the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 25 Sep 2025
Evaluating ocean alkalinity enhancement for carbon dioxide removal: evidence from a one-year saltmarsh field experiment
Abstract. Ocean alkalinity enhancement is a promising carbon dioxide removal (CDR) strategy aimed at reducing atmospheric carbon dioxide (CO2) concentrations. To evaluate its effectiveness and potential biogeochemical impacts, field experiments under natural conditions are essential. We report results from a one-year in-situ experiment conducted in the saltmarsh pioneer vegetation zone at Ria Formosa coastal lagoon, Portugal. The experiment comprised replicate deployments of olivine and basalt (treatments), and untreated control sites. Total alkalinity (TA) responded immediately to the treatments, with pore water 1.5 to 2.3 mM higher than the control. High concentrations of CO2 in pore water led to an increase of dissolved inorganic carbon (DIC) higher than TA. Continuous CO2 degassing from the saltmarsh soil was observed, with the treatments prompting higher CO2 fluxes than control. Carbon was laterally exported to the ocean (outwelling), following the trend of excess TA production. This effect was most pronounced during the first seven months after deployment, with basalt producing the best results. These findings provide critical insights into the temporal dynamics and efficacy of alkalinity enhancement in coastal vegetated systems.
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Status: final response (author comments only)
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RC1: 'Comment on egusphere-2025-4555', Anonymous Referee #1, 26 Sep 2025
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AC1: 'Reply on RC1', Isabel Mendes, 28 Oct 2025
Overview
The manuscript “Evaluating ocean alkalinity enhancement for carbon dioxide removal: evidence from a one-year saltmarsh field experiment” tests basalt and olivine for their suitability for OAH in-situ at a saltmarsh. While the manuscript presents an interesting and comprehensive dataset, some of the calculations rely on very simplified approaches e.g.CO2 emissions are calculated based on TA and pH measurements, and outwelling based on concentration differences between inside and outside the plots. This information is still valuable, but authors have to be more careful when presenting and comparing this data. See comments below.
We appreciate the reviewer’s careful evaluation and valuable comments. CO2 concentrations were indeed calculated from measured total alkalinity (TA) and pH values, using the CO2SYS program, which is a well-established and widely used standard in marine carbonate chemistry when direct pCO2 measurements are unavailable. This approach enables comparability with numerous previous studies.
The outwelling calculations were based on the concentration differences between the surface water inside the plots (which interacted with porewater during high tide) and the incoming tidal channel water representing the open-ocean endmember. This method follows approaches used in previous studies (e.g., Wang et al., 2016; Santos et al., 2019) and allows for estimating the material flux from the saltmarsh to the adjacent coastal waters. We acknowledge the reviewer’s concern and will ensure that the limitations and assumptions of these calculations are clearly stated in the revised manuscript.
General comments
Your abstract/discussion and title are not well aligned. Introducing CO2 fluxes and outwelling independently seems disconnected. Put them always into perspective to OAH.
We thank the reviewer for this valuable observation. Having read the title, abstract and discussion, we agree that these sections could be better connected. We will revise them accordingly, including possible adjustments to the title, and rewrite some sentences in the abstract and discussion to better integrate them in the context of OAH.
Calculating CO2 fluxes based on calculated pCO2 from alkalinity and pH seems like a stretch. Saltmarshes likely have high organic alkalinity messing up co2sys calculations and pH measurements tend to be very unreliable. You could make a sensitivity analysis to see how calculated pCO2 values change when assuming organic alkalinity to be 1-5% (remove from TA when calculating CO2) and accounting for the pH precision (use pH plus and minus precision). Then you could report a range for pCO2 and corresponding fluxes. Same for calculated DIC.
We thank the reviewer for this valuable comment. Calculating pCO₂ from total alkalinity (TA) and pH using the CO2SYS program is a well-established and widely applied approach in marine carbonate chemistry when direct pCO₂ measurements are not feasible. We acknowledge that this method can be subject to uncertainties, particularly in low-alkalinity or organic-rich systems where non-carbonate (organic) alkalinity contributes to TA. This may lead to an overestimation of calculated pCO₂ and, an underestimation of DIC.
