the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 02 Feb 2023
Evidence of deep subsurface sulfur cycle in a sediment core from eastern Arabian Sea
Abstract. Anaerobic microbial sulfate reduction and oxidative sulfur cycling have been studied in long sediment cores mainly acquired as part of IODP explorations. The most remarkable observation in many of these studies is the existence of an active sulfur cycle in the deep subsurface sediments that have very low organic carbon content and are presumably refractory. Here we investigate the interstitial sulfate concentrations and sulfur isotope ratios in a 290 m long core collected from the eastern Arabian Sea at a water depth of 2663 m. Continuous decrease in pore water-sulfate concentrations with depth (up to 75 mbsf) coupled with enrichment in δ34SSO4 values suggests organoclastic sulfate reduction (OSR) processes attributed to the activity of sulfate-reducing bacteria (SRB) and retention of labile organic substrates amenable to the SRBs. Below a depth of 75 mbsf, the absence of a further reduction in sulfate concentrations indicates insufficient labile substrate to drive SRB. An increase in sulfate concentrations at the deeper subsurface (below 128.5 mbsf) coupled with decreasing δ34SSO4 values may be attributed to a ferric-oxyhydroxide driven oxidation of Fe-sulfide. This study reveals that even under deep aerobic water columns, organic matter may continue to be a source of labile organic substrates at significantly deeper subsurface. Enhanced sulfate concentrations in the deeper depths may be attributed to the oxidation of sulfides via ferric-oxyhydroxides buried deep within the sediment. A microbiological investigation may reveal further details of the sulfur cycle at the deep surface.
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Interactive discussion
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RC1: 'Comment on bg-2023-3', Anonymous Referee #1, 02 Mar 2023
Dear authors, dear editor,
Please find below my review for the submitted manuscript entitled “Evidence of deep subsurface sulfur cycle in a sediment core from eastern Arabian Sea” by Dr. Aninda Mazumdar and collaborators.
I hope they will be useful to the authors.
Best regards------------------------------------------------------------------------------------------------------------------
In the submitted manuscript, the author investigated the sulfur cycling in a 290-meter-long core collected from the eastern Arabian Sea. They investigated the porewater sulfate concentration, sulfate sulfur isotopic compositions, total organic matter, alkalinity etc to evaluate the (bio)geochemical processes during the early diagenesis. Based on the decrease in porewater sulfate and increase in sulfur isotopic composition, they suggested that organoclastic sulfate reduction can exist in the top 75 meters sediments. Further down, patterns of increased sulfate concentration and decreased sulfur isotope compositions were observed, which were interpreted as the results of iron sulfide oxidation in iron oxide rich environments. Overall, the research topic, exploring the sulfur cycle in deep subsurface marine sediments, is of high interest and suits the research topic of this journal. The explanation of OSR in the top sediment is convincing, but the interpretation on the iron oxide-driven Fe sulfide oxidation is speculative. Some points in the discussion need to be strengthened to make a more compelling story.
Mainpoints:
In fact, as mentioned in the introduction, other possibilities (e.g., seawater intrusion through deep cracks, deeper brine flux) can cause the anomalous sulfate concentrations and isotope pattern in porewater at deeper sediments. Consider to evaluate any possibility for your case.
I think a key evidence might come from the iron sulfide (e.g., pyrite) in the sediments.
Can you observe depletion of iron sulfide contents and enrichment of iron oxides if the oxidation of iron sulfide was the main processes in deep sediments?
What is the sulfur isotope composition of iron sulfide? Can they be low enough to lower the d34S of porewater sulfate?
Please note that sulfate sulfur isotope composition is still higher than the seawater sulfate value (~21 permill). An seawater-like fluid intrusion might lead to similar porewater patterns.
The interpretation of high alkalinity in most deep sediment need to be considered further.
