Influence of manganese cycling on alkalinity in the redox stratified water column of Chesapeake Bay

Thibault de Chanvalon, Aubin; Luther, George W.; Estes, Emily R.; Necker, Jennifer; Tebo, Bradley M.; Su, Jianzhong; Cai, Wei-Jun

doi:https://doi.org/10.5194/bg-20-3053-2023

Articles | Volume 20, issue 14

https://doi.org/10.5194/bg-20-3053-2023

© Author(s) 2023. This work is distributed under
the Creative Commons Attribution 4.0 License.

https://doi.org/10.5194/bg-20-3053-2023

© Author(s) 2023. This work is distributed under
the Creative Commons Attribution 4.0 License.

Articles | Volume 20, issue 14

Research article

|

31 Jul 2023

Research article |

| 31 Jul 2023

Influence of manganese cycling on alkalinity in the redox stratified water column of Chesapeake Bay

Aubin Thibault de Chanvalon, George W. Luther, Emily R. Estes, Jennifer Necker, Bradley M. Tebo, Jianzhong Su, and Wei-Jun Cai

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Final revised paper (published on 31 Jul 2023)
Preprint (discussion started on 03 Jun 2022)

Interactive discussion

Status: closed

RC1:
'Comment on egusphere-2022-428', Anonymous Referee #1, 28 Jun 2022

Review of Thibault de Chanvalon et al. EGUsphere

This paper presents an original dataset of the carbonate system and major redox species in the water column of a stratified estuary with anoxic deep waters. The objective is to determine the main reactions that lead to a net production of alkalinity in the estuarine bottom waters. Based on an analysis of TA/DIC ratio and the stoichiometry of reactions, the authors conclude that MnO2 reduction followed by Mn carbonate precipitation are the two main reaction that can explain the observed trends in TA. I found many problems in this MS, including several small mistakes on the principles of the carbonate chemistry in the text, figures of poor quality not appropriate to describe the processes that are discussed in the text, a presentation aggregating results and discussion that makes the authors reasoning very hard to follow, and finally, a conclusion that appears speculative and not fully supported by the data. I had hard work reading the MS because of language problems and too many shortcuts all along, but I first thought it could be reconsidered after major revision because of the high quality of the data. However, when reaching the end of the discussion, I found the conclusions speculative and not fully based on appropriate quantitative statements, so I believe the analysis should be started over and the paper in its present form could be simply rejected, or at least revised in depth.

Main problems:

1-presentation

Presentation of the results is confusing and the MS structure with a “result and discussion” section makes it worth. Choice is made to present only plots of concentrations versus salinity aggregating two sampling periods. Readers cannot get a precise idea of the vertical structure of the water column in the estuary. Conceptually, longitudinal gradients are mixed with vertical gradients without any consideration about respective mixing times. A long and unnecessary discussion is made about the choice of the freshwater end-member values (which is not a real freshwater), although it appears that most of the salinity gradient studied here occurs vertically. We have no map of the estuary with sampling points. No info about timescales, mixing of end members is analysed with little information about the timescale for the mixing to occur.

I was disappointed by the absence of real vertical profiles (some are in Fig A2, but not DIC and TA, pCO2, Sal, T, pH…) in the main text, although I understand the usefulness of the time composite salinity plot in Fig. 1 for the modelling and mass-balance purpose (assuming that the authors are able to demonstrate that the hypothesis behind such plot are valid)

2- scientific content

see mistakes and imprecisions, in line by line comments

Stoichiometric model in fig.3 does not include the possibility for gas exchange to alter DIC and AOU, at least near the surface layer. Depending on pCO2 and O2 %sat values at the surface, gas exchange can alter the AOU/EDIC ratio away from 1. Deviation of the O2 / CO2 correlation can be due to carbonate buffering effect on CO2 but not on O2 (see e.g. in rivers: Stets et al. (2017), doi:10.1002/2016GB005578.).

In fact, because the salinity and redox gradients are vertical at the study site, there is no need to always consider the gas exchange and its impact on DIC. Using the pCO2 value at the surface, it would be possible to calculate the change in DIC due to invasion of atmospheric CO2 in the first meters of the water column during the representative mixing time, and show that this change is negligible.

The main problem I see concerns the conclusion that Mn oxide reduction coupled to Mn carbonate precipitation is the “key” mechanism.

First it is not clear in the MS what are the respective roles of Mn and Fe, both appear in the title and abstract, but only Mn is considered in the stoichiometric approach. Second, the argumentation on the predominance of Mn reactions on the production of alkalinity is based only on the TA/DIC slope of 2.4 observed between the suboxic zone and the sulfidic zone (Fig. 3). However, there are many processes and reactions potentially occurring in this transition zone and the slope of the TA/DIC ratio does not only depend on the nature of the reactions as the authors analyse, but also on the intensity of the reactions and on the mixing intensity by turbulence and vertical transport between the two layers. Indeed, at the top of this suboxic-sulfidic gradient some TA consuming processes by secondary reaction not involving organic matter can occur. So the presented analysis considering the TA/DIC slope variations with the stoichiometry of primary reactions followed by secondary reaction such as CaMn precipitation does not account for secondary reactions that may decrease the TA without changing the DIC.

Finally, the MS itself reveals the weakness of the conclusion about the importance of Mn reactions: L310 “Based on an average concentration of 20 μmol g-1 of Mn in suspended particles, the 88 μM of MnO2 would require a suspended material concentration of about 4.4 g L-1, which is again one or two orders of magnitude higher than the 0.01 – 0.1 g L-1 usually found in the Chesapeake Bay.”

Line by line comments

Abstract

« burial of carbonate which modulates the ability of the ocean to trap anthropogenic CO2. ». Not clear if you refer to build up of alkalinity in the ocean, which is indeed a sink of atmospheric CO2 or burial of CaCO3 which leads to degassing of CO2 (Buffer factor 0.7, See works by Frankignoulle and Gattuso end of 90s in coral reefs). burial of carbonate would not trap anthropogenic CO2.

L15: according to the profiles, how was NEP distributed? Positive at the surface and negative below?

You mention carbonate dissolution, but no precipitation occurs for instance in blooms at the surface?

