Supplements
The explanation of the method should be more to the point, and stress the important aspects, such as what are the effects of the long incubation time, and what is the limit of detection?
L 356 ff: DNA extraction: why was the extraction performed after the experiments? This is not the in-situ community!!
Figure 3: This graph is rather unconventional; I would prefer to show the longitude on the x-axis and color code the concentrations…. This would make your message much clearer
Figure 4: as in figure 3, it would be clearer to have the geographic settings, depth and longitude on the x/y axis and the variable with color coding
Figure 6: is this a significant relationship? what is the value of p? Would it be better to use the logarithmic values? Especially at the low values, I doubt that there is a significant correlation....
figure 5: Methane in situ =? Why do not you name it methane concentration, better wording, Keep it simple, if you are talking about MOX, just name it methane oxidation rate or MOS, the details of determination are already given in MM section
L 474 ff: A bit more text on the results of the MOX, where are why the highest / lowest rates? As it is an important factor of this work, the describing text is very meagre
L 502 ff: Community structure: Did you detect no known methanotrophs at all?? Even after such long incubations and MOX activity? Is it known if the detected species have the genes for methane oxidation? Could this be an incubation artifact, any comparison with water without any incubations? There is no known relation between Flavobacteria and methane oxidation, thus it seems to me, that you just did not detect any MOBs, but I do not understand the connection between MOX and these other bacterial groups….
Sea ice: Was there are difference in methane concentration between multi-year and first-year ice, please clarify! A figure with both methane concentrations in the sea water and ice cores would be helpful… If you state a difference in variability in the isotopic composition of sea ice and water, please give the exact numbers for the variability, and what for is this information needed?
Discussion:
Already the first introduction sentence is not supported by the result section.
Also, the discussion on Figure 9 is not supported by data from the results, also statistics on this figure are not convincing.
The discussion on the kinetics of methane oxidation is completely confusing and without any profoundness on the subject.
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AC2: 'Reply on RC2', Alessandra D'Angelo, 18 Mar 2023
Dear Referee 2, thanks for the comments. We appreciate the time and effort that you and the reviewers dedicated to providing constructice feedback on our manuscript. Your insightful comments suggested valuable improvements to our paper. Below you can find our replies (Author Comment - AC).
The study of D’Angelo et al. describes the methane concentrations and oxidation rates in Canadian Arctic Sea. This is certainly a valuable data set and area with few investigations. However, the study is rather lengthy and confusing. The result section is presented in messy way. The aspects of the discussion are not supported by the result section.
Please see my comments below and additional remarks in the text.
L 232 ff: The Method for MOX used is not the standard one, i.e. 3H or 14C tracer, a direct comparison of the method would be useful
AC: To date, there is no direct comparison between the two methods. The use of stable isotopes has recently been developed from Chan et al. (2016) and Leonte et al. (2017). Here, they used stable isotopes to measure methane oxidation rates in in-vitro seawater. It would be beneficial to assess the difference in methodologies and how these differ in their approach and their rate estimates, but this would require a separate study.
If this method is published the respective section should be shortened and moved to the Supplements.
AC: The method section will be shortened. We followed published methodologies; hence we will remove the redundant text and cite the existing literature.
The explanation of the method should be more to the point, and stress the important aspects, such as what are the effects of the long incubation time, and what is the limit of detection?
AC: The section on the methods will be revised in order to better highlight the most important aspects.
L 356 ff: DNA extraction: why was the extraction performed after the experiments? This is not the in-situ community!!
AC: The in-situ community was analyzed in parallel with the in-vitro samples. Hence, we had both community data at “time zero” and at “time final” of the experiments. We acknowledge this was unclear in the text, and we apologize for this. We will describe it better in the revised version of the manuscript.
Figure 3: This graph is rather unconventional; I would prefer to show the longitude on the x-axis and color code the concentrations…. This would make your message much clearer. Figure 4: as in figure 3, it would be clearer to have the geographic settings, depth and longitude on the x/y axis and the variable with color coding.
AC: Thanks for the suggestions. We will redo the figures as recommended.
Figure 6: is this a significant relationship? what is the value of p? Would it be better to use the logarithmic values? Especially at the low values, I doubt that there is a significant correlation....
AC: Figure 6 shows the relationship between the in-situ methane concentrations and isotopic ratio. This figure suggests that the water column likely experienced methane microbial oxidation in the past. We used this figure as a simplified version of the Fenwick et al. (2017) Figure 14 (https://agupubs.onlinelibrary.wiley.com/doi/full/10.1002/2016JC012493). We followed the referee suggestion and plotted the [CH4] values on logarithmic scale (supplement 1). The R2 and p-value did not improve much, but for the purpose of the figure this is not a concern.
figure 5: Methane in situ =? Why do not you name it methane concentration, better wording, Keep it simple, if you are talking about MOX, just name it methane oxidation rate or MOS, the details of determination are already given in MM section
AC: We will re-name the terms in order to make the text clearer. Methane in-situ data include both concentrations and isotope ratio, hence we endeavored to use a clear and correct terminology.
L 474 ff: A bit more text on the results of the MOX, where are why the highest / lowest rates? As it is an important factor of this work, the describing text is very meagre
AC: We will work on implementing and enriching the text in the results section for the methane oxidation rates.
L 502 ff: Community structure: Did you detect no known methanotrophs at all?? Even after such long incubations and MOX activity? Is it known if the detected species have the genes for methane oxidation? Could this be an incubation artifact, any comparison with water without any incubations? There is no known relation between Flavobacteria and methane oxidation, thus it seems to me, that you just did not detect any MOBs, but I do not understand the connection between MOX and these other bacterial groups….
AC: The genomic analysis only showed the 25 most abundant taxa in our samples, and some of them were unclassified. It is likely that methanotrophs occurred in the samples, but we could not detect them. We did not identify known methane oxidizing taxa both in in-situ and in-vitro samples. Other studies (e.g., Redmond and Valentin, 2011; Jensen et al., 2008; Radajewski et al. 2002) suggested that Bacteroidetes Flavobacteria might be directly involved with methane uptake, as secondary consumer.
Sea ice: Was there are difference in methane concentration between multi-year and first-year ice, please clarify! A figure with both methane concentrations in the sea water and ice cores would be helpful… If you state a difference in variability in the isotopic composition of sea ice and water, please give the exact numbers for the variability, and what for is this information needed?
AC: There was no trend of methane concentrations from first-year to multi-year ice cores. We can add a figure with both methane concentrations in the sea water and sea ice in the supplementary material. In this study, we use the isotopic ratio of methane as tracer for supporting the methane concentration data. For confirming the methane oxidation, we rely on the consistency of both datasets. In the case of the isotopic ratio within the sea ice samples, we highlighted the differences between seawater and sea ice data, to support the hypothesis of methane oversaturation along the whole vertical profile of the sea ice (hence more homogeneous range of values, suggesting targeted inputs). We will provide the exact value of the variability in the text.
Discussion:
Already the first introduction sentence is not supported by the result section.
AC: The introductory section highlighted the main outcomes showed above in the result section (methane excess in shallow waters, highest oxidation rates in surface and Pacific-origin waters), but we take the referee critique and will write the section clearer, in order to reflect the above results.
Also, the discussion on Figure 9 is not supported by data from the results, also statistics on this figure are not convincing.
AC: In figure 9, we reported the averaged values of kox against the dissolved methane concentration. We showed this relationship to assess how the in-situ methane concentrations affect the methane oxidation rates and we linked this outcome to the above presented results of methane concentrations and oxidation rates (lines 582 – 584). We accept the reviewer’s critique that this did not connect well with previous results, and we will revise the paragraph according to the suggestion.
The discussion on the kinetics of methane oxidation is completely confusing and without any profoundness on the subject.
AC: We will improve this paragraph. We will remove Figure 10 and qualitatively discuss the Michaelis-Menten kinetics related to the Figure 9.
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AC2: 'Reply on RC2', Alessandra D'Angelo, 18 Mar 2023
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RC3: 'Comment on egusphere-2023-74', Anonymous Referee #3, 08 Mar 2023
The authors present a study that focuses on the methane budget in Arctic marine environment and the role of microbial metabolism in the water column and in sea ice driven by environmental factors such as nutrient supply, water mass movements, and input of fresh water. Samples for this study were collected during a two-week cruise in July/August 2019; the 17 investigated stations were located in the Parry Channel, Canadian Arctic Archipelago.
The data set of this study consists of depth profiles of CTD measurements, nutrient analyses, analysis of the bacterial community via 16S rRNA sequencing, microbial in-vitro incubations to evaluate methane consumption/production, and methane concentration measurements of seawater and sea ice and from the in-vitro incubations. This is a multi-faceted dataset from an area where there is only little research available.
Unfortunately, several paragraphs in the manuscript appear confused especially the results part where many outcomes are already discussed quite detailed.
Most confusing to me is the section about the microbial community composition. The authors identified Aurantivirga, Oleispira and Planctomarina as dominant bacteria in the in-vitro incubation and suggested these taxa as being the main methane oxidizers in the study area. It would be of interest, if any known MOB were found in the samples even if in small quantities. It is not clear to me for how long each samples was incubated – L261: “The time of the incubations varied between 7 and 25 days”. Further, authors state “The oxidation detection limit was passed between 5 and 18 incubation days after incubation began, revealing the range of rates we observed.” (L497). On which basis did authors decide to run one incubation longer than the other? Was the duration of the incubation experiment the same for all samples after they reached the detection limit? What was the total duration of the incubation experiment? How did you make sure that you actually can compare the rates among samples from different sites if incubation times differ that much? Another factor is that the community composition in an incubation changes over time, and if a sample for molecular analysis is only taken at the end of an experiment where incubation times differed over weeks (I assume from the information given), how will it be possible to make a valid estimate of microbial population in an sample and further transfer this assumption to the studied area? Why didn´t you sequence water and sea ice samples (before incubating them)?
The introduction is inconsistent. In L47, the authors promise to give and introduction to microbial metabolisms associated with methane in the marine environment. They start with describing the methane oxidizing taxa, but forgot to mention microbes associated to methanogensis. In the next paragraph, methanogenesis is subject, but only in context with environmental drivers. I would like to learn more about what is known about the community structure of methane producers in the ecosystem the study is focusing on. On the other hand, this information might become irrelevant when the molecular analysis doesn´t reveal any microbial taxa that are clearly associated with methanogensis or MOx.
In the last paragraph of the introduction, authors promise to “elucidate the methane budget in the NWP”, but the final calculation of the budget for the entire study area or at least for a transect is not part of the manuscript.
Generally, authors should be more consistent with word spelling (e.g. Western-most Station/ Westernmost Station) and abbreviations. In one paragraph the full site names are used, in the next paragraph only IDs. Same applies to the water masses throughout the manuscript. I recommend to use as little abbreviations as possible.
L46: Are there more recent studies available?
L49: I agree that MOx is an important sink for dissolved methane in the water column, but the phrase “over some depth ranges and at some locations” is a bit too simple. MOx is, wherever it happens, an important mechanism to remove CH4 from the environment. Please, be more precise and clarify what you mean with “over some depth ranges”! From shallow shelf to deep ocean can be a range of several 1000 meters. The same applies to the location. Do you mean “some locations” are more relevant for MOx activity than others? If so, why is that? Or are you referring to the limited studies focusing on MOx in the Arctic? Make that clear!
L61: Too much of a jump in topic – wonder what the environmental drivers for MOx are.
L85: Microbial community structure as measure for ecosystem states - add a reference! This sentence is a bit lost in the context, since the following paragraph is completely independent of the above-mentioned community structure.
L88: fix typo “inasmuch”
L102 - 109: No need to give an overview of the general structure of the manuscript. This paragraph can be deleted.
L114: Could you rephrase it to: “This Channel connects Baffin Bay to the east with the Beaufort Sea to the west.”?
Fig.1: Why are red dots numbered and yellow dots not?
L153: “The western part of the CAA is characterized by a more consistent sea-ice coverage” compared to?
The material and methods part is sometimes too details that makes the manuscript hard to read. Authors should think of either shorten it and refer to references if methods were published elsewhere already and/or moving some lengthily parts to the supplements.
L166: “samples were collected in the vicinity of Parry Channel” – were samples taken in the Parry Channel or only in the vicinity of (near to) the Channel. To me it makes a difference.
L176: “Sea ice charts were collected by the Canada ice center” - Why is this relevant?
L188: With “in-vitro methane incubations” do you mean the MOx rate measurements mentioned in L186? It is not clear to me where these samples were taken. Be consistent with wording throughout the text.
L191: the sterivex filters were removed from where? from the bags?
L200: it´s not relevant at which institution the measurements were done as long as instrument specifications are shown. If you want to give credit to an collaborating institution, do this in the acknowledgements.
L207: You tried to identify outliners through other procedures. Want to mention them?
L222: “For the calibration of the instrument, we used additional methane standards.” - this information is irrelevant if you don´t add the name of instrument that was used. I think, you do that at a later point, so this sentence can be removed.
L229: Again, what is meant by in-situ measurements? Methane concentration measurements? What are the experimental bags? The Incubation experiments? MOx rate measurements? Be consistent with wording used throughout the manuscript.
L275 and the following lines: check subscripts in the formulae and in the text and correct them.
L306: only give the final concentration of NaOH in your samples.