Abstract:
Lines 30-31: “Enhanced sulfate concentrations …… via ferric-oxyhydroxides buried deep within the sediment” – repetition with the sentence abovd starting from Line 25 “An increase in sulfate concentrations at deeper … a ferric-oxyhydroxide driven oxidation of Fe-sulfide”.
Introduction:
Line 40: Mn reduction should come prior to Fe reduction. Change the positions of Mn4+ and Fe3+.
Line 46: Correct order.
Line 72: The reason for the depletion of sulfate within SMTZ could also be result from sulfate-driven anaerobic oxidation of methane.
Line 182: Regarding to Fe-sulfide formation, the absence of H2S suggest a hydrogen sulfide-limited and iron-rich environment.
Line 186: It is useful that the author can provide more details about the pyrite formation in the sediments. For example, the distributional pattern and sulfur isotopic composition (if they existed).
Line 197-199: Or there is additional sulfate input.
Line 203: Can you add some pictures of iron oxide aggregates or gypsum into the manuscript? This might help to strength your point.
Line 210-212: If the elevated alkalinity was due to the carbonate dissolution, one would expect a decreased, rather than an increased calcium carbonate content. You might better describe the background of sediment at the beginning. Can you observe some changes of the sedimentary phase in different zones (I - IV)?
Line 244-245: How to explain the variation of organic matter in the sediment? In addition to OSR, can it affect by the dynamic of productivity in the water column?
Line 246: I agree the OSR in the top 75 m sediment. However, the interpretation on the iron oxide-driven Fe sulfide oxidation is speculative. For example, a deep crack lead to instruction of seawater in deeper sediment, or deeper brine fluid might also lead to the similar patterns. These hypotheses might not be answered in the end, but at least they should be evaluated.
Citation: https://doi.org/10.5194/bg-2023-3-RC1 -
RC2: 'Comment on bg-2023-3', Anonymous Referee #2, 17 Mar 2023
Thank you for submitting your manuscript to Biogeosciences. This study explains the anomalous SO42- concentrations and δ34SSO4 profiles in the interstitial waters in a long sediment core to discuss sulfur cycle. But, after careful evaluation, I regret to inform you that there are some problems with your manuscript, and it needs to be rejected.
- The abstract is a brief introduction to the full text. First, you should briefly introduce the research background and limitations of your current study, and then introduce your work. In addition, the sulfate concentrations and sulfur isotope ratios were introduced in the abstract, and the explanation were showed. But I think these reasons are over-stated because there is lack of evidence.
- The introduction should try to quote the domestic and foreign scientific and technological papers published in the last 5 years. In addition, explain their importance, mention the past work that has tried to solve or answer the research question, and finally conclude with a clear research objective. Besides, Geology section is redundant, and should be simplified.
- In general, the description of material methods is not clear and rigorous enough, there is a lack of explanation of scientific and replicates methods used in the study: (a) Study site and sample collection: latitude and longitude information, sampling depth, sample number, biological repetition, etc., should be accurately described. I have another concern, what is the significance of analyzing sediment core? In my opinion, the authors need to clarify the vertical interactions of these parameters (SO42-, ions, TOC, etc.). (b) Biogeochemical analysis methods are best described together. Why is the δ34SSO4 values measured?
- In Results and Discussion, I think the main problem is that some explanation is lack of evidence. For example, OSR processes attributed to the activity of sulfate-reducing bacteria, but SRB was not analyzed in this manuscript; decreasing d34SSO4 values may be attributed to a ferric-oxyhydroxide driven oxidation of Fe-sulfide, which is also the speculation.
Citation: https://doi.org/10.5194/bg-2023-3-RC2 -
EC1: 'Comment on bg-2023-3', Tina Treude, 31 Mar 2023
Dear Dr. Peketi, Dr. Mazumar, and Co-Workers,
we received the third official review of your manuscript (Anonymous Referee #3) past the discussion deadline due to unforeseen circumstances. I am providing the review below. Please consider the review for the revision of your manuscript. You can post your response directly below my editor's comment.