L28 “weathering” rather than “erosion”

“enrichment not associated with a Ca2+ enrichment, in contrast to the HCO3- released from continental erosion (preponderant at thousands to a million year scale, Urey, 1952).” HCO3- also comes from dissolution of continental rocks others than carbonate rocks (100% atmospheric CO2), and thus without Ca2+ enrichment.

L40 “with a high vertical resolution (down to 10 cm).” a pity we cannot see these high-resolution profiles in the MS, at least some XXX

Introduction is focussed on CaCO3, but the paper is mostly based on an analysis of TA/DIC ratios. Better introducing the principles of TA/DIC ratio analysis would be helpful

L49: eleven or “a dozen”?

L62 define DI

L93 “an excel sheet implemented with values from (Millero, 1995)” > which carbonate and bicarbonate dissociation constants and solubility coefficient of CO2 ?

L100 “TA and DIC are conservative during mixing” for DIC, this is true only if no gas exchange occurs, which is the case vertically in a water column, below a certain water depth that could be calculated with the data and a simple gas exchange parameterization

L108 “Such changes were not necessary for DICex calculation.” Why? The choice of the freshwater TA & DIC end-members looks arbitrary. Please better explain. In theory, the sensitivity of calculated DICex and TAex to the values in the freshwater end-members can be calculated

L111 “the uncertainty of our description” Awkward formulation

L151 “While direct plots against depth generate noisy profiles that are less informative, plots against salinity provide consistent information about the processes.”. In a section called “water column stratification”, one would expect to see at minima T and S profiles versus depth. Why “noisy profiles”? are they altered by the sampling procedure? How can profiles be noisy versus depth but not versus salinity? Are salinity profiles “noisy”? Does the sampling keep the stratification intact? Is the noise due to heterogeneity induced by tidal currents despite samples being taken at tidal slack?

L152 > “River” flow

L158 “Below, with increasing depth, an important increase of pCO2 accompanying the decrease of O2, pH and temperature is visible.” In fact, readers cannot see anything “visible” “with increasing depth”, only Fig A2 reports vertical profiles, and no S, T, pH, O2, pCO2 are shown. In addition, it looks that some 2017 profiles start only at 8m, why? In Fig. 1 the surface “PP” layer is referenced as 2 meters depth, does this mean that the surface layer sampling includes only some of the stations? Why such strategy? Why no systematic surface sampling? This needs clarification

L159: “A relatively invariable low O2 zone (called ILO in Fig. 1) is here defined by the depth invariance of O2 concentrations, and 160 corresponds to a concentration of about 30 μM in 2017 and 110 μM in 2018. Other species are also relatively stable for this depth such as pCO2, at about 2500 μatm in 2017 and 1800 μatm in 2018, and pH, about 7.3 in 2017 and 7.4 in 2018.” Readers have no idea what depth you are referring to. There is no figure versus depth for these parameters

“The main changes between the two campaigns correspond to a greater oxygen penetration in 2018, preventing nitrite accumulation and to the appearance of a surface layer (with salinity below 3) that stands above the primary production zone in 2018.” Readers are lost not only because figures are not showing what you are referring to, also because you show and discuss the data at the same time.

L172 “Because of the presence of oxygen, the NO2- production would be more likely associated with nitrification of the NH4+ diffusing upward rather than denitrification despite the possibility of reducing conditions occurrence in micro niches.” No NH4 and NO3 data are shown, it looks speculative.

L178 “The MnOx decrease fits perfectly to the Mn2+ increases in sulfidic conditions (Fig. 2)”. sorry, I could not find this perfect fit in the sulfidic zone in Fig.2

L180 “efflux” > “flux”

End of page 7: you are discussing analytical aspects in a section about vertical stratification. This section is very difficult to follow. Rewrite.

L192 “However, due to river mixing with ocean waters…” the paper appears very confusing when it aggregates all mixing processes, spatial and time scales: longitudinal and vertical, seasonal. What are the typical vertical and longitudinal mixing times? I guess if the vertical structure is stable over time as the authors write, then vertical mixing is slow and the described geochemical reactions occur at timescales of months to year? This is what justifies the use of a single plot that aggregates the two seasons? Then the longitudinal mixing with seawater is not sampled here (salinity > 20) but it could be shorter? Mixing of buffered marine water with anoxic bottom waters (and thus reoxidation reactions) at low river flow and mixing with surface fresher waters at high river flow?

L197 “This offset is within the uncertainty of the endmember calculation even if slight DICex background enrichment has been modelled (Shen et al., 2019) resulting from faster atmospheric equilibration of O2 than CO2 after respiration reactions.” Not clear what you mean here: what has DICex enrichment to do with different rates of CO2/O2 atmospheric exchange? Please explain. This is a classical problem when results are mixed with discussion. The amount of data presented and the relative complexity of the geochemical analysis make the combination of result and discussion sections very difficult to follow.

What is the point discussing these values of freshwater end-member? all the reactions described in the paper occur at salinity >1.7 or 7.1, so this salinity value can be used as end-member. Extrapolating all TA values until Sal 1.7 (high river flow) as done in the MS is ok if vertical mixing time , no need for a long text about the choice of FW end-member, same for SW. Describe in Mat & Met

Fig 3 panel c: arrow direction “CO2 uptake” would decrease DICex, not increase

L200 “Interestingly, the relative changes of DICex and TAex, further named ΔTAex and ΔDICex, does not depend on the endmember calculation and their ratio presents much lower uncertainties (about 0.1) facilitating their interpretation”. This could be partly transferred to the Mat & methods section. A scheme in a suppl. figure could also help to define the variables along the vertical salinity gradient.

L200 “In 2017, TAex stayed almost constant up to the oxic zone (Fig. 3a)” we cannot see the “oxic zone” in Fig 3a, only guess it. Result section could show depth profiles and discussion the salinity plot

“ΔTAex/ΔDICex ratio of 0.1 ± 0.1 which indicates a net aerobic respiration (AR)” not only respiration, also primary production assimilating NH4+ . What is a “net” aerobic respiration?

What has the discussion in L200-L220 to do with “river flow control”, the title of the section? The MS needs to be reorganized.