L349: “A third outcome of the incubations can be methane production.” This sounds weird, could you rephrase it?
L356: Why is there a reference? Are data published elsewhere? If you followed a method/protocol published by Uhlig, than make that clear.
L357: According to the paragraph in L188-194, samples for molecular analysis were collected via Sterivex filters. Here you are giving two different kits for DNA extraction. Which one was used – the MoBio or the Millipore? Did you follow the standard extraction protocol? If yes, then all lines after L359 starting with “without the need for enzymes or hazardous organic chemicals.” and including L368 can be removed. “Inhibitor Removal Technology® (IRT) was included to provide high-quality DNA from all types of water samples, even those containing heavy amounts of contaminants.” Was IRT part of the extraction kit? Or is it something you added to the extraction protocol? If IRT is a regular ingredient of the kit, it´s not worth mentioning it.
How was the sequence analysis and taxonomical classification done after receiving the sequencing reads? Which pipeline and reference database were used? On which platform are the raw data stored?
L370: Is the protocol for the library prep. not published elsewhere? If yes, please, give reference and consider to shorten this paragraph and move details into the SUPP.
L392: define SA and apply superscript to d18O
L419: Space missing
Fig.4: T and S define as temperature and salinity instead
Fig.6: It´s hard to distinguish between different green shades. Could you apply a better color scale?
The results part contains detailed discussion already e.g. L444, 457, 460, 496, 503….especially in 3.4., most of the results are already discussed (L503 and L511 – 524).
Tab.2: Could be moved to the SUPP, since data are shown in Fig.7. L480: apply subscript to kox, remove your personal note!
Fig.7: you could apply a longitude color scaling to this figure, too, to indicate sampling sites. Or add IDs.
L532: redundant information - already mentioned in L529.
L536: “in the proximity of the Westernmost station.” – could you give a better measure for distances and direction here, please?
L544: Add a measure for “thin first-year ice” like you did in L546. How thin was it?
Fig.8: This figure only shows results of core 1 and 2. Why are data from core 3,4, and 5 not shown? Were can I find those profile data? (BTW it´s not obverse at the first sight that this data belong to core 1 and 2 – I suggest to change the heading of each plot from just “1” and “2” to “Core 1” and “Core 2”).
L562: “Here, we also recorded higher methane microbial oxidation rates, likely associated with Pacific-origin microbes and with the seasonal biology.” - I don´t understand where this assumption comes from.
L569: Only two references here? this suggests that there are only two studies available!, but it´s not true, there are more than only two studies of MOx in Arctic marine environments that are worth mentioning here.
L576: Again, only two references for a general statement – add “e.g.” in front of the references mentioned and use references which give the best example for underlining your statement.
Fig.9: 592: brackets missing, L594: can´t find any labels above dots in the figure.
L601: define DWH.
Fig.10: It´s called Prins Karls Forland (L633). What does NPP mean?
L652: What is MW and SIM? Define it. It gets too confusing with water mass and site ID abbreviations.
L669: What´s data CB?
L670: Check the display of your references! This applies to the entire manuscript!
Fig.11: What are MP results?
L706: What is meant by “weak methane metabolism”? Better give ranges that indicate “weak” and “stronger” activities.
L715: “the greatest sea ice cover” compared to?
Fig.13: Add abbreviation (SIC) behind “sea ice concentrations”. What does “Kox averaged by CTD” mean? Is it the average value of all depth profile measurements at one site?
L763: Add references that show that Aurantivirga are associated with sediments.
L767: Is there any study that confirms that Chloroplast sequences from V4-V5 region were used for environmental prediction of bloom scenarios?
L792 – 797: This statement was concluded in the previous sentences, no need to summarize it again.
It is not necessary to mention the name of the research vessel every time when something is done onboard.
Citation: https://doi.org/10.5194/egusphere-2023-74-RC3 -
AC3: 'Reply on RC3', Alessandra D'Angelo, 18 Mar 2023
Dear Referee 3, thanks for the comments. We appreciate the time and effort that you and the reviewers dedicated to providing constructice feedback on our manuscript. Your insightful comments suggested valuable improvements to our paper. Below you can find our replies (Author Comment - AC).
The authors present a study that focuses on the methane budget in Arctic marine environment and the role of microbial metabolism in the water column and in sea ice driven by environmental factors such as nutrient supply, water mass movements, and input of fresh water. Samples for this study were collected during a two-week cruise in July/August 2019; the 17 investigated stations were located in the Parry Channel, Canadian Arctic Archipelago.
The data set of this study consists of depth profiles of CTD measurements, nutrient analyses, analysis of the bacterial community via 16S rRNA sequencing, microbial in-vitro incubations to evaluate methane consumption/production, and methane concentration measurements of seawater and sea ice and from the in-vitro incubations. This is a multi-faceted dataset from an area where there is only little research available.
Unfortunately, several paragraphs in the manuscript appear confused especially the results part where many outcomes are already discussed quite detailed.
Most confusing to me is the section about the microbial community composition. The authors identified Aurantivirga, Oleispira and Planctomarina as dominant bacteria in the in-vitro incubation and suggested these taxa as being the main methane oxidizers in the study area. It would be of interest, if any known MOB were found in the samples even if in small quantities. It is not clear to me for how long each samples was incubated – L261: “The time of the incubations varied between 7 and 25 days”. Further, authors state “The oxidation detection limit was passed between 5 and 18 incubation days after incubation began, revealing the range of rates we observed.” (L497).
AC: Thanks for bringing this up, we will add a table with all the information in the supplementary material.
On which basis did authors decide to run one incubation longer than the other? Was the duration of the incubation experiment the same for all samples after they reached the detection limit? What was the total duration of the incubation experiment? How did you make sure that you actually can compare the rates among samples from different sites if incubation times differ that much?
AC: The duration of the incubation is driven by the logistical constraints. Because the stable isotope and mass balance method is less sensitive to changes in methane, the incubation time needs to be longer than the radioisotope method. Samples collected at the early part of the cruise had longer time to incubate, whereas samples at the end had a shorter time. Post-cruise, we extended the incubation times by continuing our analysis at a lab in Thule airbase (Greenland). However, this period could not be extended beyond 10 days. Given the incubation time, the smallest oxidation rates will not be resolvable, but we can determine what the lower limit is using the uncertainty, and this has been reported, as it was in Uhlig and Loose (2017).
Another factor is that the community composition in an incubation changes over time, and if a sample for molecular analysis is only taken at the end of an experiment where incubation times differed over weeks (I assume from the information given), how will it be possible to make a valid estimate of microbial population in an sample and further transfer this assumption to the studied area? Why didn´t you sequence water and sea ice samples (before incubating them)?
AC - As RC2: The in-situ community was analyzed in parallel with the in-vitro samples. Hence, we had both data at “time zero” and at “time final” of the incubations. We acknowledge this was unclear in the text, and we will work to clarify the potential for divergence between the two communities. Likewise, we refer to the methane oxidation measurements as ‘potential methane oxidation’ as described in Uhlig and Loose (2017) to reflect that the addition of methane and the incubation time can lead to a change in microbial community composition.
The introduction is inconsistent. In L47, the authors promise to give and introduction to microbial metabolisms associated with methane in the marine environment. They start with describing the methane oxidizing taxa, but forgot to mention microbes associated to methanogenesis. In the next paragraph, methanogenesis is subject, but only in context with environmental drivers. I would like to learn more about what is known about the community structure of methane producers in the ecosystem the study is focusing on. On the other hand, this information might become irrelevant when the molecular analysis doesn´t reveal any microbial taxa that are clearly associated with methanogensis or MOx.
AC: We acknowledge that the introduction diverges somewhat from the eventual results and discussion, and we will endeavor to provide the most relevant background.
In the last paragraph of the introduction, authors promise to “elucidate the methane budget in the NWP”, but the final calculation of the budget for the entire study area or at least for a transect is not part of the manuscript.
AC – as RC1: True, the term “budget” is misleading. We will refer to “quantifying oxidation” as one important term in the methane budget.
Generally, authors should be more consistent with word spelling (e.g. Western-most Station/ Westernmost Station) and abbreviations. In one paragraph the full site names are used, in the next paragraph only IDs. Same applies to the water masses throughout the manuscript. I recommend to use as little abbreviations as possible.
AC: Thanks for this advice. We will be more accurate in the terminology.
L46: Are there more recent studies available?
AC: Yes. For example, Steinle et al. (2015), and Shakhova et al. (2013). We will add them in the text.
L49: I agree that MOx is an important sink for dissolved methane in the water column, but the phrase “over some depth ranges and at some locations” is a bit too simple. MOx is, wherever it happens, an important mechanism to remove CH4 from the environment. Please, be more precise and clarify what you mean with “over some depth ranges”! From shallow shelf to deep ocean can be a range of several 1000 meters. The same applies to the location. Do you mean “some locations” are more relevant for MOx activity than others? If so, why is that? Or are you referring to the limited studies focusing on MOx in the Arctic? Make that clear!
AC: We will rephrase it to make the concept clearer. The sentence referred to the Arctic region, where we have hotspots for methane sink and hotspots for methane source.
L61: Too much of a jump in topic – wonder what the environmental drivers for MOx are.
AC: We will work on making the introduction clearer; we will avoid writing about methane production as not reported in this study.
L85: Microbial community structure as measure for ecosystem states - add a reference! This sentence is a bit lost in the context, since the following paragraph is completely independent of the above-mentioned community structure.
AC: We agree with this comment. The text will be edited.
L88: fix typo “inasmuch”
AC – as RC1: This will be fixed.
L102 - 109: No need to give an overview of the general structure of the manuscript. This paragraph can be deleted.
AC: The paragraph will be removed as suggested.
L114: Could you rephrase it to: “This Channel connects Baffin Bay to the east with the Beaufort Sea to the west.”?
AC: Thanks for the suggestion. We will edit it accordingly.
Fig.1: Why are red dots numbered and yellow dots not?
AC: The red dots showed the ice cores which were named by numbers, whereas the yellow dots showed the seawater samples, which were named by location and sample ID. We will add the CTD station ID on top of the yellow dots to be consistent with the sea ice samples.
L153: “The western part of the CAA is characterized by a more consistent sea-ice coverage” compared to?
AC: We will complete the sentence with “… compared to the eastern side”.
The material and methods part is sometimes too details that makes the manuscript hard to read. Authors should think of either shorten it and refer to references if methods were published elsewhere already and/or moving some lengthily parts to the supplements.
AC – as all referees: The method section will be shortened. We followed published methodologies; hence we will remove the redundant text and cite the existing literature.
L166: “samples were collected in the vicinity of Parry Channel” – were samples taken in the Parry Channel or only in the vicinity of (near to) the Channel. To me it makes a difference.
AC: The samples were taken within Parry Channel, but we also included Jones Sound samples, so it was more accurate to write “in the vicinity of”. We will describe the site locations better in the text.
L176: “Sea ice charts were collected by the Canada ice center” - Why is this relevant?
AC: We used the Canadian Ice Center data to observe the sea ice coverage over time. We can explain this better in the text.
L188: With “in-vitro methane incubations” do you mean the MOx rate measurements mentioned in L186? It is not clear to me where these samples were taken. Be consistent with wording throughout the text.
AC: Correct. We were sampling in parallel: dissolved methane (in-situ), and in-vitro methane (for assessing the methane microbial oxidation rate). We will be more specific in the text and define these terms earlier on in the manuscript.
L191: the sterivex filters were removed from where? from the bags?
AC: The water was drawn from the sterivex filter to transfer DNA onto it. We will be more descriptive in the text.
L200: it´s not relevant at which institution the measurements were done as long as instrument specifications are shown. If you want to give credit to an collaborating institution, do this in the acknowledgements.
AC: We will remove those lines and add them in the acknowledgements.
L207: You tried to identify outliners through other procedures. Want to mention them?
AC – as RC1: Details will be added.
L222: “For the calibration of the instrument, we used additional methane standards.” - this information is irrelevant if you don´t add the name of instrument that was used. I think, you do that at a later point, so this sentence can be removed.
AC: The sentence will be removed.
L229: Again, what is meant by in-situ measurements? Methane concentration measurements? What are the experimental bags? The Incubation experiments? MOx rate measurements? Be consistent with wording used throughout the manuscript.
AC: As aforementioned, we will be more specific in the text.
L275 and the following lines: check subscripts in the formulae and in the text and correct them.
AC: We will do it.
L306: only give the final concentration of NaOH in your samples.
AC: We will do it.
L349: “A third outcome of the incubations can be methane production.” This sounds weird, could you rephrase it?
AC: The sentence will be rephrased.
L356: Why is there a reference? Are data published elsewhere? If you followed a method/protocol published by Uhlig, than make that clear.
AC: Yes, we followed an existing method. We will be clearer in the text.
L357: According to the paragraph in L188-194, samples for molecular analysis were collected via Sterivex filters. Here you are giving two different kits for DNA extraction. Which one was used – the MoBio or the Millipore?
AC: Millipore is the brand of the filters (Line 190), while Qiagen is the brand of the extraction kit (Line 193). Line 357 erroneously refers to MoBio, because MoBio was bought out by Qiagen recently and some material still have the “MoBio” logo on it. We apologize for the confusion.