The authors present pore-water data and solid-phase total organic carbon contents of an about 290 m long sediment core retrieved from the eastern Arabian Sea during an IODP expedition with RV JOIDES RESOLUTION in 2006. Besides the pore-water data that have been aquired directly on board, the authors present pore-water concentrations and the stable sulfur isotopic composition (d34S) of sulfate. The main goal of this study is to explain the observed „anomalous“ profile shapes of pore-water sulfate concentrations and d34S values.
I was surprised to see that other important pore-water constituents – like hydrogen sulfide and Fe2+ - and in particular solid-phase data on Fe oxide and Fe sulfide mineral phases in the solid phase are missing. These data are crucial to support the discussion of the potential factors and depositional/geochemical conditions most likely explaining the observed pore-water profiles of sulfate and the d34S-sulfate. Without these important data the interpretation of the pore-water data and the discussion of possible drivers responsible for the observed distribution patterns remain absolutely speculative. While reading the manuscript, I understood that hydrogen sulfide was measured but not detectable. Based on this, I assume that free Fe2+ is present in at least some of the units of the core. These data should definitely be shown. Even more important is to include solid-phase Fe data. The authors mentioned that these have been published by Collett et al. (2008) and are thus available.
The authors should also consider and discuss the potential impact of temporal changes in depositional and geochemical conditions at the study site – including rates of sedimentation, bioturbation and organic carbon burial as well as fluctuations in the type of plankton remains arriving at the seafloor. What about changes in bottom-water oxygen in the past? Is there anything known about past changes in bottom-water oxygen concentrations in the study area? Previous studies such as those by Wehrmann et al. (2013; GCA) and Köster et al. (2021;G3) have demonstrated that such changes can significantly modulate pore-water signatures – besides sediment depth-related changes in sulfate reduction and sulfide oxidation. In this light the observed shapes of the concentration profiles of sulfate and d34S of sulfate may certainly not be as unusual or „anomalous“ as stated by the authors.
Based on these considerations and my further comments given below I regret to say that I cannot recommend publication of this manuscript in it’s present form. However, I would strongly encourage the authors to include further key dissolved and solid-phase data (in particular Fe oxide and sulfide mineral phases) into their study. I am convinced that based on these additional data sets the authors should be able to come up with a more in-depth discussion and a much better supported interpretation.
Specific comments
Title: I would suggest the following: „Evidence for deep subsurface sulfur cycling in sediments of the eastern Arabian Sea“
Abstract:
I do not agree with the statement in the first sentence of the abstract. Prior to detailed investigations of sulfur cycling in deeper subsurface sediments performed in the framework of ODP/IODP there has been a wealth of studies investigating the biogeochemical cycling of sulfur using surface sediments and cores of up to 10 to 15 m length collected by gravity coring. In this context I would particularly bring your attention to the extensive and groundbreaking work by Bo Barker Jørgensen and his group since the early 1970s – including work in the North Sea, the Skagerrak/Kattegat, the Baltic Sea, the Black Sea as well as the continental shelves underlying the high productivity areas off Chile/Peru and Namibia (Jørgensen 1977, 1982; Jørgensen et al., XXXX, Treude et al., 2005; etc.) only to mention a few. Work on sulfur cycling in subsurface sediments low in OC content and reactivity has also been performed in sediments of the Argentine/Uruguayan Margin and the Nankai Trough (Hensen et al., 2003; Riedinger et al., 2010, 2017). You also cite some of these studies.
Lines 23/24: What precisely do you mean with „retention“ and „amenable“ in this context? Not clear to me. Please, specify.
L. 29: This part of the sentence sounds a bit odd. Please, rephrase.
L. 40: Please, cite the intial studies by Froelich et al. (1979) and Berner (1980) here.
Ls. 40/41: What precisely do you mean with „degenerated“ and „reorganized“ organic particulates?