L210 “Finally, for 2017, despite pCO2 being below atmospheric saturation at about 2 m depth (Fig. 1), the possible CO2 invasion does not significantly modify the observed ΔDICex/ΔAOU signal at the shallowest depth sampled.” I agree that gas exchange is a slow process compared to PP and AR. However, gas exchange still occurs and it affects DIC/AOU ratio with a slope still close to 1

L215 “In 2018, this surface water history did not repeat as fresh and light water masses brought by the exceptional flood drastically modified the carbonate system equilibrium. First, a low salinity layer with pCO2 at 1000 μatm overlays the primary production layer (Fig. 1)” We really need to see the most relevant vertical profiles…. Or isolines.

L217 “Just below the air-sea interface, the lock down of atmospheric exchanges by the law salinity layer produces supersaturation of trapped O2 (Fig. 1, for S between 3 and 4).” Exhausting to follow. Contrarily to the authors, the reader has not seen the vertical profiles before. Law salinity > low salinity

“In Fig. 3a and 3b, this process translates into a vertical distribution at DICex = 40 μM associated with negative AOU and slightly positive TAex.” I see no “vertical distribution” in Fig 3. Negative AOU is nothing special in surface productive waters

L219 “This original signature can be modelled by the combination of simultaneous carbonate dissolution (CD) and PP fuelled by NH4+, in equal proportion and would result in no DICex, only TAex production (see Table 2); the carbonate dissolution buffers the DIC consumption produced by PP. The Ca2+ concentrations observed by Su et al. (2021) and during the 2018 cruise (data not shown) vary linearly with salinity i. e. [Ca2+] = 0.282 S + 0.4 in mmol L-1. Assuming similar behaviour in 2017, calculations show that the whole water column is undersaturated with respect to calcite and validates the possibility for CD.” This seems speculative (no calcite saturation value is shown); in general, PP increases the pH and favours CaCO3 precipitation rather than dissolution. One could also say that if Ca2+ is conservative, then little or no precipitation/dissolution occurs.

L220-230 are difficult to follow; this section starts identifying some preponderant reaction at the top of the water column (oxic condition, what about reoxidation of reduced species diffusing from below?), but the following section is entitled “Identification of preponderant reactions”. The paper needs a better organisation

There seems to be a mistake in reaction SR-O In table 1, H2SO4 appearing on both sides of the arrow. If you eliminate H2SO4, then the reaction is aerobic oxidation. In fact you cannot combine two reactions when one occurs only in oxic condition and another only in anoxic condition

L235 remove “3.3. Sediment control”

L238 “cannot be explained by most typical chemical reactions such carbonate dissolution (CD), aerobic respiration (AR), CO2 uptake or primary production (PP = -AR).” I though this section concerned anoxic conditions. This is confusing

L241 “Moreover, SR alone underestimates the importance of the H2S oxidation pathway.” Not sure what you mean here, please reword

L246 “Middelburg et thal., 2020” many typos in the MS

L248 “corresponds to the uncharged species produced, mostly in solid or gaseous phases” be precise… you mean N2 by denitrification and FeS ?

L257 “a non-charged species.” > specie

L260 reasoning on the importance of N based only on NO2- data looks speculative if no NO3- / NH4+ are shown

Fig4: show all units

L263-266 Suddenly, the authors mention a “monthly timescale” without any apparent reason for that.

L267 “ “important” stock concentrations at a monthly timescale (with concentrations that frequently exceed 1 mM in anoxic porewater).” Why porewater? The study does not deal with sediment

L272 “represent the main expected respiration processes” please better explain why the 2 mentioned reactions are expected to predominate. Why Mn more than Fe?

L270-285 contains many shortcuts and language imprecisions and hardly convince the readers that the mentioned reactions are preponderant. The analysis appears almost only qualitative, based on TA/DIC ratios, not quantitative based on concentrations and mass-balance

“The reduction of HNO3 down to NH3 is not detailed but would result in almost similar alkalinity changes: 1.15 for NH3 production (DNRA) versus 0.95 for N2 production.” Instead of “alkalinity changes”, do you mean TA/DIC ratio?

“The only solid form of Mn(II) is MnCO3, since MnS is negligible” why should Mn(II) be solid? Unclear. In fig 2 max Mn(II) concentration is about 8microM in the bottom layer, how does this contribute stoichiometrically to the 100 microM increase of TA?

L275 “FeCO3 production would produce a very similar reaction as MnCO3 production; the latter, more common, is favoured in this simple description.” What “simple description” are you referring to here?

L277 “minimum required amount of sulfate reduction” Awkward formulation improve language

L280 “After sulfate reduction, H2S can also accumulate in the water (SR reaction) or be oxidized back to SO42- (SR-O is detailed as an example).” Yes indeed. However, H2S oxidation by O2 will lead to zero delta DIC and negative delta TA, and would result in an increase in the observed dTA/dDIC slope without the necessity of involving Mn secondary reactions. If H2S is totally reoxidized by O2, then the overall delta TA is null.

L285. Readers need to know to what redox zone you are refering to. This 2.4 slope concerns only the suboxic-sulfidic transition zone. In general, the paper needs a better organization and more detailed discussion.

L310-320 seems speculative and is not convincing: in the water column the quantities of Mn is not sufficient to validate the stoichiometric model. Why should the reaction occur in the sediment, if the 2.4 TA/DIC slope concerns the bottom of the water column and not the sediment porewater?

“The sedimentary solid Mn stock is about 10 mM” per square meter, per kilogram?

“which largely exceeds the 88 μM required to produce the 100 μM TAex increase.” The TA increase occurs in the bottom waters, if you want to relate it quantitatively to the sediment content, you should not only compare concentrations, but rather upward and downward fluxes in the bottom layers and at the sediment-water interface.