Did you follow the standard extraction protocol? If yes, then all lines after L359 starting with “without the need for enzymes or hazardous organic chemicals.” and including L368 can be removed. “Inhibitor Removal Technology® (IRT) was included to provide high-quality DNA from all types of water samples, even those containing heavy amounts of contaminants.” Was IRT part of the extraction kit? Or is it something you added to the extraction protocol? If IRT is a regular ingredient of the kit, it´s not worth mentioning it.
AC: For IRT yes, all the technology is included in the kit. We will remove the redundant part.
How was the sequence analysis and taxonomical classification done after receiving the sequencing reads? Which pipeline and reference database were used? On which platform are the raw data stored?
AC: The data were stored at National Center for Biotechnology Information (NCBI BioProject PRJNA718862). We will ensure that this information will be included in the methods with proper data source attribution in acknowledgements or open data statement.
L370: Is the protocol for the library prep. not published elsewhere? If yes, please, give reference and consider to shorten this paragraph and move details into the SUPP.
AC: The protocol was published last year in Kerrigan and D’Hondt (2022). We will refer to it and shorten the paragraph.
L392: define SA and apply superscript to d18O
AC: We will do it.
L419: Space missing
AC: We will fix it.
Fig.4: T and S define as temperature and salinity instead
AC – as RC1: We will do it.
Fig.6: It´s hard to distinguish between different green shades. Could you apply a better color scale?
AC: We will do it.
The results part contains detailed discussion already e.g. L444, 457, 460, 496, 503….especially in 3.4., most of the results are already discussed (L503 and L511 – 524).
AC: We will work on better discriminate between the results and the discussion.
Tab.2: Could be moved to the SUPP, since data are shown in Fig.7. L480: apply subscript to kox, remove your personal note! Fig.7: you could apply a longitude color scaling to this figure, too, to indicate sampling sites. Or add IDs.
AC – Table 2 will be moved to Supplemental material and Figure 7 will be re-edited with a color scale showing the longitude, as suggested.
L532: redundant information - already mentioned in L529.
AC: The sentence will be removed.
L536: “in the proximity of the Westernmost station.” – could you give a better measure for distances and direction here, please?
AC: We will do it.
L544: Add a measure for “thin first-year ice” like you did in L546. How thin was it?
AC: We will do it.
Fig.8: This figure only shows results of core 1 and 2. Why are data from core 3,4, and 5 not shown? Were can I find those profile data? (BTW it´s not obverse at the first sight that this data belong to core 1 and 2 – I suggest to change the heading of each plot from just “1” and “2” to “Core 1” and “Core 2”).
AC – as RC1: We usually prefer to show a few panels per figure in the manuscript, for a better visualization. We can certainly add all cores data in the supplemental material. We will edit the headers to make them clearer.
L562: “Here, we also recorded higher methane microbial oxidation rates, likely associated with Pacific-origin microbes and with the seasonal biology.” - I don´t understand where this assumption comes from.
AC – as RC1: The sentence will be revised.
L569: Only two references here? this suggests that there are only two studies available!, but it´s not true, there are more than only two studies of MOx in Arctic marine environments that are worth mentioning here. L576: Again, only two references for a general statement – add “e.g.” in front of the references mentioned and use references which give the best example for underlining your statement.
AC: We apologize, we forgot to add “e.g.,”.
Fig.9: 592: brackets missing, L594: can´t find any labels above dots in the figure.
AC – as all referees: The figure will be edited.
L601: define DWH.
AC: We will do it.
Fig.10: It´s called Prins Karls Forland (L633). What does NPP mean?
AC: Northwest Passage Project, we will add the full name.
L652: What is MW and SIM? Define it. It gets too confusing with water mass and site ID abbreviations.
AC: Meteoric water and sea ice meltwater. We will avoid using abbreviation to make it clearer for the reader. Thanks for the advice.
L669: What´s data CB?
AC: We missed the term “from” Croker Bay.
L670: Check the display of your references! This applies to the entire manuscript!
AC: We will do it.
Fig.11: What are MP results?
AC: Multiparameter analysis (MP). We will add it.
L706: What is meant by “weak methane metabolism”? Better give ranges that indicate “weak” and “stronger” activities.
AC: We will do it.
L715: “the greatest sea ice cover” compared to?
AC: Compared to East.
Fig.13: Add abbreviation (SIC) behind “sea ice concentrations”. What does “Kox averaged by CTD” mean? Is it the average value of all depth profile measurements at one site?
AC: Correct.
L763: Add references that show that Aurantivirga are associated with sediments.
AC: We will do it.
L767: Is there any study that confirms that Chloroplast sequences from V4-V5 region were used for environmental prediction of bloom scenarios?
AC: We are not aware of any published studies confirming this; however, we know that there are some works looking at chloroplasts from 16S data. We will correct line 766 in order to avoid any confusion.
L792 – 797: This statement was concluded in the previous sentences, no need to summarize it again.
AC: Thanks for the suggestion, we will remove it.
It is not necessary to mention the name of the research vessel every time when something is done onboard.
AC: We will remove the name when superfluous.
Citation: https://doi.org/10.5194/egusphere-2023-74-AC3
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AC3: 'Reply on RC3', Alessandra D'Angelo, 18 Mar 2023
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RC4: 'Comment on egusphere-2023-74', Anonymous Referee #4, 17 Mar 2023
The study presents a dataset including seawater salinity, nutrients, methane concentration and isotopic ratios in seawater and ice, and calculations of methane oxidation rates and constants. The nutrient data are not discussed in the context of the other data. Announced as thermohaline data in the abstract, I missed temperature data and found the usage of the salinity data disappointing.
The authors argue for higher methane oxidation in surface water than in deeper waters, based on rate measurements. However comparing the isotopic ratios coupled to the “in situ” concentrations reveals a pattern in contradiction to this statement. The low concentration paired with 13C-enriched ratios in “deeper waters” refers rather to methane oxidation therein than in “surface waters” where higher concentrations are paired with 13C-depleted ratios (compared to each other).
These discrepancies in the outcomes when using rate measurements from experiments and data from “in situ” measurements needs to be discussed as both are relevant for the evaluation of methane oxidation.
In general the discussion of the isotopic data is too weak and partly wrong. Figure 6 gives the relationship between concentrations and isotopic ratios. The regression line is used to argue for methane oxidation. However, to calculate the oxidation by those data a Rayleigh fraction calculation is mandatory (Whiticar, 1999). Just by eye I postulate a Rayleigh oxidation curve fitting to the dark green dots (the “deepest” water, i.e. the water with the highest salinity). Hence, reflected by the most 13C-enriched methane (related to the whole data set given in this paper) clear evidences for methane oxidation in this water mass are given. But unfortunately these data are not discussed in context to methane oxidation.
The discussion starts with: “...dissolved methane showed a vertical stratification with methane excess mostly recorded in shallow waters...”, so far so good but in summer the water masses discussed in this paper are stratified as well, clearly seen by the large gradient in salinity (Fig 5 salinity: 27.5-32.5). However this circumstance is not even mentioned nor considered in the discussion of the data. The discussion ignores the potential link of methane excess to the water stratification. Therefore the methane data are not discussed in context with oceanographic data or how it is promised in the abstract “paired with “thermohaline data”.
In Fig 6 the regression line covers the whole water column, i.e. surface water to deep water, just weakly distinguished by slightly different colored green points. However, due to the water stratification the vertical exchange is rather low. While the surface water is mostly locally affected by sea ice melt, the “deeper” water mass is most likely transported by currents. This circumstance needs to be considered in the discussion because of the different water “history” also the “history” of methane incorporated in each of those water masses is different. Therefore the regression line covering all water masses is not the right tool to say anything about oxidation.
In line 540 the authors promise to be able to identify the role of sea ice playing on the methane cycle. Unfortunately beside a short description of the status quo concerning the saturation level within sea ice nothing followed to convince me that this question is really answered.
Abstract:
It is not clear to me which data the statement: “quickly oxidized by microbes” is based on (last line in the abstract). The isotopic signature (13C-depleted or vice versa 12C-enriched) rather points to a missing oxidation in surface water.
212
Fig 2: the axis legend is too small
line 425: not clear to me what a... “seawater equilibrium supersaturation “... means,
line 426: Does 3.42 nM mean the atmospheric equilibrium in surface water?
line 426: It is also not clear to me which atmospheric methane concentration the calculation of the equilibrium is based on.
line 429: if fig 4 does not show a clear trend the question arises if this kind of figure is useful?
line 452-455: should be shifted before line 426
line 445 ... which is a clear evidence for water stratification
line 462: the isotopic ratios in the range of low concentration rather reflects an oxidation effect than a source effect (suggest to calculate a Rayleigh curve)
Fig 5: values in surface water don’t refer to methane oxidation
Fig 7: Methane discussed in the context of this paper is never abiotic
line 527: not clear to me on which calculation these numbers are based on
Unclear to me where the high methane concentration in sea ice might come from. Also, if we assume a methane production therein, a storage during the melt season therein is unlikely. While numbers of the brine volume fraction are missing I assume, when the bulk salinity (I assume here the bulk salinity is meant) is just 2, brine is nearly completely lost by melt. If so it remains an open question where within ice the high methane concentration might be localized. Rather it seems that the difference in concentration between seawater and sea ice is an “artefact” by the “salinity effect” of the calculation of concentration. Further” “contamination” during melt by flushing with seawater is likely. Also the coring procedure itself might contaminate melted ice cores with seawater.
line 539: which physical-chemical parameters are meant?
Fig 12: the white dots are too small.
line 730: ...”released the gas...” you mean the release of dissolved methane by brine ? needs clarification
line 740: what is meant with methane gas (dissolved or gaseous methane) ?
Citation: https://doi.org/10.5194/egusphere-2023-74-RC4 -
AC4: 'Reply on RC4', Alessandra D'Angelo, 18 Mar 2023
Dear Referee 4, thanks for the comments. We appreciate the time and effort that you and the reviewers dedicated to providing constructive feedback on our manuscript. Your insightful comments suggested valuable improvements to our paper. Below you can find our replies (Author Comment - AC).
The study presents a dataset including seawater salinity, nutrients, methane concentration and isotopic ratios in seawater and ice, and calculations of methane oxidation rates and constants. The nutrient data are not discussed in the context of the other data. Announced as thermohaline data in the abstract, I missed temperature data and found the usage of the salinity data disappointing.
AC: The nutrient data were used as ancillary data supporting the methane data, and we used this data in the multiparameter analysis to detect the water mass contribution. We acknowledge that the structure of the manuscript can be misleading, so we will edit it. The temperature data, together with the entire dataset, can be found in the Arctic Data Center DOI provided in the text.
The authors argue for higher methane oxidation in surface water than in deeper waters, based on rate measurements. However comparing the isotopic ratios coupled to the “in situ” concentrations reveals a pattern in contradiction to this statement. The low concentration paired with 13C-enriched ratios in “deeper waters” refers rather to methane oxidation therein than in “surface waters” where higher concentrations are paired with 13C-depleted ratios (compared to each other).
These discrepancies in the outcomes when using rate measurements from experiments and data from “in situ” measurements needs to be discussed as both are relevant for the evaluation of methane oxidation.
AC: The methane data measured in in-situ waters describe past processes, while the in-vitro experiments provide information of the present environment. The in-situ low concentration paired with 13C-enriched ratios in deeper waters suggested methane microbial oxidation during the past.
In general the discussion of the isotopic data is too weak and partly wrong. Figure 6 gives the relationship between concentrations and isotopic ratios. The regression line is used to argue for methane oxidation. However, to calculate the oxidation by those data a Rayleigh fraction calculation is mandatory (Whiticar, 1999). Just by eye I postulate a Rayleigh oxidation curve fitting to the dark green dots (the “deepest” water, i.e. the water with the highest salinity). Hence, reflected by the most 13C-enriched methane (related to the whole data set given in this paper) clear evidences for methane oxidation in this water mass are given. But unfortunately these data are not discussed in context to methane oxidation.
AC – as RC2: Figure 6 shows the relationship between the in-situ methane concentrations and isotopic ratio. We used this figure to show that the water column likely experienced methane microbial oxidation in the past. This was a simplified version of the Rayleigh distillation model as in Fenwick et al. (2017), Figure 14 (https://agupubs.onlinelibrary.wiley.com/doi/full/10.1002/2016JC012493).
The discussion starts with: “...dissolved methane showed a vertical stratification with methane excess mostly recorded in shallow waters...”, so far so good but in summer the water masses discussed in this paper are stratified as well, clearly seen by the large gradient in salinity (Fig 5 salinity: 27.5-32.5). However this circumstance is not even mentioned nor considered in the discussion of the data. The discussion ignores the potential link of methane excess to the water stratification. Therefore the methane data are not discussed in context with oceanographic data or how it is promised in the abstract “paired with “thermohaline data”.
AC: In the paragraph 1.2 we described the water column structure characterizing the Canadian Arctic Archipelago waters during the summer (lines 146 – 152) and we referred to the stratification of the water column in Figure 12. We think that the multiparameter analysis (MP) was a better way to map the water masses within our area of study. The salinity data were used in the MP analysis for the detection of the water masses and the results were discussed paired to the methane data. We take the referee’s critique, and we will make it clearer in the revised manuscript.