However, our study site is characterized by relatively high TA and pH, where such effects are expected to be of minor influence. Similar studies have shown that in such buffered systems, CO2SYS calculations agree well with direct pCO₂ measurements (e.g., Abril et al., 2015, Biogeosciences). In our study, we compare different treatments with untreated control boxes, both placed in the same area. Thus, any potential bias in absolute pCO₂ values would be consistent across treatments and would not affect the relative differences between them.
Regarding pH measurements, we used a high-precision pH sensor (SenTix® 940-3, accuracy of ±0.004) that was calibrated monthly with three standard buffer solutions (pH 4: YSI‐381, pH 7: YSI‐3822, and pH 10: YSI‐3823) before fieldwork. The buffer solutions have an accuracy of 0.002 units at 25°C according to the manufacturer's data instructions. They are compatible with National Institute of Standards and Technology pH standards. To ensure accuracy and minimize sensor drift, the probe was allowed to equilibrate in ambient surface water prior to each measurement, and it was carefully cleaned between samples to prevent cross-contamination. We are therefore confident in the reliability of our pH data and the robustness of our derived pCO₂ estimates.
Outwelling/lateral flux calculations ignore porewater/groundwater fluxes, which are a major drivers of carbon outwelling in saltmarshes. Your calculations are still interested but be more specific in the abstract and discussion. E.g., “Saltmarshes were source of TA at low tide as indicated by elevated TA concentrations inside the plots compared to external seawater.” Right now abstract reads as if you did ecosystem scale measurement. To report outwelling in mmol/m2/d when you only calculated for such a short amount of time is not valid. You have to report in per hour and always add “at ebb tide”.
We thank the reviewer for this valuable comment. We agree that our flux calculations are based on short-term (approximately quarter of the day) measurements during ebb tide and do not capture continuous or groundwater-driven fluxes. However, groundwater seepage is not expected to influence our study site. In the Ria Formosa lagoon, groundwater seepage occur only in a few places (Leote et al., 2008). They were recognised by short pulses of low salinity in a tidal channel by the authors (unpublished). At the Esteiro Ancao backbarrier section, they were not recognised higher than 0.6 m below mean tidal level and showed a higher salinity than the outflowing tidal waters (Schönfeld and Mendes, 2021). These settings differ markedly from our sampling area, where no evidence of groundwater inputs has been reported.
Our approach is consistent with previous studies that estimated tidal outwelling from concentration differences between marsh and adjacent coastal waters (e.g., Wang et al., 2016; Santos et al., 2019). While porewater fluxes were not directly used, the surface water sampled during ebb tide had equilibrated with porewater during high tide, as also described in Wang et al. (2016). Thus, the measured concentrations already reflect the integrated influence of porewater exchange on the surface-water composition that is later exported during ebb tide. This surface-water export represents the operational definition of “outwelling” applied in comparable saltmarsh studies.
We will revise the Abstract and Discussion to clarify that our study represents discrete, monthly measurements of surface-water fluxes at ebb tide, rather than ecosystem-scale fluxes. The term “at ebb tide” will be used in places where it is important for the understanding.
Comments by line
L15 Set this into context of the basalt/olivine addition or remove.
We will change the sentence accordingly.
L16-17 Why did control have lower CO2 fluxes despite higher TA?
We thank the reviewer for the comment and would like to clarify that the control plots did not have higher TA. In fact, the treatment plots showed higher TA values compared to the control. Correspondingly, the control exhibited lower TA and lower CO₂ fluxes. We will rephrase the respective sentence in the manuscript to accurately reflect these findings and avoid this misunderstanding.
L17-18 Was outwelling different between treatments?
Yes, outwelling differences among treatments were observed during the first 7 months of the experiment. During this period, DIC outwelling was 3.5 % (3.9 mmol m-2 h-1) higher in the treatments than in the control, with the coarse-grained olivine (5.2 mmol m-2 d-1) and basalt (4.8 mmol m-2 d-1) treatments showing the highest values. Similarly, TA outwelling was 2.6 % higher than in the control, with the highest differences (3.3 %) also recorded in the coarse-grained olivine and basalt treatments (both 4.3 mmol m-2 d-1).