L. 45: „fuel“ instead of „fuels“
Pages 3 and 4: In this part of the introduction the authors give an rather broad overview of potential substrates for and microbial pathways/drivers of sulfate reduction. However, in their manuscript they do not present any related organic geochemical or microbiological data. So, I was wondering why they put so much emphasis on these issues in the introduction (and also in some parts oft he discussion) if they do not have data to later properly discuss this.
Ls. 72/73: Wording is odd. Sulfate concentration profile „is accompanied by“?!
Ls. 162 ff.: The authors suggest sulfide oxidation but show neither pore-water hydrogen sulfide concentration nor the distribution of different Fe oxide or sulfide mineral phases within the sediments. Moreover, do you mean oxidation of dissolved hydrogen sulfide or solid-phase Fe sulfides?! Not clear as it stands here.
L. 174: „major“ instead of „most critical“
L. 175: of „a“ chloride anomaly
L. 178: Not clear what you mean with „HS-/H2S phase“ here?! I guess, you mean pore water. But if yes, why do you speak of a „phase“?!
Ls.: Please, also consider the work by Torres et al. (1996) and other earlier studies here. Böttcher et al. (2004) are certainly not the first who have observed and published this.
Ls. 181 ff.: Here you mention for the first time that hydrogen sulfide in pore-water was not detected. So, it has obviously been measured and should thus also be part of the „Methodology“.
Ls. 185/186: Only mentioning that pyrite was detected in the sediments retrieved by this core does not make much sense. I would suggest to definitely show the distribution of pyrite (and other Fe sulfide phases – as e.g. AVS) published by Collett et al. (2008) over depth along with the other data produced in the framework of this study.
Ls. 187 ff.: Also here, the authors expand on substrates used in OSR – however, they do not show any related data.
L. 200: „retention“ ?
General comments/remarks
The English language needs considerable overhaul and polishing. I would strongly suggest to ask an English native speaker to check any new version of the manuscript. I have only corrected a few flaws – however, it is the task of the authors to take care of proper English language.
It is not modern practice and state-of-the-art to only list data in the form of tables. In order to agree with the guidelines of good scientific practice and the international FAIR principles and in this way ensure accessibility and longterm-storage of scientific data, the authors should submit their data to an international data portal and include the doi of this data set in the manuscipt.
It would have been important to also show the pore-water profiles of hydrogen sulfide and Fe2+. The authors are also not presenting any solid-phase data which would have considerably enhanced the interpretation of the pore-water sulfate and the stable sulphur isotopic signatures of sulfate. You even mention that pore water was retrieved under anoxic conditions to avoid oxidation of hydrogen sulfide. So, I assume that pore-water HS data are available. Only later in the discussion one reads that HS was not detectable.
Citation: https://doi.org/10.5194/bg-2023-3-EC1
Interactive discussion
Status: closed
-
RC1: 'Comment on bg-2023-3', Anonymous Referee #1, 02 Mar 2023
Dear authors, dear editor,
Please find below my review for the submitted manuscript entitled “Evidence of deep subsurface sulfur cycle in a sediment core from eastern Arabian Sea” by Dr. Aninda Mazumdar and collaborators.
I hope they will be useful to the authors.
Best regards------------------------------------------------------------------------------------------------------------------
In the submitted manuscript, the author investigated the sulfur cycling in a 290-meter-long core collected from the eastern Arabian Sea. They investigated the porewater sulfate concentration, sulfate sulfur isotopic compositions, total organic matter, alkalinity etc to evaluate the (bio)geochemical processes during the early diagenesis. Based on the decrease in porewater sulfate and increase in sulfur isotopic composition, they suggested that organoclastic sulfate reduction can exist in the top 75 meters sediments. Further down, patterns of increased sulfate concentration and decreased sulfur isotope compositions were observed, which were interpreted as the results of iron sulfide oxidation in iron oxide rich environments. Overall, the research topic, exploring the sulfur cycle in deep subsurface marine sediments, is of high interest and suits the research topic of this journal. The explanation of OSR in the top sediment is convincing, but the interpretation on the iron oxide-driven Fe sulfide oxidation is speculative. Some points in the discussion need to be strengthened to make a more compelling story.