In Fig 6 the regression line covers the whole water column, i.e. surface water to deep water, just weakly distinguished by slightly different colored green points. However, due to the water stratification the vertical exchange is rather low. While the surface water is mostly locally affected by sea ice melt, the “deeper” water mass is most likely transported by currents. This circumstance needs to be considered in the discussion because of the different water “history” also the “history” of methane incorporated in each of those water masses is different. Therefore the regression line covering all water masses is not the right tool to say anything about oxidation.
AC: As aforementioned, we used this figure to show that the water column likely experienced methane microbial oxidation in the past. The purpose of this figure was to provide insight about the processes occurred during the past rather than the significative relationship between the methane concentration and isotope ratio of the present. We acknowledge that this was not clear in the text, and we will work on strengthening this point.
In line 540 the authors promise to be able to identify the role of sea ice playing on the methane cycle. Unfortunately beside a short description of the status quo concerning the saturation level within sea ice nothing followed to convince me that this question is really answered.
AC: In paragraph 4.4 we described the influence of the sea ice on the collected methane data. Because it was a summer campaign, we did not expect great impact of the sea ice on the seawater methane. Few stations were ice covered and we described the outcome both in the text and in Figure 13.
Abstract:
It is not clear to me which data the statement: “quickly oxidized by microbes” is based on (last line in the abstract). The isotopic signature (13C-depleted or vice versa 12C-enriched) rather points to a missing oxidation in surface water.
AC: The results of the in-vitro experiment suggested higher methane oxidation rates in shallow and Pacific-dominated waters. The in-situ isotopic signature describes past processes occurred in the water column.
Fig 2: the axis legend is too small
AC: We will fix it
line 425: not clear to me what a... “seawater equilibrium supersaturation “... means,
AC: “equilibrium” is a typo. It will be removed. Thanks for noticing it.
line 426: Does 3.42 nM mean the atmospheric equilibrium in surface water?
line 426: It is also not clear to me which atmospheric methane concentration the calculation of the equilibrium is based on.
AC: We use the Bunsen coefficient for the gas solubility to calculate the atmospheric methane concentration at in-situ temperature and salinity. The link to the code for the calculation is in line 248.
line 429: if fig 4 does not show a clear trend the question arises if this kind of figure is useful?
AC: Figure 4 is meant to show all the methane concentrations expressed as saturation anomalies. This provides important information even if not showing a spatial trend.
line 452-455: should be shifted before line 426
AC: We will edit it
line 445 ... which is a clear evidence for water stratification
line 462: the isotopic ratios in the range of low concentration rather reflects an oxidation effect than a source effect (suggest to calculate a Rayleigh curve).
Fig 5: values in surface water don’t refer to methane oxidation
AC: As aforementioned, the methane data measured in in-situ waters describe past processes, while the in-vitro experiments provide information of the present environment. The in-situ low concentration paired with 13C-enriched ratios in deeper waters suggested methane microbial oxidation during the past.
Fig 7: Methane discussed in the context of this paper is never abiotic.
AC: During the in-vitro experiments, we recorded flat trend of methane concentrations and isotope ratio over time in two samples (shown in fig.7), suggesting methane abiotic. We did not take these values into account for the microbial methane oxidation rates, to not bias the results.
line 527: not clear to me on which calculation these numbers are based on
AC: Methods are described in paragraph 2.3.
Unclear to me where the high methane concentration in sea ice might come from. Also, if we assume a methane production therein, a storage during the melt season therein is unlikely. While numbers of the brine volume fraction are missing I assume, when the bulk salinity (I assume here the bulk salinity is meant) is just 2, brine is nearly completely lost by melt. If so it remains an open question where within ice the high methane concentration might be localized. Rather it seems that the difference in concentration between seawater and sea ice is an “artefact” by the “salinity effect” of the calculation of concentration. Further” “contamination” during melt by flushing with seawater is likely. Also the coring procedure itself might contaminate melted ice cores with seawater.
AC: The salinity of the ice cores felt in a range of 0.5 and 3.5. We believe that the brine rejection was negligible at that time. We suggest that the methane excess in the sea ice was due to past freezing processes and that the increase of ice permeability influenced the methane enrichment within the underneath seawater and, in turn, methane depletion within the sea ice. We recognize that during the sampling process there could be seawater contamination, but we exclude that this could have affected all the sea ice results.
line 539: which physical-chemical parameters are meant?
AC: We measured: temperature, salinity, δ18O, δD, [CH4], δ13CH4. We can add this information in the text.
Fig 12: the white dots are too small.
AC: The white dots indicate the data points, so we prefer to keep them small in order to highlight the outcomes of the figure.
line 730: ...”released the gas...” you mean the release of dissolved methane by brine ? needs clarification
line 740: what is meant with methane gas (dissolved or gaseous methane) ?
AC: We mean the release of dissolved methane through the permeability of the sea ice.
Citation: https://doi.org/10.5194/egusphere-2023-74-AC4
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AC4: 'Reply on RC4', Alessandra D'Angelo, 18 Mar 2023
Status: closed
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RC1: 'Comment on egusphere-2023-74', Anonymous Referee #1, 28 Feb 2023
The manuscript presents a dataset including nutrients, methane concentration in seawater and ice, and calculations of methane oxidation rates and constants. The authors investigate the possible source of the methane. They propose that microbes can rapidly oxidize methane produced within the ice during Arctic blooms, and they also conclude that sea ice is oversaturated in methane and that meteoric waters have higher methane oxidation rates than Atlantic waters.
The overall story is not very convincing with many inconsistencies when comparing numbers in the text and figures or tables, and sometimes figures not correctly sited. New information is also mentioned in the discussion or the conclusion with no support from figures or tables (e.g. lines 691, 722, 769, 779). The nutrients results are not presented until the conclusion. Moreover, many instances of plagiarism from Uhlig’s work should be avoided by referring to their papers. I have several issues throughout the text as presented below.
The abstract presents some information from a rejected companion manuscript (D’Angelo et al., 2022, https://doi.org/10.5194/essd-2022-306) and this information is not mentioned in the rest of the manuscript (e.g. chl. A correlation with meteoric waters and methane concentration in the abstract). The simple calculation (lines 25-26) is also not mentioned in the manuscript.
The introduction promises methane budget in the Northwest Passage but this is not calculated. At the beginning of the 1.2, none of the names (line 113) are shown on figure 1. The last paragraph details the different water masses and chemistry, but only ranges of salinity are given. The authors should also indicate ranges for temperature, nutrient and oxygen saturations.
Material and methods: Transects are mentioned in the sampling procedures (2.1), but only one is visible on figure 1 (West of Navy Board Inlet).
Please explain in this section the difference between experimental and discrete samples for methane and why you do this distinction. Why not presenting methane concentrations in seawater in table S1 like shown for sea ice in table S2? Table S1 shows 76 in situ samples, and 27 experimental. Where is the 56 number coming from in table S1? 18 seawater samples were collected for microbial community but only 9 samples are presented in figure 12. Please explain.
The link for Uhlig and Loose 2017 directs towards their data repository in PANGAEA instead of their publication. The manuscript contained several instances of plagiarism from Uhlig and Loose 2017 and Uhlig et al. 2018. The only differences for chemical and biological analyses are the names given to the variables and the in-depth of the analysis. The authors should explain their choice of using αox of 1.007 as a lower bounds when Uhlig and Loose states that this value overestimates the oxidation. Moreover, the correlation using this value is not very convincing. Because the submitted manuscript is primarily a repetition Uhlig’s work, references and brief summary of the majority of the material and method would probably suffice.
The section “Estimating the oxidation rates from mass balance and isotopic fractionation” is unclear (explanation of kox.delta). 28 degrees is not the threshold between warm and cold environments, the authors mean 1 degrees as also mentioned in Uhlig and Loose 2017.
Water mass detection: please give the range for all markers, not only for δ18O.
Results: The authors only show the methane concentration and isotopic signature for one profile at Croker Bay, and figure 6 is the only figure showing all these without giving the location or depth. A general figure showing all data with regard to the longitude would be helpful and might give more indication on the spatial variation. Figure 7 only shows kox average between all profiles. The authors should add all data in this graph (may be instead of table 2), including the average by using a different thickness of line for example. I have the same comment regarding the ice cores, where only 1 and 2 are shown in figure 8. The authors indicate a methane maxima at Westernmost Station of 24nM, but the figure shows a value closer to 21nM. Finally, the summary of the ice core section (isotopic signature in ice cores was between -52 and -33 ‰) is inconsistent with the text and figure 8.
Discussion: Please explain the statement line 561-562 and rephrase the sentence that follows. Table 2 presents kox and rox, and the stations influenced by PW only present shallow water. Please explain how this might influence the conclusions. The authors state that higher microbial oxidation rates correspond to higher methane concentrations from Figure 9 which shows an extremely low (0.03) correlation coefficient, even if the data measured in CB influence the trend. Could this low value be due to the lower bound chosen for αox? There is no labels over the dots in figure 9 as indicated in the caption. The Michaelis-Menten kinetics plot is supposed to confirm that high methane concentrations are associated to low kox, but this is not obvious in the figure. The low methane oxidation rates in ice covered sites is not shown in figure 13.
The authors present the influence of SIM and MW on methane concentration and isotopic signature (figure 11), but the comparison with PW and AW is in the appendix. The authors should present all results in a figure with different panels. They also refer to distribution of methane across the study area from figure 12, but this figure shows kox and not CH4.
Specific comments:
Line 88: typo (inasmuch)
Line 92: define CAA (has only been defined in the abstract)
Line 297: where is the linear correlation of 0.52 coming from? The caption in figure 2 indicates 0.2564.
Line 206-207: “We also tried to identify the outliers through other procedures”: this doesn’t say much.
Line 392: define SA as Absolute salinity
Line 426: where is this number coming from?
Line 435: T and S are used for the first time. Please define.
Line 480: remove
Line 611: inconsistency of the average kox stated here and table 2.
Line 661: Figure 7 and table 2, not figure 10.
Figure 10: The font in the inlet figure is too small, typo in the caption (Forland and not Forlan)Citation: https://doi.org/10.5194/egusphere-2023-74-RC1 -
AC1: 'Reply on RC1', Alessandra D'Angelo, 18 Mar 2023
Dear Referee 1, thanks for the comments. We appreciate the time and effort that you and the reviewers dedicated to providing constructice feedback on our manuscript. Your insightful comments suggested valuable improvements to our paper. Below you can find our replies (Author Comment - AC).
The overall story is not very convincing with many inconsistencies when comparing numbers in the text and figures or tables, and sometimes figures not correctly sited. New information is also mentioned in the discussion or the conclusion with no support from figures or tables (e.g. lines 691, 722, 769, 779).
AC: The numbers in the text are averaged values, while the numbers in the tables show the individual values. Thank you for pointing this out, we will report the maximum in the averages, rather than reporting the maximum from the individual samples, to be consistent with the figures. If the readers want to explore the methane data, they can download the source data from the Arctic Data Center (https://doi.org/10.18739/A2BN9X45M); whereas the table with the Spearman’s correlation will be added in the supplemental material.
The nutrients results are not presented until the conclusion. Moreover, many instances of plagiarism from Uhlig’s work should be avoided by referring to their papers. I have several issues throughout the text as presented below.
AC: Nutrients results are shown in 3.1 and mentioned in 4.2 prior conclusions. We have followed the method that Uhlig and Loose and Uhlig et al. describe, and we have endeavored to strike a balance between citing that work and reproducing key equations here, in order to make it easy for the reader to follow the method. We take the reviewers critique that this reads like some material has been copied verbatim and we will revise the methods to avoid that.
The abstract presents some information from a rejected companion manuscript (D’Angelo et al., 2022, https://doi.org/10.5194/essd-2022-306) and this information is not mentioned in the rest of the manuscript (e.g. chl. A correlation with meteoric waters and methane concentration in the abstract).
AC: The reference to the rejected manuscript referred to a “preprint” DOI (lines 206, 402), while the sentence that the reviewer is highlighting refers to the DOI of the published dataset (see lines 648 and 653). We will remove references to the ESSD manuscript that is in the process of resubmission, and simply cite the dataset DOI.
The simple calculation (lines 25-26) is also not mentioned in the manuscript.
AC: A description will be added.
The introduction promises methane budget in the Northwest Passage but this is not calculated.
AC: True, the term “budget” is misleading. We will refer to “quantifying oxidation” as one important term in the methane budget.
At the beginning of the 1.2, none of the names (line 113) are shown on figure 1.
AC: The locations will be added on the map.
The last paragraph details the different water masses and chemistry, but only ranges of salinity are given. The authors should also indicate ranges for temperature, nutrient and oxygen saturations.
AC: Values of temperature, nutrient and oxygen saturations will be added from literature.
Material and methods: Transects are mentioned in the sampling procedures (2.1), but only one is visible on figure 1 (West of Navy Board Inlet).
AC: In Fig.1, we showed only the stations where methane was investigated.
Please explain in this section the difference between experimental and discrete samples for methane and why you do this distinction. Why not presenting methane concentrations in seawater in table S1 like shown for sea ice in table S2?
AC: A clarification about why we implemented different treatments for in-situ and in-vitro samples will be added in the text. The seawater methane data are shown in the Arctic Data Center (https://doi.org/10.18739/A2BN9X45M), cited in the text.
Table S1 shows 76 in situ samples, and 27 experimental. Where is the 56 number coming from in table S1?