Corresponding clarifications and supporting details will be added to the Abstract and Discussion sections to emphasize these treatment-related differences in outwelling.
L24 Change to “might” be necessary
We appreciate the suggestion. However, we prefer to retain the phrasing “are deemed necessary,” as there is broad consensus among stakeholders and experts that carbon dioxide removal (CDR) is necessary to compensate for residual, unavoidable CO₂ emissions. This conclusion is also supported by the IPCC, which states that CDR will be required to achieve net-zero CO₂ emissions.
L49 km2 superscript
Accepted.
L47 – 64 This should be under Methods: 2.1 Study site
We thank the reviewer for the suggestion and will incorporate this information into the Methods section (Section 2.1, Study site).
L64-70 Reduce methodological details. Describe aims and hypothesis.
We will revise this section to reduce methodological details. A new paragraph will be added at the end of the Introduction, to clearly describing the study’s aims and hypotheses, as suggested by the reviewer.
L71 Not entire caption in bold. Nice map!
Thank you! We will do the captions in regular letters and only the “Figure 1” in bold.
L91 Remove minus before ” - ml”
Accepted.
L91 For which parameters which vials/beakers?
We will clarify this information in the manuscript by specifying in brackets which vials were used for each parameter. Specifically, 20 ml vials were used for alkalinity measurements to ensure samples could be stored chilled and airtight, while 100 ml vials were used for probe direct measurements and for collecting water for nutrient and trace metal analyses.
L93 Why porewater extracted so shallow? Top 1 cm likely mixture of porewater and water sitting on top.
The porewater was extracted from the top 1 cm because this corresponds to the thickness of the substrate layer deployed in the experiment. Sampling within this layer was essential to capture the direct effects of material dissolution on porewater chemistry. Below this depth, biological activity and other geochemical processes could already influence the chemical composition, potentially masking the specific effects of the added material. For methodological coherence, the same sampling depth was used the control boxes. We will add a clarifying sentence to the manuscript to explain this rationale.
L97 remove ) after YSI-381
Accepted.
L98 Need accuracy of instrument not the buffer solution.
Accepted. The brand and type (SenTix® 940-3), and the accuracy (±0.004) of the pH sensor will be added in the Water sampling and on-site measurements description section.
L106 What is precision?
The reproducibility, accuracy and linearity of the alkalinity titration method can be obtained from Mendes et al. (2025), Supporting Information S2, as mentioned in the manuscript. Verification of the method over a period of three days yielded an accuracy of 1.64%, an inter-day precision of 1.96%, and a linearity of 0.995.
L109 Report constants.
Accepted. We added the constants to the Manuscript.
L190 Split section in smaller paragraphs. Some for rest of manuscript to improve readability.
Accepted. The section will be divided in smaller paragraphs to improve readability, as were other parts of the manuscript.
L211 Remove variability and comma before from.
Accepted.
Fig 3. I wonder of delta TA (treatment – control) would be more informative. Maybe you could add two more subplots. For panel a, could you use a shorter y scale. It is very hard so see differences. Same for all other figures. Would adapt y axis to data of each plot.
Round to significant digits throughout results.
The delta TA (treatment – control), referred in this study referred as the excess of alkalinity, is available in the Supplement Figure S1 (surface water) and S2 (pore water) to complement the information presented in Fig. 3. In these supplementary figures, the differences between the treatments and the control are more clearly visible. Because we aimed to directly compare the same parameters in the surface and pore water, we considered using the same y-scale the most effective way to visualize these differences.
In addition, all data throughout the manuscript have been rounded to the appropriate number of significant digits.
L314-316 This is interesting and could be mentioned in abstract.
We appreciate the reviewer’s suggestion. A new sentence will be added to the abstract mentioning that the olivine treatments produced more CO2 than the control, while basalt produced the best results.
L322-330 Repetition of results. Shorten.
We shorten the paragraph and took out the repetition of the Results.
L330 Or is the alkalinity decrease just caused by substrate being washed away over time. If not over the surface maybe over porewater fluxes.