Mainpoints:
In fact, as mentioned in the introduction, other possibilities (e.g., seawater intrusion through deep cracks, deeper brine flux) can cause the anomalous sulfate concentrations and isotope pattern in porewater at deeper sediments. Consider to evaluate any possibility for your case.
I think a key evidence might come from the iron sulfide (e.g., pyrite) in the sediments.
Can you observe depletion of iron sulfide contents and enrichment of iron oxides if the oxidation of iron sulfide was the main processes in deep sediments?
What is the sulfur isotope composition of iron sulfide? Can they be low enough to lower the d34S of porewater sulfate?
Please note that sulfate sulfur isotope composition is still higher than the seawater sulfate value (~21 permill). An seawater-like fluid intrusion might lead to similar porewater patterns.
The interpretation of high alkalinity in most deep sediment need to be considered further.
Abstract:
Lines 30-31: “Enhanced sulfate concentrations …… via ferric-oxyhydroxides buried deep within the sediment” – repetition with the sentence abovd starting from Line 25 “An increase in sulfate concentrations at deeper … a ferric-oxyhydroxide driven oxidation of Fe-sulfide”.
Introduction:
Line 40: Mn reduction should come prior to Fe reduction. Change the positions of Mn4+ and Fe3+.
Line 46: Correct order.
Line 72: The reason for the depletion of sulfate within SMTZ could also be result from sulfate-driven anaerobic oxidation of methane.
Line 182: Regarding to Fe-sulfide formation, the absence of H2S suggest a hydrogen sulfide-limited and iron-rich environment.
Line 186: It is useful that the author can provide more details about the pyrite formation in the sediments. For example, the distributional pattern and sulfur isotopic composition (if they existed).
Line 197-199: Or there is additional sulfate input.
Line 203: Can you add some pictures of iron oxide aggregates or gypsum into the manuscript? This might help to strength your point.
Line 210-212: If the elevated alkalinity was due to the carbonate dissolution, one would expect a decreased, rather than an increased calcium carbonate content. You might better describe the background of sediment at the beginning. Can you observe some changes of the sedimentary phase in different zones (I - IV)?
Line 244-245: How to explain the variation of organic matter in the sediment? In addition to OSR, can it affect by the dynamic of productivity in the water column?
Line 246: I agree the OSR in the top 75 m sediment. However, the interpretation on the iron oxide-driven Fe sulfide oxidation is speculative. For example, a deep crack lead to instruction of seawater in deeper sediment, or deeper brine fluid might also lead to the similar patterns. These hypotheses might not be answered in the end, but at least they should be evaluated.
Citation: https://doi.org/10.5194/bg-2023-3-RC1 -
RC2: 'Comment on bg-2023-3', Anonymous Referee #2, 17 Mar 2023
Thank you for submitting your manuscript to Biogeosciences. This study explains the anomalous SO42- concentrations and δ34SSO4 profiles in the interstitial waters in a long sediment core to discuss sulfur cycle. But, after careful evaluation, I regret to inform you that there are some problems with your manuscript, and it needs to be rejected.
- The abstract is a brief introduction to the full text. First, you should briefly introduce the research background and limitations of your current study, and then introduce your work. In addition, the sulfate concentrations and sulfur isotope ratios were introduced in the abstract, and the explanation were showed. But I think these reasons are over-stated because there is lack of evidence.
- The introduction should try to quote the domestic and foreign scientific and technological papers published in the last 5 years. In addition, explain their importance, mention the past work that has tried to solve or answer the research question, and finally conclude with a clear research objective. Besides, Geology section is redundant, and should be simplified.