AC: We collected duplicated samples for the incubations in order to have a better reproducibility; hence, the samples were 56 (28x2) in total. One sample was leaking, so we took it off (27x2). We acknowledge that the text lacks information and we will add it.
18 seawater samples were collected for microbial community but only 9 samples are presented in figure 12. Please explain.
AC: Same as before. In the plot we show the averaged samples of the replicates (9x2), as explained in the caption.
The link for Uhlig and Loose 2017 directs towards their data repository in PANGAEA instead of their publication.
AC: Thanks for noticing it, it will be fixed.
The manuscript contained several instances of plagiarism from Uhlig and Loose 2017 and Uhlig et al. 2018. The only differences for chemical and biological analyses are the names given to the variables and the in-depth of the analysis.
AC: As aforementioned, we have followed the method that Uhlig and Loose and Uhlig et al. describe, and we have endeavored to strike a balance between citing that work and reproducing key equations here, to make it easy for the reader to follow the method. We take the reviewers critique that this reads like some material has been copied verbatim and we will revise the methods to avoid that.
The authors should explain their choice of using αox of 1.007 as a lower bounds when Uhlig and Loose states that this value overestimates the oxidation. Moreover, the correlation using this value is not very convincing. Because the submitted manuscript is primarily a repetition Uhlig’s work, references and brief summary of the majority of the material and method would probably suffice.
AC: We are sorry, in the text is reported the wrong information. Based on values that matched with the mass balance oxidation rate constant (kox.mass.balance), we decided to use the αox = 1.025 for our estimation of kox.isotope.ratio. We’d like to thank the referee for bringing up this concern and we will certainly update the text in the revised manuscript.
The section “Estimating the oxidation rates from mass balance and isotopic fractionation” is unclear (explanation of kox.delta).
AC: In this section, we described the procedure for calculating the methane oxidation rate constants. We followed published methods; hence we will remove the redundant text and cite the existing literature.
28 degrees is not the threshold between warm and cold environments, the authors mean 1 degrees as also mentioned in Uhlig and Loose 2017.
AC: This was a typo, it was 2⁰C, as in Uhlig and Loose (2017).
Water mass detection: please give the range for all markers, not only for δ18O.
AC: The endmembers for the multivariate analysis will be all collected in a table.
Results: The authors only show the methane concentration and isotopic signature for one profile at Croker Bay
AC: All of the methane concentration data is shown as saturation anomalies in Figure 4. We decided to show only one site for a visual purpose. The choice of Croker Bay was motivated by the highest methane concentration coupled to the lowest isotopic signature. To fill out the picture of in-situ methane concentrations, we will add all station profiles to a multi-panel figure in Supplemental material.
figure 6 is the only figure showing all these without giving the location or depth. A general figure showing all data with regard to the longitude would be helpful and might give more indication on the spatial variation.
AC: Figure 4 also shows all the methane concentrations expressed as saturation anomalies. It is challenging to depict the spatial variations in Lat/Lon/Depth in one figure, so we have attempted to make other depictions. Figure 6 had the purpose of providing information about the general trend of the in-situ methane samples. The aim of plotting the data using a color scale showing the seawater absolute salinity was to highlight the influence of the freshwater on the methane cycle. Nevertheless, we will add a plot showing all the profiles of methane concentration and isotope ratio by station in the supplemental material.
Figure 7 only shows kox average between all profiles. The authors should add all data in this graph (may be instead of table 2), including the average by using a different thickness of line for example.
AC: Figure 7 and Table 2 show averages between the duplicate in-vitro samples. If the reader wants to examine the values of the duplicates, they can download the source data from the Arctic Data Center. We don't have profiles of methane oxidation at each station and can only assemble a profile by providing oxidation rates from all the stations.
I have the same comment regarding the ice cores, where only 1 and 2 are shown in figure 8.
AC: We usually prefer to show few panels per figure in the manuscript, for a better visualization. We can certainly add all cores data in the supplemental material.
The authors indicate a methane maxima at Westernmost Station of 24nM, but the figure shows a value closer to 21nM.
AC: Thank you for pointing this out, we will report the maximum in the averages, rather than reporting the maximum from the individual samples, to be consistent with the figure.
Finally, the summary of the ice core section (isotopic signature in ice cores was between -52 and -33 ‰) is inconsistent with the text and figure 8.
AC: In the summary we showed the range of the values, while in the text and figure we showed the averaged values. We will make sure that a revised manuscript uses values that are consistent with the figures, to reinforce these points, and avoid creating confusion. We will do this in the text related to Figure 8 and throughout the manuscript.
Discussion: Please explain the statement line 561-562 and rephrase the sentence that follows. Table 2 presents kox and rox, and the stations influenced by PW only present shallow water. Please explain how this might influence the conclusions.
AC: We acknowledge that the sentence is incomplete as written, and we will revise the manuscript with “Pacific Water (PW) was present at fractions greater than 50% in the waters above 200 m, which also coincided with the regions of high methane oxidation. Moreover, in samples collected from deeper layers we recorded lower oxidation rates, suggesting that the AW-origin layers did not support present methane microbial metabolism.”. This will also answer the second comment.
The authors state that higher microbial oxidation rates correspond to higher methane concentrations from Figure 9 which shows an extremely low (0.03) correlation coefficient, even if the data measured in CB influence the trend. Could this low value be due to the lower bound chosen for αox?
AC: We chose the αox upper bound for calculating the kox.isotope.ratio, and this decreased the order of magnitude of the averaged kox.Yes, the choice of the fractionation coefficient influences the magnitude of the oxidation rate constant, that is the reason why it is important to observe both isotope ratio and mass balance oxidation rate constants. In this study, the kox.isotope.ratio data were consistent with the mass balance data (kox.mass.balance), as shown in Figure 2.
There is no labels over the dots in figure 9 as indicated in the caption.
AC: This will be fixed.
The Michaelis-Menten kinetics plot is supposed to confirm that high methane concentrations are associated to low kox, but this is not obvious in the figure.
AC: The aim of this plot is to show the reaction velocity as a function of substrate concentration. However, we acknowledge that the little amount of data does not highlight the outcome, hence we will remove Figure 10 and qualitatively discuss the Michaelis-Menten kinetics related to the Figure 9.
The low methane oxidation rates in ice covered sites is not shown in figure 13.
AC: The color scale shows the methane oxidation rate constant, and the light green indicates the lower values. We can work on making it clearer for the reader.
The authors present the influence of SIM and MW on methane concentration and isotopic signature (figure 11), but the comparison with PW and AW is in the appendix. The authors should present all results in a figure with different panels.
AC: For a better visualization we did not show all the data, but we can add it as suggested.
They also refer to distribution of methane across the study area from figure 12, but this figure shows kox and not CH4.
AC: It will be fixed.
Line 611: inconsistency of the average kox stated here and table 2.
AC: In Table 2 we showed all the values of the averaged methane oxidation rate constant (kox.av), including the 0s. In the calculation for the average, we only took into account the values of kox.av >0 (suggesting methane oxidation). We recognize that this information was missing in the text, and we will add it.
Line 88: typo (inasmuch)
AC: We will fix it.
Line 92: define CAA (has only been defined in the abstract)
AC: We will fix it.
Line 297: where is the linear correlation of 0.52 coming from? The caption in figure 2 indicates 0.2564.
AC: We will add the Spearman’s correlation and linear regression information in the supplemental material.
Line 206-207: “We also tried to identify the outliers through other procedures”: this doesn’t say much.
AC: More details will be added.
Line 392: define SA as Absolute salinity
AC: We will fix it.
Line 426: where is this number coming from?
AC: More details will be added.
Line 435: T and S are used for the first time. Please define.
AC: We will fix it.
Line 480: remove
AC: We will fix it.
Line 661: Figure 7 and table 2, not figure 10.
AC: We will fix it.
Figure 10: The font in the inlet figure is too small, typo in the caption (Forland and not Forlan)
AC: We will fix it.
Citation: https://doi.org/10.5194/egusphere-2023-74-AC1
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AC1: 'Reply on RC1', Alessandra D'Angelo, 18 Mar 2023
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RC2: 'Comment on egusphere-2023-74', Anonymous Referee #2, 07 Mar 2023
The study of D’Angelo et al. describes the methane concentrations and oxidation rates in Canadian Arctic Sea. This is certainly a valuable data set and area with few investigations. However, the study is rather lengthy and confusing. The result section is presented in messy way. The aspects of the discussion are not supported by the result section.
Please see my comments below and additional remarks in the text.
L 232 ff: The Method for MOX used is not the standard one, i.e. 3H or 14C tracer, a direct comparison of the method would be useful
If this method is published the respective section should be shortened and moved to the Supplements
The explanation of the method should be more to the point, and stress the important aspects, such as what are the effects of the long incubation time, and what is the limit of detection?
L 356 ff: DNA extraction: why was the extraction performed after the experiments? This is not the in-situ community!!
Figure 3: This graph is rather unconventional; I would prefer to show the longitude on the x-axis and color code the concentrations…. This would make your message much clearer
Figure 4: as in figure 3, it would be clearer to have the geographic settings, depth and longitude on the x/y axis and the variable with color coding
Figure 6: is this a significant relationship? what is the value of p? Would it be better to use the logarithmic values? Especially at the low values, I doubt that there is a significant correlation....
figure 5: Methane in situ =? Why do not you name it methane concentration, better wording, Keep it simple, if you are talking about MOX, just name it methane oxidation rate or MOS, the details of determination are already given in MM section
L 474 ff: A bit more text on the results of the MOX, where are why the highest / lowest rates? As it is an important factor of this work, the describing text is very meagre
L 502 ff: Community structure: Did you detect no known methanotrophs at all?? Even after such long incubations and MOX activity? Is it known if the detected species have the genes for methane oxidation? Could this be an incubation artifact, any comparison with water without any incubations? There is no known relation between Flavobacteria and methane oxidation, thus it seems to me, that you just did not detect any MOBs, but I do not understand the connection between MOX and these other bacterial groups….
Sea ice: Was there are difference in methane concentration between multi-year and first-year ice, please clarify! A figure with both methane concentrations in the sea water and ice cores would be helpful… If you state a difference in variability in the isotopic composition of sea ice and water, please give the exact numbers for the variability, and what for is this information needed?
Discussion:
Already the first introduction sentence is not supported by the result section.
Also, the discussion on Figure 9 is not supported by data from the results, also statistics on this figure are not convincing.
The discussion on the kinetics of methane oxidation is completely confusing and without any profoundness on the subject.
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AC2: 'Reply on RC2', Alessandra D'Angelo, 18 Mar 2023
Dear Referee 2, thanks for the comments. We appreciate the time and effort that you and the reviewers dedicated to providing constructice feedback on our manuscript. Your insightful comments suggested valuable improvements to our paper. Below you can find our replies (Author Comment - AC).
The study of D’Angelo et al. describes the methane concentrations and oxidation rates in Canadian Arctic Sea. This is certainly a valuable data set and area with few investigations. However, the study is rather lengthy and confusing. The result section is presented in messy way. The aspects of the discussion are not supported by the result section.
Please see my comments below and additional remarks in the text.
L 232 ff: The Method for MOX used is not the standard one, i.e. 3H or 14C tracer, a direct comparison of the method would be useful
AC: To date, there is no direct comparison between the two methods. The use of stable isotopes has recently been developed from Chan et al. (2016) and Leonte et al. (2017). Here, they used stable isotopes to measure methane oxidation rates in in-vitro seawater. It would be beneficial to assess the difference in methodologies and how these differ in their approach and their rate estimates, but this would require a separate study.
If this method is published the respective section should be shortened and moved to the Supplements.
AC: The method section will be shortened. We followed published methodologies; hence we will remove the redundant text and cite the existing literature.
The explanation of the method should be more to the point, and stress the important aspects, such as what are the effects of the long incubation time, and what is the limit of detection?
AC: The section on the methods will be revised in order to better highlight the most important aspects.
L 356 ff: DNA extraction: why was the extraction performed after the experiments? This is not the in-situ community!!
AC: The in-situ community was analyzed in parallel with the in-vitro samples. Hence, we had both community data at “time zero” and at “time final” of the experiments. We acknowledge this was unclear in the text, and we apologize for this. We will describe it better in the revised version of the manuscript.
Figure 3: This graph is rather unconventional; I would prefer to show the longitude on the x-axis and color code the concentrations…. This would make your message much clearer. Figure 4: as in figure 3, it would be clearer to have the geographic settings, depth and longitude on the x/y axis and the variable with color coding.
AC: Thanks for the suggestions. We will redo the figures as recommended.
Figure 6: is this a significant relationship? what is the value of p? Would it be better to use the logarithmic values? Especially at the low values, I doubt that there is a significant correlation....
AC: Figure 6 shows the relationship between the in-situ methane concentrations and isotopic ratio. This figure suggests that the water column likely experienced methane microbial oxidation in the past. We used this figure as a simplified version of the Fenwick et al. (2017) Figure 14 (https://agupubs.onlinelibrary.wiley.com/doi/full/10.1002/2016JC012493). We followed the referee suggestion and plotted the [CH4] values on logarithmic scale (supplement 1). The R2 and p-value did not improve much, but for the purpose of the figure this is not a concern.
figure 5: Methane in situ =? Why do not you name it methane concentration, better wording, Keep it simple, if you are talking about MOX, just name it methane oxidation rate or MOS, the details of determination are already given in MM section
AC: We will re-name the terms in order to make the text clearer. Methane in-situ data include both concentrations and isotope ratio, hence we endeavored to use a clear and correct terminology.