The saltmarsh vegetation, together with the installed frames, prevented the substrate from being washed away during the experiment. Over time, after approximately one year, the mineral layer became patchily covered with newly deposited mud. However, quarterly sediment sampling confirmed that the substrate remained in place and was still present after one year.
L385-399 Outwelling would not be order of magnitude higher if fluxes from high tide would be accounted for. Cannot compare your fluxes to other sites that measured ecosystem scale outwelling. Focus more on the differences between treatments than on actual numbers.
We appreciate the reviewer’s comment. Our study does not represent an ecosystem control, as it was based on measurements from 15 small experimental boxes, located in the pioneer vegetation zone of the salt marsh. Accordingly, the corresponding paragraph will be revised to emphasize the differences between treatments and the control site.
L400-401 Important finding should be in the abstract.
We appreciate the reviewer’s comment and agree with this observation. Accordingly, we will add a sentence to the abstract highlighting that no significant differences were observed between the olivine and basalt treatments or among grain sizes in total alkalinity enhancement.
References:
Abril, G., Bouillon, S., Darchambeau, F., Teodoru, C. R., Marwick, T. R., Tamooh, F., Ochieng Omengo, F., Geeraert, N., Deirmendjian, L., Polsenaere, P., and Borges, A. V.: Technical Note: Large overestimation of pCO2 calculated from pH and alkalinity in acidic, organic-rich freshwaters, Biogeosciences, 12, 67–78, https://doi.org/10.5194/bg-12-67-2015, 2015.
Leote, C., Ibánhez, J.S., Rocha, C.: Submarine groundwater discharge as a nitrogen source to the Ria Formosa studied with seepage meters, Biogeochemistry, 88, 185–194. https://doi.org/10.1007/s10533-008-9204-9, 2008.
Santos, I. R., Burdige, D. J., Jennerjahn, T. C., Bouillon, S., Cabral, A., Serrano, O., Wernberg, T., Filbee-Dexter, K., Guimond, J. A., and Tamborski, J. J.: The renaissance of Odum's outwelling hypothesis in 'Blue Carbon' science, Estuarine, Coastal and Shelf Science, 255, 107361, https://doi.org/10.1016/j.ecss.2021.107361, 2021.; Santos et al., 2019.
Schönfeld, J. and Mendes, I.: Environmental triggers of faunal changes revealed by benthic foraminiferal monitoring, Estuarine, Coastal and Shelf Science, 253, https://doi.org/10.1016/j.ecss.2021.107313, 2021.
Wang, Z. A., Kroeger, K. D., Ganju, N. K., Gonneea, M. E., and Chu, S. N.: Intertidal salt marshes as an important source of inorganic carbon to the coastal ocean, Limnology and Oceanography, 61, 1916-1931, https://doi.org/10.1002/lno.10347
Citation: https://doi.org/10.5194/egusphere-2025-4555-AC1
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AC1: 'Reply on RC1', Isabel Mendes, 28 Oct 2025
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RC2: 'Comment on egusphere-2025-4555', Anonymous Referee #2, 05 Dec 2025
The authors present observations from a year-long field trial of alkalinity enhancement in a salt marsh and use these to evaluate the feasibility of the method in a similar coastal system. The experimental design appears to have been made with care and attention to detail. The paper concludes that large scale deployment of OAE in a saltmarsh system is unlikely to be viable, partly due to the modest benefits that are extrapolated from this small-scale trial to a larger deployment. These results provide needed in-situ context for rapidly evolving discussions about deploying OAE at scale. There is some incomplete reasoning that could be expanded upon and I have made suggestions for changes to some of the figures and data presentation.
Major comments:
Scaling to annual values – this seems to be a bit liberal – consider working with daily, or seasonal rates that may be more appropriate to your experimental results?
Figures – it is difficult to follow the results describing the difference (or similarity) between pore water and surface water (and rising and lowering tide) with the axes limits in the current figures. Consider using a range that better suits the data, even if it means changes within a figure (i.e., subplots with different ranges).
Section 3.4 – the last line of this section, which indicates that positive (outgassing) fluxes were observed throughout the experiment, and that olivine treatments were associated with larger fluxes than basalt and the control, seems like an important result and should perhaps be included in the abstract?