- In general, the description of material methods is not clear and rigorous enough, there is a lack of explanation of scientific and replicates methods used in the study: (a) Study site and sample collection: latitude and longitude information, sampling depth, sample number, biological repetition, etc., should be accurately described. I have another concern, what is the significance of analyzing sediment core? In my opinion, the authors need to clarify the vertical interactions of these parameters (SO42-, ions, TOC, etc.). (b) Biogeochemical analysis methods are best described together. Why is the δ34SSO4 values measured?
- In Results and Discussion, I think the main problem is that some explanation is lack of evidence. For example, OSR processes attributed to the activity of sulfate-reducing bacteria, but SRB was not analyzed in this manuscript; decreasing d34SSO4 values may be attributed to a ferric-oxyhydroxide driven oxidation of Fe-sulfide, which is also the speculation.
Citation: https://doi.org/10.5194/bg-2023-3-RC2 -
EC1: 'Comment on bg-2023-3', Tina Treude, 31 Mar 2023
Dear Dr. Peketi, Dr. Mazumar, and Co-Workers,
we received the third official review of your manuscript (Anonymous Referee #3) past the discussion deadline due to unforeseen circumstances. I am providing the review below. Please consider the review for the revision of your manuscript. You can post your response directly below my editor's comment.
The authors present pore-water data and solid-phase total organic carbon contents of an about 290 m long sediment core retrieved from the eastern Arabian Sea during an IODP expedition with RV JOIDES RESOLUTION in 2006. Besides the pore-water data that have been aquired directly on board, the authors present pore-water concentrations and the stable sulfur isotopic composition (d34S) of sulfate. The main goal of this study is to explain the observed „anomalous“ profile shapes of pore-water sulfate concentrations and d34S values.
I was surprised to see that other important pore-water constituents – like hydrogen sulfide and Fe2+ - and in particular solid-phase data on Fe oxide and Fe sulfide mineral phases in the solid phase are missing. These data are crucial to support the discussion of the potential factors and depositional/geochemical conditions most likely explaining the observed pore-water profiles of sulfate and the d34S-sulfate. Without these important data the interpretation of the pore-water data and the discussion of possible drivers responsible for the observed distribution patterns remain absolutely speculative. While reading the manuscript, I understood that hydrogen sulfide was measured but not detectable. Based on this, I assume that free Fe2+ is present in at least some of the units of the core. These data should definitely be shown. Even more important is to include solid-phase Fe data. The authors mentioned that these have been published by Collett et al. (2008) and are thus available.
The authors should also consider and discuss the potential impact of temporal changes in depositional and geochemical conditions at the study site – including rates of sedimentation, bioturbation and organic carbon burial as well as fluctuations in the type of plankton remains arriving at the seafloor. What about changes in bottom-water oxygen in the past? Is there anything known about past changes in bottom-water oxygen concentrations in the study area? Previous studies such as those by Wehrmann et al. (2013; GCA) and Köster et al. (2021;G3) have demonstrated that such changes can significantly modulate pore-water signatures – besides sediment depth-related changes in sulfate reduction and sulfide oxidation. In this light the observed shapes of the concentration profiles of sulfate and d34S of sulfate may certainly not be as unusual or „anomalous“ as stated by the authors.
Based on these considerations and my further comments given below I regret to say that I cannot recommend publication of this manuscript in it’s present form. However, I would strongly encourage the authors to include further key dissolved and solid-phase data (in particular Fe oxide and sulfide mineral phases) into their study. I am convinced that based on these additional data sets the authors should be able to come up with a more in-depth discussion and a much better supported interpretation.