L 474 ff: A bit more text on the results of the MOX, where are why the highest / lowest rates? As it is an important factor of this work, the describing text is very meagre
AC: We will work on implementing and enriching the text in the results section for the methane oxidation rates.
L 502 ff: Community structure: Did you detect no known methanotrophs at all?? Even after such long incubations and MOX activity? Is it known if the detected species have the genes for methane oxidation? Could this be an incubation artifact, any comparison with water without any incubations? There is no known relation between Flavobacteria and methane oxidation, thus it seems to me, that you just did not detect any MOBs, but I do not understand the connection between MOX and these other bacterial groups….
AC: The genomic analysis only showed the 25 most abundant taxa in our samples, and some of them were unclassified. It is likely that methanotrophs occurred in the samples, but we could not detect them. We did not identify known methane oxidizing taxa both in in-situ and in-vitro samples. Other studies (e.g., Redmond and Valentin, 2011; Jensen et al., 2008; Radajewski et al. 2002) suggested that Bacteroidetes Flavobacteria might be directly involved with methane uptake, as secondary consumer.
Sea ice: Was there are difference in methane concentration between multi-year and first-year ice, please clarify! A figure with both methane concentrations in the sea water and ice cores would be helpful… If you state a difference in variability in the isotopic composition of sea ice and water, please give the exact numbers for the variability, and what for is this information needed?
AC: There was no trend of methane concentrations from first-year to multi-year ice cores. We can add a figure with both methane concentrations in the sea water and sea ice in the supplementary material. In this study, we use the isotopic ratio of methane as tracer for supporting the methane concentration data. For confirming the methane oxidation, we rely on the consistency of both datasets. In the case of the isotopic ratio within the sea ice samples, we highlighted the differences between seawater and sea ice data, to support the hypothesis of methane oversaturation along the whole vertical profile of the sea ice (hence more homogeneous range of values, suggesting targeted inputs). We will provide the exact value of the variability in the text.
Discussion:
Already the first introduction sentence is not supported by the result section.
AC: The introductory section highlighted the main outcomes showed above in the result section (methane excess in shallow waters, highest oxidation rates in surface and Pacific-origin waters), but we take the referee critique and will write the section clearer, in order to reflect the above results.
Also, the discussion on Figure 9 is not supported by data from the results, also statistics on this figure are not convincing.
AC: In figure 9, we reported the averaged values of kox against the dissolved methane concentration. We showed this relationship to assess how the in-situ methane concentrations affect the methane oxidation rates and we linked this outcome to the above presented results of methane concentrations and oxidation rates (lines 582 – 584). We accept the reviewer’s critique that this did not connect well with previous results, and we will revise the paragraph according to the suggestion.
The discussion on the kinetics of methane oxidation is completely confusing and without any profoundness on the subject.
AC: We will improve this paragraph. We will remove Figure 10 and qualitatively discuss the Michaelis-Menten kinetics related to the Figure 9.
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AC2: 'Reply on RC2', Alessandra D'Angelo, 18 Mar 2023
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RC3: 'Comment on egusphere-2023-74', Anonymous Referee #3, 08 Mar 2023
The authors present a study that focuses on the methane budget in Arctic marine environment and the role of microbial metabolism in the water column and in sea ice driven by environmental factors such as nutrient supply, water mass movements, and input of fresh water. Samples for this study were collected during a two-week cruise in July/August 2019; the 17 investigated stations were located in the Parry Channel, Canadian Arctic Archipelago.
The data set of this study consists of depth profiles of CTD measurements, nutrient analyses, analysis of the bacterial community via 16S rRNA sequencing, microbial in-vitro incubations to evaluate methane consumption/production, and methane concentration measurements of seawater and sea ice and from the in-vitro incubations. This is a multi-faceted dataset from an area where there is only little research available.
Unfortunately, several paragraphs in the manuscript appear confused especially the results part where many outcomes are already discussed quite detailed.
Most confusing to me is the section about the microbial community composition. The authors identified Aurantivirga, Oleispira and Planctomarina as dominant bacteria in the in-vitro incubation and suggested these taxa as being the main methane oxidizers in the study area. It would be of interest, if any known MOB were found in the samples even if in small quantities. It is not clear to me for how long each samples was incubated – L261: “The time of the incubations varied between 7 and 25 days”. Further, authors state “The oxidation detection limit was passed between 5 and 18 incubation days after incubation began, revealing the range of rates we observed.” (L497). On which basis did authors decide to run one incubation longer than the other? Was the duration of the incubation experiment the same for all samples after they reached the detection limit? What was the total duration of the incubation experiment? How did you make sure that you actually can compare the rates among samples from different sites if incubation times differ that much? Another factor is that the community composition in an incubation changes over time, and if a sample for molecular analysis is only taken at the end of an experiment where incubation times differed over weeks (I assume from the information given), how will it be possible to make a valid estimate of microbial population in an sample and further transfer this assumption to the studied area? Why didn´t you sequence water and sea ice samples (before incubating them)?
The introduction is inconsistent. In L47, the authors promise to give and introduction to microbial metabolisms associated with methane in the marine environment. They start with describing the methane oxidizing taxa, but forgot to mention microbes associated to methanogensis. In the next paragraph, methanogenesis is subject, but only in context with environmental drivers. I would like to learn more about what is known about the community structure of methane producers in the ecosystem the study is focusing on. On the other hand, this information might become irrelevant when the molecular analysis doesn´t reveal any microbial taxa that are clearly associated with methanogensis or MOx.
In the last paragraph of the introduction, authors promise to “elucidate the methane budget in the NWP”, but the final calculation of the budget for the entire study area or at least for a transect is not part of the manuscript.
Generally, authors should be more consistent with word spelling (e.g. Western-most Station/ Westernmost Station) and abbreviations. In one paragraph the full site names are used, in the next paragraph only IDs. Same applies to the water masses throughout the manuscript. I recommend to use as little abbreviations as possible.
L46: Are there more recent studies available?
L49: I agree that MOx is an important sink for dissolved methane in the water column, but the phrase “over some depth ranges and at some locations” is a bit too simple. MOx is, wherever it happens, an important mechanism to remove CH4 from the environment. Please, be more precise and clarify what you mean with “over some depth ranges”! From shallow shelf to deep ocean can be a range of several 1000 meters. The same applies to the location. Do you mean “some locations” are more relevant for MOx activity than others? If so, why is that? Or are you referring to the limited studies focusing on MOx in the Arctic? Make that clear!
L61: Too much of a jump in topic – wonder what the environmental drivers for MOx are.
L85: Microbial community structure as measure for ecosystem states - add a reference! This sentence is a bit lost in the context, since the following paragraph is completely independent of the above-mentioned community structure.
L88: fix typo “inasmuch”
L102 - 109: No need to give an overview of the general structure of the manuscript. This paragraph can be deleted.
L114: Could you rephrase it to: “This Channel connects Baffin Bay to the east with the Beaufort Sea to the west.”?
Fig.1: Why are red dots numbered and yellow dots not?
L153: “The western part of the CAA is characterized by a more consistent sea-ice coverage” compared to?
The material and methods part is sometimes too details that makes the manuscript hard to read. Authors should think of either shorten it and refer to references if methods were published elsewhere already and/or moving some lengthily parts to the supplements.
L166: “samples were collected in the vicinity of Parry Channel” – were samples taken in the Parry Channel or only in the vicinity of (near to) the Channel. To me it makes a difference.
L176: “Sea ice charts were collected by the Canada ice center” - Why is this relevant?
L188: With “in-vitro methane incubations” do you mean the MOx rate measurements mentioned in L186? It is not clear to me where these samples were taken. Be consistent with wording throughout the text.
L191: the sterivex filters were removed from where? from the bags?
L200: it´s not relevant at which institution the measurements were done as long as instrument specifications are shown. If you want to give credit to an collaborating institution, do this in the acknowledgements.
L207: You tried to identify outliners through other procedures. Want to mention them?
L222: “For the calibration of the instrument, we used additional methane standards.” - this information is irrelevant if you don´t add the name of instrument that was used. I think, you do that at a later point, so this sentence can be removed.
L229: Again, what is meant by in-situ measurements? Methane concentration measurements? What are the experimental bags? The Incubation experiments? MOx rate measurements? Be consistent with wording used throughout the manuscript.
L275 and the following lines: check subscripts in the formulae and in the text and correct them.
L306: only give the final concentration of NaOH in your samples.
L349: “A third outcome of the incubations can be methane production.” This sounds weird, could you rephrase it?
L356: Why is there a reference? Are data published elsewhere? If you followed a method/protocol published by Uhlig, than make that clear.
L357: According to the paragraph in L188-194, samples for molecular analysis were collected via Sterivex filters. Here you are giving two different kits for DNA extraction. Which one was used – the MoBio or the Millipore? Did you follow the standard extraction protocol? If yes, then all lines after L359 starting with “without the need for enzymes or hazardous organic chemicals.” and including L368 can be removed. “Inhibitor Removal Technology® (IRT) was included to provide high-quality DNA from all types of water samples, even those containing heavy amounts of contaminants.” Was IRT part of the extraction kit? Or is it something you added to the extraction protocol? If IRT is a regular ingredient of the kit, it´s not worth mentioning it.
How was the sequence analysis and taxonomical classification done after receiving the sequencing reads? Which pipeline and reference database were used? On which platform are the raw data stored?
L370: Is the protocol for the library prep. not published elsewhere? If yes, please, give reference and consider to shorten this paragraph and move details into the SUPP.
L392: define SA and apply superscript to d18O
L419: Space missing
Fig.4: T and S define as temperature and salinity instead
Fig.6: It´s hard to distinguish between different green shades. Could you apply a better color scale?
The results part contains detailed discussion already e.g. L444, 457, 460, 496, 503….especially in 3.4., most of the results are already discussed (L503 and L511 – 524).
Tab.2: Could be moved to the SUPP, since data are shown in Fig.7. L480: apply subscript to kox, remove your personal note!
Fig.7: you could apply a longitude color scaling to this figure, too, to indicate sampling sites. Or add IDs.
L532: redundant information - already mentioned in L529.
L536: “in the proximity of the Westernmost station.” – could you give a better measure for distances and direction here, please?
L544: Add a measure for “thin first-year ice” like you did in L546. How thin was it?
Fig.8: This figure only shows results of core 1 and 2. Why are data from core 3,4, and 5 not shown? Were can I find those profile data? (BTW it´s not obverse at the first sight that this data belong to core 1 and 2 – I suggest to change the heading of each plot from just “1” and “2” to “Core 1” and “Core 2”).
L562: “Here, we also recorded higher methane microbial oxidation rates, likely associated with Pacific-origin microbes and with the seasonal biology.” - I don´t understand where this assumption comes from.
L569: Only two references here? this suggests that there are only two studies available!, but it´s not true, there are more than only two studies of MOx in Arctic marine environments that are worth mentioning here.
L576: Again, only two references for a general statement – add “e.g.” in front of the references mentioned and use references which give the best example for underlining your statement.
Fig.9: 592: brackets missing, L594: can´t find any labels above dots in the figure.
L601: define DWH.
Fig.10: It´s called Prins Karls Forland (L633). What does NPP mean?
L652: What is MW and SIM? Define it. It gets too confusing with water mass and site ID abbreviations.
L669: What´s data CB?
L670: Check the display of your references! This applies to the entire manuscript!
Fig.11: What are MP results?
L706: What is meant by “weak methane metabolism”? Better give ranges that indicate “weak” and “stronger” activities.
L715: “the greatest sea ice cover” compared to?
Fig.13: Add abbreviation (SIC) behind “sea ice concentrations”. What does “Kox averaged by CTD” mean? Is it the average value of all depth profile measurements at one site?
L763: Add references that show that Aurantivirga are associated with sediments.
L767: Is there any study that confirms that Chloroplast sequences from V4-V5 region were used for environmental prediction of bloom scenarios?
L792 – 797: This statement was concluded in the previous sentences, no need to summarize it again.
It is not necessary to mention the name of the research vessel every time when something is done onboard.
Citation: https://doi.org/10.5194/egusphere-2023-74-RC3 -
AC3: 'Reply on RC3', Alessandra D'Angelo, 18 Mar 2023
Dear Referee 3, thanks for the comments. We appreciate the time and effort that you and the reviewers dedicated to providing constructice feedback on our manuscript. Your insightful comments suggested valuable improvements to our paper. Below you can find our replies (Author Comment - AC).
The authors present a study that focuses on the methane budget in Arctic marine environment and the role of microbial metabolism in the water column and in sea ice driven by environmental factors such as nutrient supply, water mass movements, and input of fresh water. Samples for this study were collected during a two-week cruise in July/August 2019; the 17 investigated stations were located in the Parry Channel, Canadian Arctic Archipelago.
The data set of this study consists of depth profiles of CTD measurements, nutrient analyses, analysis of the bacterial community via 16S rRNA sequencing, microbial in-vitro incubations to evaluate methane consumption/production, and methane concentration measurements of seawater and sea ice and from the in-vitro incubations. This is a multi-faceted dataset from an area where there is only little research available.