L320-326 are disconnected from the rest of the paper

Citation: https://doi.org/10.5194/egusphere-2022-428-RC1
- AC1: 'Reply on RC1', Aubin Thibault de chanvalon, 04 Jul 2022
  
  Reviewer #1 did an intensive reading of the document resulting in important general comments supported by many detailed criticisms. Reserving our detailed answers for the final response, we would like to address here 3 of the main comments made by Reviewer #1.
  First, Reviewer #1 was frustrated by the presentation of the data. In particular, he/she suggests that Figure 1 aggregates two sampling periods, longitudinal gradient along the estuary and vertical gradients. This frustration is indicated often, sometimes by requiring a map to describe clearly the longitudinal gradient, sometimes requiring vertical profiles with depth in the y-axes. It seems that all this frustration came from a misunderstanding, that could easily be avoided if the manuscript does a better job underlining the sampling design. However, in the current manuscript it is indicated precisely that “During two sampling campaigns from August 3rd to 9th, 2017 and July 28th to August 3rd 2018 eleven profile casts were conducted in a 25 m water depth in the Chesapeake Bay (Station 858, 38°58.54’N; 076°22.22’W)”. This text indicates that all the samples came from the same location, reducing considerably the interest for a map and the pertinence of the reviewer’s criticism about longitudinal variations. Additionally, the Figure 1 clearly separates the 2017 campaign from the 2018 campaign avoiding any confusion. Finally, the reviewer suggests that plotting data against depth will better describe the vertical gradient than plotting data against salinity. Density plots (here approximated by the salinity) are often preferred to depth plots and in our case makes the data from the same time period much more comparable.
  Second, about the science, the criticisms made by reviewer #1 are more fundamental. The current manuscript fails to convince him/her about the rationality of the method and about the strength of the conclusion. Our goal is to investigate the influence of iron and manganese on alkalinity (TA). Important variables such as dissolved inorganic carbon (DIC) and apparent oxygen uptake (AOU) are also reported. The method has two steps, first we identify all the processes likely to modify these 3 parameters based on our understanding of the environment. Second, we combine these processes, with different intensity, to get a model fitting the data. Among the combinations that fit, the simplest one (with less involved processes) is preferred (Okham razor). Reviewer #1 regrets we don’t estimate the CO₂ invasion in the water although it certainly happens. It will be done, but it was neither the goal of the manuscript nor requested by the method since parameters in the most superficial layer are fully explained based on 1 process: aerobic respiration. It is not possible to assess the relative importance of each potential process, we only identify the preponderant one. The variations of CO₂ invasion impact with depth are probably too small to compare to the variation of respiration impact on the ratios TA/DIC and TA/AOU.
  Finally, the main criticism by Reviewer #1 is “the argumentation on the predominance of Mn reactions on the production of alkalinity is based only on the TA/DIC slope of 2.4 observed between the suboxic zone and the sulfidic zone (Fig. 3)…” Note that this important reactivity of MnOx and Mn(II) was observed during both campaigns.
  “… However, there are many processes and reactions potentially occurring in this transition zone and the slope of the TA/DIC ratio does not only depend on the nature of the reactions as the authors analyse, but also on the intensity of the reactions and on the mixing intensity by turbulence and vertical transport between the two layers…”
  Mixing, and mixing intensity (between waters) will not directly modify the DICex or TAex because they are conservative during mixing. It is the reason why we are using them (for example pH is not conservative and does not support the discussion). Only reactions can modify this ratio. Mixing plays a role only if it favours rapprochement followed by reaction between two species. That is why our approach (Table 1) – and it is part of the originality of our ms - takes into account sequences of reactions that can occur in a water mass from its equilibrium with the atmosphere to the position where we sample it. About the importance of reactions intensities: the DICex/TAex produced by one reaction is independent of its intensity which is one other strength of our approach. In case of many simultaneous reactions, the relative intensity is important and is taken into account in our approach. For example, the ΔTAex/ΔDICex of 0.77 associated with a ΔDICex/ΔAOU of 1.5 can be fitted by the combination of 1 mole of organic matter respiration simultaneously to 0.5 mole of carbonate dissolution (Table 2).
  “...Indeed, at the top of this suboxic-sulfidic gradient some TA consuming processes by secondary reaction not involving organic matter can occur. So the presented analysis considering the TA/DIC slope variations with the stoichiometry of primary reactions followed by secondary reaction such as CaMn precipitation does not account for secondary reactions that may decrease the TA without changing the DIC.”
  When we describe a sequence of primary reactions followed by any secondary reaction such as CaMn precipitation we surely take into account the effect of secondary reaction, as this is the goal of building these combinations. That is why we speak about net reaction and take into account only species available in large quantities likely to react from its equilibrium with the atmosphere to the position where we sample it. No intermediate species produced after atmospheric equilibrium and consumed before sampling such as catalysts are relevant in our approach. That is why the reviewer’s comment “If H₂S is totally reoxidized by O₂, then the overall delta TA is null.” is not relevant: the overall delta TA needs to be considered from the equilibrium of the water with the atmosphere. Therefore, the reaction producing H₂S has to be taken into account, namely sulfate reduction, to generate an overall delta TA of 0.15 (produced by nutrient release) as illustrated by the reaction SR-O (Table 1).
  Some of the discussion provided here can surely be added in the discussion section for clarification. However, we demonstrate that the main criticisms from reviewer #1 do not break down our demonstration that only a reaction producing metal carbonate is able to generate the observed TA/DIC ratio of 2.4.
  
  Citation: https://doi.org/10.5194/egusphere-2022-428-AC1
RC2:
'Comment on egusphere-2022-428', Anonymous Referee #2, 11 Jul 2022

The comment was uploaded in the form of a supplement: https://egusphere.copernicus.org/preprints/2022/egusphere-2022-428/egusphere-2022-428-RC2-supplement.pdf

Citation: https://doi.org/10.5194/egusphere-2022-428-RC2
- AC2: 'Final response', Aubin Thibault de chanvalon, 20 Jul 2022
  