Specific comments
Title: I would suggest the following: „Evidence for deep subsurface sulfur cycling in sediments of the eastern Arabian Sea“
Abstract:
I do not agree with the statement in the first sentence of the abstract. Prior to detailed investigations of sulfur cycling in deeper subsurface sediments performed in the framework of ODP/IODP there has been a wealth of studies investigating the biogeochemical cycling of sulfur using surface sediments and cores of up to 10 to 15 m length collected by gravity coring. In this context I would particularly bring your attention to the extensive and groundbreaking work by Bo Barker Jørgensen and his group since the early 1970s – including work in the North Sea, the Skagerrak/Kattegat, the Baltic Sea, the Black Sea as well as the continental shelves underlying the high productivity areas off Chile/Peru and Namibia (Jørgensen 1977, 1982; Jørgensen et al., XXXX, Treude et al., 2005; etc.) only to mention a few. Work on sulfur cycling in subsurface sediments low in OC content and reactivity has also been performed in sediments of the Argentine/Uruguayan Margin and the Nankai Trough (Hensen et al., 2003; Riedinger et al., 2010, 2017). You also cite some of these studies.
Lines 23/24: What precisely do you mean with „retention“ and „amenable“ in this context? Not clear to me. Please, specify.
L. 29: This part of the sentence sounds a bit odd. Please, rephrase.
L. 40: Please, cite the intial studies by Froelich et al. (1979) and Berner (1980) here.
Ls. 40/41: What precisely do you mean with „degenerated“ and „reorganized“ organic particulates?
L. 45: „fuel“ instead of „fuels“
Pages 3 and 4: In this part of the introduction the authors give an rather broad overview of potential substrates for and microbial pathways/drivers of sulfate reduction. However, in their manuscript they do not present any related organic geochemical or microbiological data. So, I was wondering why they put so much emphasis on these issues in the introduction (and also in some parts oft he discussion) if they do not have data to later properly discuss this.
Ls. 72/73: Wording is odd. Sulfate concentration profile „is accompanied by“?!
Ls. 162 ff.: The authors suggest sulfide oxidation but show neither pore-water hydrogen sulfide concentration nor the distribution of different Fe oxide or sulfide mineral phases within the sediments. Moreover, do you mean oxidation of dissolved hydrogen sulfide or solid-phase Fe sulfides?! Not clear as it stands here.
L. 174: „major“ instead of „most critical“
L. 175: of „a“ chloride anomaly
L. 178: Not clear what you mean with „HS-/H2S phase“ here?! I guess, you mean pore water. But if yes, why do you speak of a „phase“?!
Ls.: Please, also consider the work by Torres et al. (1996) and other earlier studies here. Böttcher et al. (2004) are certainly not the first who have observed and published this.
Ls. 181 ff.: Here you mention for the first time that hydrogen sulfide in pore-water was not detected. So, it has obviously been measured and should thus also be part of the „Methodology“.
Ls. 185/186: Only mentioning that pyrite was detected in the sediments retrieved by this core does not make much sense. I would suggest to definitely show the distribution of pyrite (and other Fe sulfide phases – as e.g. AVS) published by Collett et al. (2008) over depth along with the other data produced in the framework of this study.
Ls. 187 ff.: Also here, the authors expand on substrates used in OSR – however, they do not show any related data.
L. 200: „retention“ ?
General comments/remarks
The English language needs considerable overhaul and polishing. I would strongly suggest to ask an English native speaker to check any new version of the manuscript. I have only corrected a few flaws – however, it is the task of the authors to take care of proper English language.
It is not modern practice and state-of-the-art to only list data in the form of tables. In order to agree with the guidelines of good scientific practice and the international FAIR principles and in this way ensure accessibility and longterm-storage of scientific data, the authors should submit their data to an international data portal and include the doi of this data set in the manuscipt.
It would have been important to also show the pore-water profiles of hydrogen sulfide and Fe2+. The authors are also not presenting any solid-phase data which would have considerably enhanced the interpretation of the pore-water sulfate and the stable sulphur isotopic signatures of sulfate. You even mention that pore water was retrieved under anoxic conditions to avoid oxidation of hydrogen sulfide. So, I assume that pore-water HS data are available. Only later in the discussion one reads that HS was not detectable.
Citation: https://doi.org/10.5194/bg-2023-3-EC1
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