Unfortunately, several paragraphs in the manuscript appear confused especially the results part where many outcomes are already discussed quite detailed.
Most confusing to me is the section about the microbial community composition. The authors identified Aurantivirga, Oleispira and Planctomarina as dominant bacteria in the in-vitro incubation and suggested these taxa as being the main methane oxidizers in the study area. It would be of interest, if any known MOB were found in the samples even if in small quantities. It is not clear to me for how long each samples was incubated – L261: “The time of the incubations varied between 7 and 25 days”. Further, authors state “The oxidation detection limit was passed between 5 and 18 incubation days after incubation began, revealing the range of rates we observed.” (L497).
AC: Thanks for bringing this up, we will add a table with all the information in the supplementary material.
On which basis did authors decide to run one incubation longer than the other? Was the duration of the incubation experiment the same for all samples after they reached the detection limit? What was the total duration of the incubation experiment? How did you make sure that you actually can compare the rates among samples from different sites if incubation times differ that much?
AC: The duration of the incubation is driven by the logistical constraints. Because the stable isotope and mass balance method is less sensitive to changes in methane, the incubation time needs to be longer than the radioisotope method. Samples collected at the early part of the cruise had longer time to incubate, whereas samples at the end had a shorter time. Post-cruise, we extended the incubation times by continuing our analysis at a lab in Thule airbase (Greenland). However, this period could not be extended beyond 10 days. Given the incubation time, the smallest oxidation rates will not be resolvable, but we can determine what the lower limit is using the uncertainty, and this has been reported, as it was in Uhlig and Loose (2017).
Another factor is that the community composition in an incubation changes over time, and if a sample for molecular analysis is only taken at the end of an experiment where incubation times differed over weeks (I assume from the information given), how will it be possible to make a valid estimate of microbial population in an sample and further transfer this assumption to the studied area? Why didn´t you sequence water and sea ice samples (before incubating them)?
AC - As RC2: The in-situ community was analyzed in parallel with the in-vitro samples. Hence, we had both data at “time zero” and at “time final” of the incubations. We acknowledge this was unclear in the text, and we will work to clarify the potential for divergence between the two communities. Likewise, we refer to the methane oxidation measurements as ‘potential methane oxidation’ as described in Uhlig and Loose (2017) to reflect that the addition of methane and the incubation time can lead to a change in microbial community composition.
The introduction is inconsistent. In L47, the authors promise to give and introduction to microbial metabolisms associated with methane in the marine environment. They start with describing the methane oxidizing taxa, but forgot to mention microbes associated to methanogenesis. In the next paragraph, methanogenesis is subject, but only in context with environmental drivers. I would like to learn more about what is known about the community structure of methane producers in the ecosystem the study is focusing on. On the other hand, this information might become irrelevant when the molecular analysis doesn´t reveal any microbial taxa that are clearly associated with methanogensis or MOx.
AC: We acknowledge that the introduction diverges somewhat from the eventual results and discussion, and we will endeavor to provide the most relevant background.
In the last paragraph of the introduction, authors promise to “elucidate the methane budget in the NWP”, but the final calculation of the budget for the entire study area or at least for a transect is not part of the manuscript.
AC – as RC1: True, the term “budget” is misleading. We will refer to “quantifying oxidation” as one important term in the methane budget.
Generally, authors should be more consistent with word spelling (e.g. Western-most Station/ Westernmost Station) and abbreviations. In one paragraph the full site names are used, in the next paragraph only IDs. Same applies to the water masses throughout the manuscript. I recommend to use as little abbreviations as possible.
AC: Thanks for this advice. We will be more accurate in the terminology.
L46: Are there more recent studies available?
AC: Yes. For example, Steinle et al. (2015), and Shakhova et al. (2013). We will add them in the text.
L49: I agree that MOx is an important sink for dissolved methane in the water column, but the phrase “over some depth ranges and at some locations” is a bit too simple. MOx is, wherever it happens, an important mechanism to remove CH4 from the environment. Please, be more precise and clarify what you mean with “over some depth ranges”! From shallow shelf to deep ocean can be a range of several 1000 meters. The same applies to the location. Do you mean “some locations” are more relevant for MOx activity than others? If so, why is that? Or are you referring to the limited studies focusing on MOx in the Arctic? Make that clear!
AC: We will rephrase it to make the concept clearer. The sentence referred to the Arctic region, where we have hotspots for methane sink and hotspots for methane source.
L61: Too much of a jump in topic – wonder what the environmental drivers for MOx are.
AC: We will work on making the introduction clearer; we will avoid writing about methane production as not reported in this study.
L85: Microbial community structure as measure for ecosystem states - add a reference! This sentence is a bit lost in the context, since the following paragraph is completely independent of the above-mentioned community structure.
AC: We agree with this comment. The text will be edited.
L88: fix typo “inasmuch”
AC – as RC1: This will be fixed.
L102 - 109: No need to give an overview of the general structure of the manuscript. This paragraph can be deleted.
AC: The paragraph will be removed as suggested.
L114: Could you rephrase it to: “This Channel connects Baffin Bay to the east with the Beaufort Sea to the west.”?
AC: Thanks for the suggestion. We will edit it accordingly.
Fig.1: Why are red dots numbered and yellow dots not?
AC: The red dots showed the ice cores which were named by numbers, whereas the yellow dots showed the seawater samples, which were named by location and sample ID. We will add the CTD station ID on top of the yellow dots to be consistent with the sea ice samples.
L153: “The western part of the CAA is characterized by a more consistent sea-ice coverage” compared to?
AC: We will complete the sentence with “… compared to the eastern side”.
The material and methods part is sometimes too details that makes the manuscript hard to read. Authors should think of either shorten it and refer to references if methods were published elsewhere already and/or moving some lengthily parts to the supplements.
AC – as all referees: The method section will be shortened. We followed published methodologies; hence we will remove the redundant text and cite the existing literature.
L166: “samples were collected in the vicinity of Parry Channel” – were samples taken in the Parry Channel or only in the vicinity of (near to) the Channel. To me it makes a difference.
AC: The samples were taken within Parry Channel, but we also included Jones Sound samples, so it was more accurate to write “in the vicinity of”. We will describe the site locations better in the text.
L176: “Sea ice charts were collected by the Canada ice center” - Why is this relevant?
AC: We used the Canadian Ice Center data to observe the sea ice coverage over time. We can explain this better in the text.
L188: With “in-vitro methane incubations” do you mean the MOx rate measurements mentioned in L186? It is not clear to me where these samples were taken. Be consistent with wording throughout the text.
AC: Correct. We were sampling in parallel: dissolved methane (in-situ), and in-vitro methane (for assessing the methane microbial oxidation rate). We will be more specific in the text and define these terms earlier on in the manuscript.
L191: the sterivex filters were removed from where? from the bags?
AC: The water was drawn from the sterivex filter to transfer DNA onto it. We will be more descriptive in the text.
L200: it´s not relevant at which institution the measurements were done as long as instrument specifications are shown. If you want to give credit to an collaborating institution, do this in the acknowledgements.
AC: We will remove those lines and add them in the acknowledgements.
L207: You tried to identify outliners through other procedures. Want to mention them?
AC – as RC1: Details will be added.
L222: “For the calibration of the instrument, we used additional methane standards.” - this information is irrelevant if you don´t add the name of instrument that was used. I think, you do that at a later point, so this sentence can be removed.
AC: The sentence will be removed.
L229: Again, what is meant by in-situ measurements? Methane concentration measurements? What are the experimental bags? The Incubation experiments? MOx rate measurements? Be consistent with wording used throughout the manuscript.
AC: As aforementioned, we will be more specific in the text.
L275 and the following lines: check subscripts in the formulae and in the text and correct them.
AC: We will do it.
L306: only give the final concentration of NaOH in your samples.
AC: We will do it.
L349: “A third outcome of the incubations can be methane production.” This sounds weird, could you rephrase it?
AC: The sentence will be rephrased.
L356: Why is there a reference? Are data published elsewhere? If you followed a method/protocol published by Uhlig, than make that clear.
AC: Yes, we followed an existing method. We will be clearer in the text.
L357: According to the paragraph in L188-194, samples for molecular analysis were collected via Sterivex filters. Here you are giving two different kits for DNA extraction. Which one was used – the MoBio or the Millipore?
AC: Millipore is the brand of the filters (Line 190), while Qiagen is the brand of the extraction kit (Line 193). Line 357 erroneously refers to MoBio, because MoBio was bought out by Qiagen recently and some material still have the “MoBio” logo on it. We apologize for the confusion.
Did you follow the standard extraction protocol? If yes, then all lines after L359 starting with “without the need for enzymes or hazardous organic chemicals.” and including L368 can be removed. “Inhibitor Removal Technology® (IRT) was included to provide high-quality DNA from all types of water samples, even those containing heavy amounts of contaminants.” Was IRT part of the extraction kit? Or is it something you added to the extraction protocol? If IRT is a regular ingredient of the kit, it´s not worth mentioning it.
AC: For IRT yes, all the technology is included in the kit. We will remove the redundant part.
How was the sequence analysis and taxonomical classification done after receiving the sequencing reads? Which pipeline and reference database were used? On which platform are the raw data stored?
AC: The data were stored at National Center for Biotechnology Information (NCBI BioProject PRJNA718862). We will ensure that this information will be included in the methods with proper data source attribution in acknowledgements or open data statement.
L370: Is the protocol for the library prep. not published elsewhere? If yes, please, give reference and consider to shorten this paragraph and move details into the SUPP.
AC: The protocol was published last year in Kerrigan and D’Hondt (2022). We will refer to it and shorten the paragraph.
L392: define SA and apply superscript to d18O
AC: We will do it.
L419: Space missing
AC: We will fix it.
Fig.4: T and S define as temperature and salinity instead
AC – as RC1: We will do it.
Fig.6: It´s hard to distinguish between different green shades. Could you apply a better color scale?
AC: We will do it.
The results part contains detailed discussion already e.g. L444, 457, 460, 496, 503….especially in 3.4., most of the results are already discussed (L503 and L511 – 524).
AC: We will work on better discriminate between the results and the discussion.
Tab.2: Could be moved to the SUPP, since data are shown in Fig.7. L480: apply subscript to kox, remove your personal note! Fig.7: you could apply a longitude color scaling to this figure, too, to indicate sampling sites. Or add IDs.
AC – Table 2 will be moved to Supplemental material and Figure 7 will be re-edited with a color scale showing the longitude, as suggested.
L532: redundant information - already mentioned in L529.
AC: The sentence will be removed.
L536: “in the proximity of the Westernmost station.” – could you give a better measure for distances and direction here, please?
AC: We will do it.
L544: Add a measure for “thin first-year ice” like you did in L546. How thin was it?
AC: We will do it.
Fig.8: This figure only shows results of core 1 and 2. Why are data from core 3,4, and 5 not shown? Were can I find those profile data? (BTW it´s not obverse at the first sight that this data belong to core 1 and 2 – I suggest to change the heading of each plot from just “1” and “2” to “Core 1” and “Core 2”).
AC – as RC1: We usually prefer to show a few panels per figure in the manuscript, for a better visualization. We can certainly add all cores data in the supplemental material. We will edit the headers to make them clearer.
L562: “Here, we also recorded higher methane microbial oxidation rates, likely associated with Pacific-origin microbes and with the seasonal biology.” - I don´t understand where this assumption comes from.
AC – as RC1: The sentence will be revised.
L569: Only two references here? this suggests that there are only two studies available!, but it´s not true, there are more than only two studies of MOx in Arctic marine environments that are worth mentioning here. L576: Again, only two references for a general statement – add “e.g.” in front of the references mentioned and use references which give the best example for underlining your statement.
AC: We apologize, we forgot to add “e.g.,”.
Fig.9: 592: brackets missing, L594: can´t find any labels above dots in the figure.
AC – as all referees: The figure will be edited.
L601: define DWH.
AC: We will do it.
Fig.10: It´s called Prins Karls Forland (L633). What does NPP mean?
AC: Northwest Passage Project, we will add the full name.
L652: What is MW and SIM? Define it. It gets too confusing with water mass and site ID abbreviations.
AC: Meteoric water and sea ice meltwater. We will avoid using abbreviation to make it clearer for the reader. Thanks for the advice.
L669: What´s data CB?
AC: We missed the term “from” Croker Bay.
L670: Check the display of your references! This applies to the entire manuscript!
AC: We will do it.
Fig.11: What are MP results?
AC: Multiparameter analysis (MP). We will add it.
L706: What is meant by “weak methane metabolism”? Better give ranges that indicate “weak” and “stronger” activities.
AC: We will do it.
L715: “the greatest sea ice cover” compared to?
AC: Compared to East.
Fig.13: Add abbreviation (SIC) behind “sea ice concentrations”. What does “Kox averaged by CTD” mean? Is it the average value of all depth profile measurements at one site?
AC: Correct.
L763: Add references that show that Aurantivirga are associated with sediments.
AC: We will do it.
L767: Is there any study that confirms that Chloroplast sequences from V4-V5 region were used for environmental prediction of bloom scenarios?
AC: We are not aware of any published studies confirming this; however, we know that there are some works looking at chloroplasts from 16S data. We will correct line 766 in order to avoid any confusion.
L792 – 797: This statement was concluded in the previous sentences, no need to summarize it again.
AC: Thanks for the suggestion, we will remove it.