  Dear Editor Middelburg,
  Both reviewers did a detailed reading of the manuscript providing important points to improve it. Both convince us about the necessity to improve the form, including 1) to split results from discussion, 2) to improve the model description, 3) to include comparison with other studies in the discussion. This will clarify which interpretation depends on the model’s hypothesis. It will also result in a more detailed section 2.3.3 underlining that the model describes the net result of sequences of reactions that occur in a water mass from its equilibrium with the atmosphere to the sampling point in order to identify the more likely preponderant reactions. It justifies the term net reaction, that the model takes into account only the reagents with substantial amounts, that it does not require a detail investigation of ongoing kinetics and that it only identifies preponderant reactions, despite minor one, such as nitrification can occur.
  On the substance, we do not consider that the criticisms from reviewers #1 and #2 break down our demonstration that only a reaction producing metal carbonate is able to generate a TA/DIC ratio of 2.4. We already answered to general comments from reviewers #1. For its part, reviewer’s #2 comments focus first on the kinetics. As noted previously, the model describes the net reactions having already modified the chemistry of the water mass since its last equilibrium with the atmosphere, independent to the rate at which these reactions have occurred. Reviewer #2 considers that the terminology proposed by Soetaert et al (2007) is as generic as the equation (4). The Soetaert et al (2007) publication was a fantastic source of inspiration, nevertheless their definition of alkalinity is based on the excess of negative charge plus/minus six specific chemical species which do not allow the reader to easily understand how new species (such as reduced FeS clusters or DOM) will change the alkalinity, which is what our equation (4) does. Finally, the main argument of reviewer #2 is that “ratios of TA/DIC exceeding 2 have been discussed in earlier works”. Unfortunately she/he does not give any references and despite additional literature survey (including Lukawska-Matuszewska, 2016; Hu et al., 2010; Drupp et al., 2016; Kuliński et al., 2014; Abril et al., 2003; Berner et al., 1970; Hiscock and Millero, 2006; Goyet et al., 1991; Rassmann et al., 2020), we were not able to find publications reporting ΔTA/ΔDIC ratios above 2.
  Whatever will be your final decision, we wanted to thank both reviewers for the improvements they proposed and the scientific stimulation it produced.
  Sincerely,
  Aubin Thibault de Chanvalon
  
  Citation: https://doi.org/10.5194/egusphere-2022-428-AC2

Peer review completion

AR: Author's response | RR: Referee report | ED: Editor decision | EF: Editorial file upload

ED: Reconsider after major revisions (02 Aug 2022) by Jack Middelburg

Dear dr. Thibault de Chanvalon:

Thank you for submitting your paper to Biogeosciences. Two referees have provided similar thorough and constructive evaluations. They believe that your paper is based on high quality data and that you address a topic of importance: the alkalinity production and consumption in a redox stratified system due to manganese (and iron) cycling. However, they identified major issues that require resolution before this paper can be published. In your final response, you have summarized the most pertinent issues and there is no need to repeat them here in detail.

The bottom-line is that your paper has value but needs a major overhaul in terms of presentation and discussion. Both referees recommended separating results and discussion and I agree. Your data interpretation framework and model description also need additional elaboration. I recommend better integration of existing knowledge and to link your approach (and the terminology) presented in section 2.3.2. with that in use by others (active and inactive vs. non-conservative and conservative, etc.). As an example, prior studies have generalized the Dicksons’ alkalinity definition for including non-traditional acid-bases such as colloids, dissolved organics, etc. It appears that you have not been able to convince the referees of some of your conclusions: in other words, you have to rethink some of your interpretations.

It is evident that your revised paper needs another round of evaluation before a binding decision can be made. I therefore give you the opportunity to revise your paper. If you decide to withdraw and publish elsewhere, I understand, but please then inform us. If you prefer resubmission, then please discuss in detail the feedback with the senior authors involved so that the next version will meet our quality standards in terms of interpretation and presentation.

With best regards,

Jack Middelburg, Associate Editor Biogeosciences

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AR by Aubin Thibault de chanvalon on behalf of the Authors (26 Oct 2022) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (14 Nov 2022) by Jack Middelburg

RR by Anonymous Referee #3 (05 Jan 2023)

RR by Anonymous Referee #2 (23 Jan 2023)

Suggestions for revision or reasons for rejection

I am reviewing this manuscript for the second time and feel that the authors have tried to incorporate the comments of both earlier reviews. The split into results and discussion helped to improve the manuscript and section 2.3.1 is a nice addition (but: see below). I feel that I am less critical on the manuscript than last time, but at the same time I am not yet on the point where I can recommend publication.

General comments
The introduction lacks a proper build-up. In the new section on anoxic environments, suddenly alkalinity is used without introducing its link to carbonate dynamics in the first paragraph. I also don’t understand the use and discussion of ‘charge transfer’; for example, when Fe and Mn oxides are used for OM decomposition, they still change alkalinity. Finally, this section contains quite some inaccurate formulations: e.g., metal oxides are not a pathway (L. 42) and are not always transformed into sulphur or carbonate species; they can also remain in dissolved form.

Section 2.3.1 is a nice addition to the manuscript but not easy to read. I like to think that I am mathematically inclined, but I still don’t follow all the reasoning here. First, the explanation now uses a mixture of ‘hypothetical species’ C and D in the equations, and TAex and DICex as examples in the text. However, for example C and D in Eq. 3 to 5 cannot directly be replaced with TAex and DICex, as they cannot be part of a reaction equation. So I suggest that you clarify how C and D are linked to TAex and DICex. Second, I don’t understand where the 0.1 in Eq. 6 is coming from. Third, I don’t think that the bow and the set of spears are as different as you present them. In my view, the bow is simply representing how the relative weight of the various reactions that make up each spear may change as a function of salinity. At the same time, each of the spears can still include an additional source (e.g. from sediments or lateral exchange) and you seem to ignore this possibility in your calculation of v and vi in Eq. 9 (L.167). When looking back at the comments on the earlier version, I see that this has also been pointed out then.

The final part of the discussion becomes very confusing (L. 404-419). How can you use a reaction driven approach if you explicitly state here that external inputs from the sediments are required? This seems very contradictory. It is only possible if 1) you include sediments as part of your system, which doesn’t seem to be the case; and 2) extend the timescale, but then the steady-state assumption doesn’t hold anymore. This point really needs clarification, and in fact probably means that the distinction between bow and set of spears cannot be drawn as black-and-white as this manuscript does.