Section 3.5 – the fact that the outwelling (advection) of both DIC and TA is far larger than the local fluxes (pore water to surface water, surface water to atmosphere) seems important, but slightly buried in the manuscript? Would this suggest that a trial with much larger quantities of minerals would be needed to get the right ‘signal to noise’ in these advection dominated (or tidally-influenced) systems?
Minor Comments –
Abstract – the first line states that ‘OAE is a carbon dioxide removal strategy aimed at reducing atmospheric CO2’ this goes without saying – i.e., it is the definition of CDR.
OAE and TA are defined several times and only rarely used. Define early in the text and be consistent with the use of the shortform thereafter.
Line 200 – put the ‘(39.5)’ after ‘salinity’ at the beginning of this sentence.
Line 255 – ‘TA:DIC ration of lowering tide RESEMBLE the ratios of control surface water samples’ – can this be quantified – it is not possible to see this from the figures that are referred to (with the current axis limits).
Line 257 – remove ‘throughout the year’
Line 295 – unclear what ‘globally’ means here?
Citation: https://doi.org/10.5194/egusphere-2025-4555-RC2 -
AC2: 'Reply on RC2', Isabel Mendes, 22 Dec 2025
We thank the reviewer for their thorough evaluation and constructive comments on our manuscript. We appreciate the positive feedback to the experimental design and implementation, and the value of our experimental results for ongoing discussions about large-scale OAE measures. We will carefully consider the reviewer’s recommendations to elaborate on sections of the manuscript where reasoning was incomplete and to improve the clarity of figures and data presentation, when the manuscript is going to be revised.
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AC2: 'Reply on RC2', Isabel Mendes, 22 Dec 2025
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RC3: 'Comment on egusphere-2025-4555', Anonymous Referee #3, 15 Dec 2025
This manuscript details a study on the application of olivine and basalt to salt marsh sediments to evaluate their effectiveness for ocean alkalinity enhancement (OAE). The research is highly relevant and timely, given the rarity of field trials in OAE. While the overall design and duration of the experiment make the study interesting, there are issues in data processing that need to be resolved. The study would also benefit from clearer contextualisation and the inclusion of additional data, which is available according to the methods section. There are currently several claims in the text that I believe are not supported by data.
Major comments:
The manuscript currently presents data on total alkalinity (TA), pH, and calculated concentrations of dissolved inorganic carbon (DIC). It is difficult to draw conclusions about the system's functioning and the impact of the added minerals from these parameters alone. However, according to the methods section, samples for nutrients and metals were also collected (L94-95). Including these data would greatly help interpret seasonal trends and understand natural TA production in the area. Any solid-phase data that might be available would be equally valuable. If data on the permanence/spread of/fate of the added minerals are not available, I suggest the authors still discuss this to the best of their ability, to understand the added minerals’ contribution to the sedimentary TA release.
The statistical treatment of the data and the presentation of results from statistical tests should be improved. Please ensure that summary tables for any relevant statistical tests, such as ANOVAs, are presented (at least in the supplementary materials). Also, consider the suitability of the statistical tests for the data. From certain parts of the text (e.g., L276-278), it appears that ANOVAs were conducted for each month. If this is the case, the tests do not permit conclusions about the overall impact of olivine and basalt over the year (only for each specific month), and the obtained p-values could be less reliable due to multiple comparisons. Furthermore, ANOVAs are generally not appropriate for time series data. I suggest that the authors consider using alternative statistical models, such as linear mixed models.
In general, the importance of the results needs to be scrutinised. There appears to be an issue with equation 10, which inflates the outwelling values. Throughout the text, there are statements about results from treatment being different, without it being clear whether the differences are statistically significant (in most cases, the figures suggest they are not). Because of these issues in data interpretation, the authors conclude that olivine and basalt drive OAE in this natural system. Based on the data, I currently do not agree that this claim is justified. If data do not show significant differences between treatments, please discuss why (since trends often are seen in laboratory experiments) – is it a question about natural variations masking the OAE, are the minerals dissolving too slowly, or is the TA lost somehow?