It is not necessary to mention the name of the research vessel every time when something is done onboard.
AC: We will remove the name when superfluous.
Citation: https://doi.org/10.5194/egusphere-2023-74-AC3
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AC3: 'Reply on RC3', Alessandra D'Angelo, 18 Mar 2023
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RC4: 'Comment on egusphere-2023-74', Anonymous Referee #4, 17 Mar 2023
The study presents a dataset including seawater salinity, nutrients, methane concentration and isotopic ratios in seawater and ice, and calculations of methane oxidation rates and constants. The nutrient data are not discussed in the context of the other data. Announced as thermohaline data in the abstract, I missed temperature data and found the usage of the salinity data disappointing.
The authors argue for higher methane oxidation in surface water than in deeper waters, based on rate measurements. However comparing the isotopic ratios coupled to the “in situ” concentrations reveals a pattern in contradiction to this statement. The low concentration paired with 13C-enriched ratios in “deeper waters” refers rather to methane oxidation therein than in “surface waters” where higher concentrations are paired with 13C-depleted ratios (compared to each other).
These discrepancies in the outcomes when using rate measurements from experiments and data from “in situ” measurements needs to be discussed as both are relevant for the evaluation of methane oxidation.
In general the discussion of the isotopic data is too weak and partly wrong. Figure 6 gives the relationship between concentrations and isotopic ratios. The regression line is used to argue for methane oxidation. However, to calculate the oxidation by those data a Rayleigh fraction calculation is mandatory (Whiticar, 1999). Just by eye I postulate a Rayleigh oxidation curve fitting to the dark green dots (the “deepest” water, i.e. the water with the highest salinity). Hence, reflected by the most 13C-enriched methane (related to the whole data set given in this paper) clear evidences for methane oxidation in this water mass are given. But unfortunately these data are not discussed in context to methane oxidation.
The discussion starts with: “...dissolved methane showed a vertical stratification with methane excess mostly recorded in shallow waters...”, so far so good but in summer the water masses discussed in this paper are stratified as well, clearly seen by the large gradient in salinity (Fig 5 salinity: 27.5-32.5). However this circumstance is not even mentioned nor considered in the discussion of the data. The discussion ignores the potential link of methane excess to the water stratification. Therefore the methane data are not discussed in context with oceanographic data or how it is promised in the abstract “paired with “thermohaline data”.
In Fig 6 the regression line covers the whole water column, i.e. surface water to deep water, just weakly distinguished by slightly different colored green points. However, due to the water stratification the vertical exchange is rather low. While the surface water is mostly locally affected by sea ice melt, the “deeper” water mass is most likely transported by currents. This circumstance needs to be considered in the discussion because of the different water “history” also the “history” of methane incorporated in each of those water masses is different. Therefore the regression line covering all water masses is not the right tool to say anything about oxidation.
In line 540 the authors promise to be able to identify the role of sea ice playing on the methane cycle. Unfortunately beside a short description of the status quo concerning the saturation level within sea ice nothing followed to convince me that this question is really answered.
Abstract:
It is not clear to me which data the statement: “quickly oxidized by microbes” is based on (last line in the abstract). The isotopic signature (13C-depleted or vice versa 12C-enriched) rather points to a missing oxidation in surface water.
212
Fig 2: the axis legend is too small
line 425: not clear to me what a... “seawater equilibrium supersaturation “... means,
line 426: Does 3.42 nM mean the atmospheric equilibrium in surface water?
line 426: It is also not clear to me which atmospheric methane concentration the calculation of the equilibrium is based on.
line 429: if fig 4 does not show a clear trend the question arises if this kind of figure is useful?
line 452-455: should be shifted before line 426
line 445 ... which is a clear evidence for water stratification
line 462: the isotopic ratios in the range of low concentration rather reflects an oxidation effect than a source effect (suggest to calculate a Rayleigh curve)
Fig 5: values in surface water don’t refer to methane oxidation
Fig 7: Methane discussed in the context of this paper is never abiotic
line 527: not clear to me on which calculation these numbers are based on
Unclear to me where the high methane concentration in sea ice might come from. Also, if we assume a methane production therein, a storage during the melt season therein is unlikely. While numbers of the brine volume fraction are missing I assume, when the bulk salinity (I assume here the bulk salinity is meant) is just 2, brine is nearly completely lost by melt. If so it remains an open question where within ice the high methane concentration might be localized. Rather it seems that the difference in concentration between seawater and sea ice is an “artefact” by the “salinity effect” of the calculation of concentration. Further” “contamination” during melt by flushing with seawater is likely. Also the coring procedure itself might contaminate melted ice cores with seawater.
line 539: which physical-chemical parameters are meant?
Fig 12: the white dots are too small.
line 730: ...”released the gas...” you mean the release of dissolved methane by brine ? needs clarification
line 740: what is meant with methane gas (dissolved or gaseous methane) ?
Citation: https://doi.org/10.5194/egusphere-2023-74-RC4 -
AC4: 'Reply on RC4', Alessandra D'Angelo, 18 Mar 2023
Dear Referee 4, thanks for the comments. We appreciate the time and effort that you and the reviewers dedicated to providing constructive feedback on our manuscript. Your insightful comments suggested valuable improvements to our paper. Below you can find our replies (Author Comment - AC).
The study presents a dataset including seawater salinity, nutrients, methane concentration and isotopic ratios in seawater and ice, and calculations of methane oxidation rates and constants. The nutrient data are not discussed in the context of the other data. Announced as thermohaline data in the abstract, I missed temperature data and found the usage of the salinity data disappointing.
AC: The nutrient data were used as ancillary data supporting the methane data, and we used this data in the multiparameter analysis to detect the water mass contribution. We acknowledge that the structure of the manuscript can be misleading, so we will edit it. The temperature data, together with the entire dataset, can be found in the Arctic Data Center DOI provided in the text.
The authors argue for higher methane oxidation in surface water than in deeper waters, based on rate measurements. However comparing the isotopic ratios coupled to the “in situ” concentrations reveals a pattern in contradiction to this statement. The low concentration paired with 13C-enriched ratios in “deeper waters” refers rather to methane oxidation therein than in “surface waters” where higher concentrations are paired with 13C-depleted ratios (compared to each other).
These discrepancies in the outcomes when using rate measurements from experiments and data from “in situ” measurements needs to be discussed as both are relevant for the evaluation of methane oxidation.
AC: The methane data measured in in-situ waters describe past processes, while the in-vitro experiments provide information of the present environment. The in-situ low concentration paired with 13C-enriched ratios in deeper waters suggested methane microbial oxidation during the past.
In general the discussion of the isotopic data is too weak and partly wrong. Figure 6 gives the relationship between concentrations and isotopic ratios. The regression line is used to argue for methane oxidation. However, to calculate the oxidation by those data a Rayleigh fraction calculation is mandatory (Whiticar, 1999). Just by eye I postulate a Rayleigh oxidation curve fitting to the dark green dots (the “deepest” water, i.e. the water with the highest salinity). Hence, reflected by the most 13C-enriched methane (related to the whole data set given in this paper) clear evidences for methane oxidation in this water mass are given. But unfortunately these data are not discussed in context to methane oxidation.
AC – as RC2: Figure 6 shows the relationship between the in-situ methane concentrations and isotopic ratio. We used this figure to show that the water column likely experienced methane microbial oxidation in the past. This was a simplified version of the Rayleigh distillation model as in Fenwick et al. (2017), Figure 14 (https://agupubs.onlinelibrary.wiley.com/doi/full/10.1002/2016JC012493).
The discussion starts with: “...dissolved methane showed a vertical stratification with methane excess mostly recorded in shallow waters...”, so far so good but in summer the water masses discussed in this paper are stratified as well, clearly seen by the large gradient in salinity (Fig 5 salinity: 27.5-32.5). However this circumstance is not even mentioned nor considered in the discussion of the data. The discussion ignores the potential link of methane excess to the water stratification. Therefore the methane data are not discussed in context with oceanographic data or how it is promised in the abstract “paired with “thermohaline data”.
AC: In the paragraph 1.2 we described the water column structure characterizing the Canadian Arctic Archipelago waters during the summer (lines 146 – 152) and we referred to the stratification of the water column in Figure 12. We think that the multiparameter analysis (MP) was a better way to map the water masses within our area of study. The salinity data were used in the MP analysis for the detection of the water masses and the results were discussed paired to the methane data. We take the referee’s critique, and we will make it clearer in the revised manuscript.
In Fig 6 the regression line covers the whole water column, i.e. surface water to deep water, just weakly distinguished by slightly different colored green points. However, due to the water stratification the vertical exchange is rather low. While the surface water is mostly locally affected by sea ice melt, the “deeper” water mass is most likely transported by currents. This circumstance needs to be considered in the discussion because of the different water “history” also the “history” of methane incorporated in each of those water masses is different. Therefore the regression line covering all water masses is not the right tool to say anything about oxidation.
AC: As aforementioned, we used this figure to show that the water column likely experienced methane microbial oxidation in the past. The purpose of this figure was to provide insight about the processes occurred during the past rather than the significative relationship between the methane concentration and isotope ratio of the present. We acknowledge that this was not clear in the text, and we will work on strengthening this point.
In line 540 the authors promise to be able to identify the role of sea ice playing on the methane cycle. Unfortunately beside a short description of the status quo concerning the saturation level within sea ice nothing followed to convince me that this question is really answered.
AC: In paragraph 4.4 we described the influence of the sea ice on the collected methane data. Because it was a summer campaign, we did not expect great impact of the sea ice on the seawater methane. Few stations were ice covered and we described the outcome both in the text and in Figure 13.
Abstract:
It is not clear to me which data the statement: “quickly oxidized by microbes” is based on (last line in the abstract). The isotopic signature (13C-depleted or vice versa 12C-enriched) rather points to a missing oxidation in surface water.
AC: The results of the in-vitro experiment suggested higher methane oxidation rates in shallow and Pacific-dominated waters. The in-situ isotopic signature describes past processes occurred in the water column.
Fig 2: the axis legend is too small
AC: We will fix it
line 425: not clear to me what a... “seawater equilibrium supersaturation “... means,
AC: “equilibrium” is a typo. It will be removed. Thanks for noticing it.
line 426: Does 3.42 nM mean the atmospheric equilibrium in surface water?
line 426: It is also not clear to me which atmospheric methane concentration the calculation of the equilibrium is based on.
AC: We use the Bunsen coefficient for the gas solubility to calculate the atmospheric methane concentration at in-situ temperature and salinity. The link to the code for the calculation is in line 248.
line 429: if fig 4 does not show a clear trend the question arises if this kind of figure is useful?
AC: Figure 4 is meant to show all the methane concentrations expressed as saturation anomalies. This provides important information even if not showing a spatial trend.
line 452-455: should be shifted before line 426
AC: We will edit it
line 445 ... which is a clear evidence for water stratification
line 462: the isotopic ratios in the range of low concentration rather reflects an oxidation effect than a source effect (suggest to calculate a Rayleigh curve).
Fig 5: values in surface water don’t refer to methane oxidation
AC: As aforementioned, the methane data measured in in-situ waters describe past processes, while the in-vitro experiments provide information of the present environment. The in-situ low concentration paired with 13C-enriched ratios in deeper waters suggested methane microbial oxidation during the past.
Fig 7: Methane discussed in the context of this paper is never abiotic.
AC: During the in-vitro experiments, we recorded flat trend of methane concentrations and isotope ratio over time in two samples (shown in fig.7), suggesting methane abiotic. We did not take these values into account for the microbial methane oxidation rates, to not bias the results.
line 527: not clear to me on which calculation these numbers are based on
AC: Methods are described in paragraph 2.3.
Unclear to me where the high methane concentration in sea ice might come from. Also, if we assume a methane production therein, a storage during the melt season therein is unlikely. While numbers of the brine volume fraction are missing I assume, when the bulk salinity (I assume here the bulk salinity is meant) is just 2, brine is nearly completely lost by melt. If so it remains an open question where within ice the high methane concentration might be localized. Rather it seems that the difference in concentration between seawater and sea ice is an “artefact” by the “salinity effect” of the calculation of concentration. Further” “contamination” during melt by flushing with seawater is likely. Also the coring procedure itself might contaminate melted ice cores with seawater.
AC: The salinity of the ice cores felt in a range of 0.5 and 3.5. We believe that the brine rejection was negligible at that time. We suggest that the methane excess in the sea ice was due to past freezing processes and that the increase of ice permeability influenced the methane enrichment within the underneath seawater and, in turn, methane depletion within the sea ice. We recognize that during the sampling process there could be seawater contamination, but we exclude that this could have affected all the sea ice results.
line 539: which physical-chemical parameters are meant?
AC: We measured: temperature, salinity, δ18O, δD, [CH4], δ13CH4. We can add this information in the text.
Fig 12: the white dots are too small.
AC: The white dots indicate the data points, so we prefer to keep them small in order to highlight the outcomes of the figure.
line 730: ...”released the gas...” you mean the release of dissolved methane by brine ? needs clarification
line 740: what is meant with methane gas (dissolved or gaseous methane) ?
AC: We mean the release of dissolved methane through the permeability of the sea ice.
Citation: https://doi.org/10.5194/egusphere-2023-74-AC4
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AC4: 'Reply on RC4', Alessandra D'Angelo, 18 Mar 2023
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