Detailed comments per line
L. 75–92: This section is very detailed in its experimental description but it lacks clarity on which Mn and Fe species are actually measured. I was only able to deduce this information from the results.
L. 102-103: I found this difference between the 2017 and 2018 campaigns quite interesting. Can you link it to the higher inflow of 2018 making e.g. the used equilibrium constants less reliable?
L. 110-112: This is a very complex sentence. Please try to simplify.
L. 115-116: Also Eq. 1 is not valuable in case of such a change.
Figure 1 caption: not sure what you mean by ‘a segment’ here.
L. 126: Why not visually add this excess to Fig 1 in order to try to link C and D better with TAex and DICex?
L. 130: “has to be determined” I would say that this is your choice and I would be really curious to know how much uM this TA endmember would have to change in order to add 5% uncertainty on the slope of the mixing line (as you discuss for the oceanic endmember). Your previous manuscript version had a big discussion on the upstream endmember and although I understand your current choice, I would like to substantiate a bit more that it is ‘less sensitive to short-term changes’ (L. 133)
L. 140: Here you should use “net stoichiometry” (or “apparent stoichiometry” as you use later in this section), it is still a mixture of several reactions.
L. 142-143: I’m not an expert in error propagation, but shouldn’t the uncertainty be equal to the square root of the sum of squared uncertainties?
L. 147-149: I don’t understand this sentence, Eq.6 doesn’t describe a single solute. Shouldn’t this refer to Eq. 4 instead?
L. 150: I don’t understand this steady state assumption in the context of what you state in L.146-147 on the temporal evolution of water masses. Is this because you exclude additional sources from your model? (See comment above on spears versus bow)
L. 177: I feel that Eq. 12 needs a bit more credit to the earlier approaches linking charge with alkalinity than a short mention in L. 186-187 alone.
L. 196: Similar zonation yes, but the 2018 profile appears noisier and the transition somewhat shallower (at 5-6 m depth rather than ~7m depth in 2017)
L. 199-203: This is again a very complex sentence. You write about pCO2 lower than atmospheric but then mention values of 505 and 770 uatm? I don’t follow this.
L. 212: I don’t like the term ‘suboxic’ anyway (I prefer hypoxic; in fact your ILO zone can be called hypoxic zone) but <1 uM already is anoxic. Anoxic and euxinic/sulphidic have clear different meanings (anoxic meaning without oxygen, euxinic meaning free sulphide present), so using anoxic here is more correct. Then, in L. 223, you can write “the transition from sulphidic to anoxic zone” which also seems more correct.
L.241: I’m not sure if you can deduce from Fig 3 and 4 that the stratification is similar. In fact that is more clearly shown in Fig. 1. Maybe a different wording would better fit what you want to describe here (e.g. zonation?)
L. 249: A zone with neither oxygen nor sulphide present is an anoxic zone, not a suboxic zone. See my earlier comment on this topic.
L. 264-266: As said before, I don’t think this is “either/or”. It might be more valid to say that one dominates the other (i.e. reactions dominate over mixing, in this case).
L. 274-278: This is quite a list of assumptions – good that they are explicitly mentioned. I don’t understand the difference between #2 and #3 – what do you mean with ‘starting point’? If that is in time, it is similar to a steady state, isn’t it?
L. 282: “this interpretation does not identify reactions with minor impact on the carbonate cycle”- because of a low rate, or their stoichiometry, or both?
L. 292: “which corresponds to the occurrence of only net aerobic respiration (AR)” – two comments: 1) add this indicates that AR > -AR (you use the same symbol for AR and net AR now), and 2) given that the slope is 0.1 and ΔTA of AR is 0.15, something else must have occurred with alkalinity as well, unless you have clear indications that OM was very different from Redfield ratio. If you were to fit ΔTA rather than ΔAOU, you would probably have around 15-20% of the produced NH4+ nitrified, I guess? What would then be the resulting ΔAOU? Are there indications that it’s more appropriate to fit ΔAOU rather than ΔTA?
L. 306: I don’t understand the infinity symbols here. Yes, ΔDICex = 0 but since you compare the slopes of three different species, ΔTAex/ΔAOU will not equal infinity. Otherwise, you have to present ΔTAex/ΔDICex/ΔAOU differently and make it clear that you always compare ΔTAex/ΔDICex and ΔAOU/ΔDICex, as you do in Fig 5 and Table 2. But from the way it is in the text, and also because you fit three reactions to three equations, this isn’t obvious at all. The same applies to the presentation of ΔTAex/ΔDICex/ΔH2S later on.
L. 314-322: Why would nitrification occur in this zone in 2018, but not in 2017 or in the zone above? The reasons regarding kinetics (L.296) prevail here as well. Are there logical reasons to assume that kinetics are limiting above (where O2 is higher), but not in this zone?
L. 327-329: Well, that depends on what you want to know. I am not sure if I agree; it depends on whether the combined ΔTAex/ΔDICex/ΔH2S can be derived by multiple combinations of multiple processes.
L. 336-344: reading this makes the focus on charge in the introduction much more understandable. I would move this text to the introduction and merge with the current paragraph (still taking into accounts the comments).
L. 345-347: But you measured these species, didn’t you? Why don’t you make this decision based on your measurements, such that you can substantiate this choice? When looking at your measurements, I am not sure if your measurements substantiate this choice; especially given that you discuss their dynamics in the result section as well.
L. 351-353: I don’t know what you want to achieve by including this reason, but the fact that you cannot distinguish SR followed by H2S oxidation from AR in your model, does not mean at all that this set of processes isn’t important. It just means that you cannot conclude it from your model.
L. 359: “as the only Fe product is FeS or FeS2”- where? In your model or in reality? (i.e. as can be deduced from your measurements)
L. 363-368: I find this section much more strongly formulated than L.360-362 which, in itself, leads to speculation. So I would revert the order: any reaction in combination with MnR-MnC leads to the production of the ratio, and some of them are more likely than others.
L. 370-372: Measured concentration of MnOx are quite low; are they high enough to support this statement?
L. 372-374: This is quite short; which set is the most likely? Do you expect this to be the same set as in the anoxic zone? And what about sedimentary input? (which you discuss earlier that it must be an important source) Again this comes back to the lack of external inputs into your reaction-driven model.
Table 3: Aren’t there studies from the Baltic Sea water column that you could include here? That system may be more similar to the Chesapeake Bay water column than many of the other systems discussed in this table.
L. 398: “The rhodocrosite saturation (Luo and Millero, 2003) is always below 0.3” – where? In the Chesapeake Bay?
L. 399-401: So this boils down to my earlier comment – a reality check on your model results.
L. 404-419: Here I get really confused – see general comment.
L. 420-426: This upscaling seems a bit out of place, given that the Chesapeake Bay may not be representative at the global scale. This is in fact the main conclusion of your study, that you show the exceptional ΔTAex/ΔDICex ratio. I would therefore suggest to remove it.
L. 436-439: These lines seem out of place in the conclusions, also in the context of my previous comment.
Figure A3: What is meant with the “dMnT…“ comments for Cast #10 of 2017?