Detailed comments:
L14-15: Please modify this statement to better represent the data. While the TA increased immediately after the addition of olivine and basalt (L14-15), this effect was transient, and no difference was observed between treatments after a few months.
L79-82: Did the addition of frames cause the plots to be constantly submerged by 2-3 cm of water, even though the soil/sediment would normally have been exposed ~70% of the time? If so, I would have expected the porewater chemistry to change substantially over the course of the experiment compared to “normal” conditions.
Sections 2.4-2.5: If I understand these sections correctly, it is assumed that no exchange of CO2 occurs while the soil/sediment is exposed. This is not correct, see e.g., Faber et al. (2012) and Migné et al. (2016).
L83-86: Why were different amounts of olivine (0.5 cm layer) and basalt (1 cm layer) added? What was the chemical/mineralogical composition of the rocks? This information is needed for a meaningful comparison of the OAE potential between olivine and basalt.
L92-93: In the treated plots, the Rhizons were inserted into the mineral layer, is that correct? How did the mineral layer evolve over time? Were mineral grains mixed into deeper layers by animals? Were grains flushed away? Overgrowth by algae?
L106-107: Is such a high accuracy really possible? Is it not supposed to be ±3.6 µM (±0.0036 mM)?
L148-149: Did the added mineral layer have the same porosity as the underlying sediment? If not, why was a 2 cm layer used for the porosity calculation?
Section 2.6: Equation 10 is written in a very unclear way. I assume that “DIC/TA” represents “DIC” or “TA”, but it could also mean the DIC concentration divided by the TA concentration. To avoid confusion, use a more generic form in the equation, e.g., C, and explain in the text that C is the concentration of DIC or TA. Furthermore, the outwelling calculation does not seem correct. Neubauer and Anderson (2003) based their calculations on hourly data of “marsh-produced DIC”; which in turn was calculated as the difference between the DIC concentration in the riverine input and the DIC concentration in one of the salt marsh creeks. In equation 10, the value used is not an excess DIC or TA concentration (produced in the marsh), but instead the total measured DIC or TA concentration. This assumes that water with 0 µM DIC enters the marsh, where ~2500 µM DIC is added and then exported to the ocean. The outwelling results are thereby highly overestimated.
Section 2.7: Both DIC and CO2 are used and compared throughout the manuscript. To facilitate comparison, I suggest that (1) the sediment-water flux is shown as DIC, and (2) that the water-atmosphere CO2 flux is given in mols instead of grams.
L219-221: It is unclear whether the numbers given across the different cases represent average values or the variation (or range) of values for the specified time points.
L244-245: Please add a reference here; anaerobic respiration processes produce both DIC and TA.
Section 3.5: Were any statistical tests done on the outwelling results? Based on Figure 6, I highly doubt that the outwelling of TA and DIC from the treated plots was generally higher than from the controls.
Section 3.6: Here, water-atmosphere CO2 fluxes are presented, but they are consistently described as “mass”. Please correct.
L350-354: This passage is hard to follow and seems to be partly incorrect. The reoxidation of sulfide consumes the TA that was produced during sulfate reduction, but this is not the main reason for the differences in TA:DIC ratio between porewater and overlying water in marsh systems. While considerable amounts of DIC are produced in the porewater, lowering the ratio, the overlying water is often mixed with water from other sources with a TA:DIC ratio >= 1 (Reithmaier et al., 2023).
L370-373: Are these differences between treatments statistically significant? Figure 5 shows a considerable spread in the data. Do you still see trends if these error bars are considered?
L401-404: Based on the data presented and considering the statistics, I do not believe that this can be concluded.
L406: Previously, “BF” has been used rather than “Durubas”.
Figure 2: Please add uncertainties to values that are averages of multiple replicates.
Figure 4: I suggest the authors add a horizontal line at TA:DIC = 1.
Figure 6: Panel b is on top of panel a; consider changing this for a more logical flow.
Figure 7: According to the text, the graphs do not show the mass but the fluxes – the y-axis titles should be corrected accordingly. Please add uncertainties on the bars.
Figure S5: The unit for the DIC is µmol/kg, whereas µM (µmol/L) is used for TA in the main text. Please be consistent and ensure that the TA:DIC ratios are calculated using the same units.