Technical comments
General: especially the newly written sections contain many typos and sloppy writing. I did not identify all occurrences but highlighted a few below.
L. 12 (and many more occurrences): use ‘dynamics’, not ‘dynamic’
L. 12: ‘carbonate minerals’
L. 39: ‘anoxic environments’ (reactions are anaerobic)
L. 56: ‘a single station’ sounds better in my opinion
L. 168: “reaction stoichiometry”
L. 175: “species”
L. 198: Explicitly refer to Fig. 3 here.
L. 209-215: add (n=xx) in between brackets for clarity. Also this text is complex to read.

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ED: Reconsider after major revisions (06 Feb 2023) by Jack Middelburg

AR by Aubin Thibault de chanvalon on behalf of the Authors (13 Mar 2023) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (13 Mar 2023) by Jack Middelburg

RR by Anonymous Referee #3 (12 Apr 2023)

Suggestions for revision or reasons for rejection

2nd Review of paper “Influences of manganese cycling on alkalinity in the redox stratified water column of Chesapeake Bay “ by Aubin Thibault de Chanvalon, George W. Luther, Emily R. Estes, Jennifer Necker, Bradley M. Tebo, Jianzhong Su, Wei-Jun Cai

The paper has evolved in a positive way since the previous version: better Figures, fair explanation of the error treatment on DICex and TAex, improvement on the “negative” biogeochemical pathways. But they fail to properly answer the other points that I raised (see below my previous comments):
- The relation with the sediment is still not properly documented (any older study at that site or nearby?) but, at least, the point is tackled in the abstract and a paragraph is written to explain this link. The authors should provide literature data concerning the sediment processes.

- The general statements: I recommended on my first review to shorten part 2.3.1. It was changed and some textbook part including the bow and spear section and Figures were removed. But I still find this part unnecessary long and I am convinced that it could be shortened or part of it diverted in an annex.

- Furthermore, I had troubles during my reading with part 2.3.2. I find the definition adopted for TA (the sum of all charges that each species would have at pH=4.5) not obvious and certainly less useful than identifying bases in solution at the in situ pH and defining which processes consume or produce them. I find this part 2.3.2 not necessary, not well-named (“TA changes indicated by reaction stoichiometry”), and not clear enough to add value to the paper. I would advice to remove it.

- Last point: the possibility of primary production in turbid waters especially during the flood. The authors did not answer to that specific question nor provide data proving that the water was clear enough to allow primary production.

I think that the paper is heading in the right direction and that the authors should consider the comments above before being published.

Detailed comments (some):
- title: “Influences” should be replaced by “Influence”
- line 134 and after: equation numbering is missing, please check!
- line 165: “spread all over the water column”. Add “and also in local sediments”
- paragraph 3.2: too many numbers in text, add a Table with all these numbers
- line 314: provide information on water turbidity to ensure primary production conditions were present at that time (2018)
-line 380: “Figure 4c demonstrates…” I think it is rather Table 2. Please change!

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Previous Comments from review 1:
1- Illustrations: In general, the graphs are of poor quality and very hard to read. Figure 3 and 4 that present the main results of the paper are hard to read as the symbols are too small (and very often quite similar), and the axis should be splitted in multiple axis (a number of software do that very nicely!) in order for the reader to access the data values. Just one example of haow hard it is to read data from the graphs: for pH, quoted in the graph legend of Fig. 3: pH = 7.175+DpH/300!! Hard to recalculate individual pH values without a calculator! Please add multiple axis and change symbol size and shape.
2- Too much generalities: The paper contains a large number of general sections with Figures and equations which are long and probably unnecessary. Especially, section 2.3.1 “Identification of biogeochemical processes…”, is too long, verbious and not so clear. It is more textbook matter when presenting mixing models (lines 110 to 120 including equations 1 and 2 and Fig 1). I would consider shortening this part especially regarding the fact that “in situ transformations” are ultimately replaced by “transfer from the sediment”.
3- Treatment of error for DICex and TAex: I understand that the uncertainty on the measurements of TA and DIC is very small (1 permil), and I acknowledge that. But I question the error calculation (and propagation) of DICex and TAex. As it is written in the paper, these numbers are differences between the measured values (assume an infinitely small uncertainty) and the mixing curve defined by the end members. The authors quote an uncertainty on the mixing slope of 5% (see also Su et al., 2021). Hence the uncertainty on the difference of concentration (DICobs-DICmix) used for calculating DICex and TAex would also be 5% of the DIC or TA at the salinity of the water mass (i.e. about 0.05*2000µM = 100µM). This rapid calculation shows that the error on DICex and TAex could be very large compared to reported values (100-300µM Fig. 3). The authors should spend more time to convince the reader that uncertainties are smaller than my simple calculation or that the observed patterns are statistically solid.
4- Negative biogeochemical pathways: in several occasions (Table 2, line 1 and line 290 “primary production (-AR; Aerobic Respiration)”; line 365 “negative SR; Sulfate Reduction”), the authors provide shortcuts in biogeochemical reactions which are clearly wrong. Primary production process is definitely not the negative aerobic respiration except in some mass balance equation summarizing the effect of these processes on water chemistry. Same for sulphate reduction and sulphide oxidation. The biological organisms that conduct these transformations are different, the biochemical pathways are different. The authors should reconsider their way of presenting these biogeochemical processes.
5- Primary production in flood conditions: I think that the mass balance reaction and chemical ratio reaches its limits when the authors propose that primary production occurs during (or right after) the flood in 2018, and is counterbalanced by carbonate dissolution (line 306). It is known that turbid waters during floods prevent primary production because of light shading, and that primary production favours carbonate precipitation due to the removal of CO2 and the increase of pH. Hence, even if the combination of CD-AR (Table 2, line 2) has the right chemical ratio (∞/0/-∞, line 306), it is very unlikely that these processes can occur in the turbid estuarine waters.
6- Line 373: The ratio of chemical elements observed in the sulfidic region are compatible with reactions involving MnOx and MnCO3, yet the ratio of DICex/H2S in 2017 and 2018 are not shown in a Figure to ascertain this point. It could be added in Fig.5 on a fourth panel or in another Figure.
7- Line 365: the authors declare that several combinations of reactions (5-6-7 of Table 2) may provide the identified DTaex/DDICex/DH2S of 2.4/1/0 in the suboxic zone. They state that it is not possible to choose between these three reactions based on the above ratio of elements. One possible way to decipher between these combined pathways is the C/N ratio produced by the reaction as they are quite different for reaction 7 than for reaction 5 and 6. The authors should investigate that point.

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RR by Anonymous Referee #2 (28 Apr 2023)

Suggestions for revision or reasons for rejection

This is the third time I am reviewing the manuscript and I have thus focused on the parts of the manuscript I was most critical about in the previous rounds of review: introduction, section 2.3.1 and discussion, especially the final part. In my view, the introduction has sufficiently improved but the authors still have some work to do on the discussion and especially section 2.3.1.

General comments
The introduction has surely improved compared to the last version. There is now a link between anoxia and the carbonate system, but the unknowns and objective of this study could still be better introduced. Why is it necessary to better constrain the carbonate cycle in temperate microtidal estuaries?

Section 2.3.1 has been shortened quite a bit (which is a good thing, from my point of view, as the old Figure 1 was probably redundant) and it is good that the meaning of C and D is now explicitly explained. However, the shortening comes at the expense of the readability of the first section. Eq. (1-5) include a lot of terms that are not introduced (such as alpha / stoichiometry and k / rate constant (I assume)) and I wonder how much is really necessary for the manuscript. In the end, the authors would like to show how TAex and DICex can be used in combination with reaction stoichiometries to infer which processes can explain the observed TAex and DICex combination (L.163-166). This means that Eq. (5) and Eq. (7) are the two key equations. I would suggest to either explain L. 118-140 more clearly (and thus expand a bit) or to keep only the essential information in (my preferred option). Maybe the text in L. 283-289 can be rewritten to include in the method section, because this text is non-technical and clearly outlines the assumptions (and confirms that Eq. (5) and (7) are indeed key).

In the previous version, both the other reviewer and I commented on the fact that it is nowhere made explicit that the reactions in Table 1 take place in the sediments and that sedimentary inputs are thus key. The abstract has now properly been rewritten to include that some of the main reactions take place in the sediment, but this needs to be clearer in section 2.3.1 as well. The authors, in their response to reviewer 1, claim that L.157-162 covers this point, but because this text is so technical this key point doesn’t come out strongly at all. Moreover, L.165 still mentions “spread all over the water column” which is fundamentally incorrect because the “zones” include the sediments. There are more examples of this (e.g. L.278, “in situ”). In short, the authors have to clearly define that the “reaction driven” approximation includes reactions in water column and sediment from the start.

This discussion benefits from always comparing ΔDICex with ΔTAex and ΔAOU or ΔH2S. I agree with the majority of changes done in the discussion and also in the final part. However, I do think that the main points of section 4.5 regarding the role of sediments (L. 444-452) need to be moved to / integrated in the method section because (again) the role of the sediments in the approach has to be clear from the start.

Detailed comments per line
L. 22: “carbonate signature” --> I suggest to change to “DIC/TA ratio” because this is what you refer to.
L. 24: “especially in river-dominated environments” --> this now reads as if it applies to all river-dominated environments, but you write yourself that the Chesapeake Bay is quite peculiar (see L. 396). Better rephrase: “the critical role of Mn in alkalinity dynamics in the Chesapeake Bay and potentially other river-dominated environments”
L. 32: “This disequilibrium” --> which one? The DIC increase without concurrent TA increase mentioned two lines earlier? Specify.
L. 36: “accounts for 2/3 of buried carbonate” --> where? Shallow waters globally? Please specify.
L. 41: Do you mean to say that humans migrate to coastal areas because of global warming, or that global warming contributes to eutrophication?
L. 46: “multiplies the possibilities for” --> strange formulation, what about “enhanced the possible build-up of”
L. 49 “negatively charge SO42-“ --> do you need to mention the charge now since you have removed it from the introduction?
L. 53: “TA and DIC concentrations” I wonder here if the TA and DIC concentrations or the fluxes matter. S burial (taking place in the sediment) leads to specific pore water TA and DIC concentrations which impact water-column TA and DIC (the subject of this study) via effluxes.
L. 165: “spread all over the water column” --> and the sediments. See general comment above.
L. 277: “in-situ processes” --> as opposed to mixing, but including the sediments. Again, that should be made clear here.
L. 289-291: I am not sure if I find this a clear comparison, and perhaps even misleading as water is also moving in the opposite direction.
L. 294-295: “an excess of ΔTAex” --> this becomes confusing. What about: “even higher ΔTAex”?
L. 308: “the weakness of nitrification” --> rephrase to something like: “the relatively slow nitrification”
L. 321: “significant nitrification”. How much approximately / at least?
L. 364-365: these low concentrations may have been found in the water column, but not in the sediments where you propose that the reactions take place. So can you use it as a reason here?
L. 386: “at this site” --> in the sediment or water column?
L. 390-392: This is quite an assumption without any sediment measurements, although I agree that on a 10-day period is it likely met.
L. 396: This line exactly indicates why the final sentence of the abstract needs rewriting.
L. 416: Title needs to be changed because global budget is removed.

Technical comments (I have not listed all)
L. 21: “Stoichiometric changes”
L. 23-24: “as summer begins” --> “at the onset of summer”
L. 32: “to DIC”--> “with DIC”
L. 35: “a process named chemical carbonate compensation”
L. 50: “coastal waters”
L. 252: “in terms of”
Figure 4: panel (d) is not explained here.
L. 335: “significant”
L. 336: “no…were not performed” --> remove “not”

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ED: Publish subject to minor revisions (review by editor) (01 May 2023) by Jack Middelburg

AR by Aubin Thibault de chanvalon on behalf of the Authors (22 May 2023) Author's response Author's tracked changes Manuscript

ED: Publish subject to technical corrections (05 Jun 2023) by Jack Middelburg

AR by Aubin Thibault de chanvalon on behalf of the Authors (15 Jun 2023) Manuscript

Short summary

The intensity of the oceanic trap of CO₂ released by anthropogenic activities depends on the alkalinity brought by continental weathering. Between ocean and continent, coastal water and estuaries can limit or favour the alkalinity transfer. This study investigate new interactions between dissolved metals and alkalinity in the oxygen-depleted zone of estuaries.