References
Faber, P. A., Kessler, A. J., Bull, J. K., McKelvie, I. D., Meysman, F. J. R., and Cook, P. L. M.: The role of alkalinity generation in controlling the fluxes of CO2 during exposure and inundation on tidal flats, Biogeosciences, 9, 4087–4097, https://doi.org/10.5194/bg-9-4087-2012, 2012.
Migné, A., Davoult, D., Spilmont, N., Ouisse, V., and Boucher, G.: Spatial and temporal variability of CO2 fluxes at the sediment–air interface in a tidal flat of a temperate lagoon (Arcachon Bay, France), J. Sea Res., 109, 13–19, https://doi.org/10.1016/j.seares.2016.01.003, 2016.
Reithmaier, G. M. S., Cabral, A., Akhand, A., Bogard, M. J., Borges, A. V., Bouillon, S., Burdige, D. J., Call, M., Chen, N., Chen, X., Cotovicz, L. C., Eagle, M. J., Kristensen, E., Kroeger, K. D., Lu, Z., Maher, D. T., Pérez-Lloréns, J. L., Ray, R., Taillardat, P., Tamborski, J. J., Upstill-Goddard, R. C., Wang, F., Wang, Z. A., Xiao, K., Yau, Y. Y. Y., and Santos, I. R.: Carbonate chemistry and carbon sequestration driven by inorganic carbon outwelling from mangroves and saltmarshes, Nat. Commun., 14, 8196, https://doi.org/10.1038/s41467-023-44037-w, 2023.
Citation: https://doi.org/10.5194/egusphere-2025-4555-RC3 -
AC3: 'Reply on RC3', Isabel Mendes, 07 Jan 2026
This manuscript details a study on the application of olivine and basalt to salt marsh sediments to evaluate their effectiveness for ocean alkalinity enhancement (OAE). The research is highly relevant and timely, given the rarity of field trials in OAE. While the overall design and duration of the experiment make the study interesting, there are issues in data processing that need to be resolved. The study would also benefit from clearer contextualisation and the inclusion of additional data, which is available according to the methods section. There are currently several claims in the text that I believe are not supported by data.
We thank the reviewer for their careful evaluation of the manuscript and for their positive assessment of the relevance and importance of this field-based study. We appreciate the recognition of the novelty of conducting an ocean alkalinity enhancement (OAE) field trial, which are rarely pursued. We have carefully considered all comments and suggestions provided by the reviewer and will revise the manuscript accordingly to improve clarity, structure, and data presentation.
Regarding the availability of additional data, we note that the field experiment generated a broader dataset, including nutrient measurements. Due to the complexity and scope of these data, we have decided to publish the results separately (Cravo et al., 2025, Marine Environmental Research, currently under review) to allow for a more comprehensive and focused interpretation of nutrient dynamics. The present manuscript focuses specifically on changes in alkalinity and carbonate system parameters and therefore did not include the nutrient data.
Metal concentrations are currently under analysis, and they are not accomplished to date due to technical issues with laboratory equipment. These data will be addressed in a future publication once they are available.
Major comments:
The manuscript currently presents data on total alkalinity (TA), pH, and calculated concentrations of dissolved inorganic carbon (DIC). It is difficult to draw conclusions about the system's functioning and the impact of the added minerals from these parameters alone. However, according to the methods section, samples for nutrients and metals were also collected (L94-95). Including these data would greatly help interpret seasonal trends and understand natural TA production in the area. Any solid-phase data that might be available would be equally valuable. If data on the permanence/spread of/fate of the added minerals are not available, I suggest the authors still discuss this to the best of their ability, to understand the added minerals’ contribution to the sedimentary TA release.
Samples for nutrients and metals were also collected, but were not included in this study. The metal data are still being analysed, and the nutrient data have been used for another publication which has recently been submitted to another journal (see above). In the nutrient data, we observed similar trends as in the alkalinity, mostly in porewater, with higher fluxes during the first 3 months of the experiment. The results are going to be published in Marine Environmental Research.
Regarding the solid-phase data, we have doubts about the reviewer point. In our study, we confined the substrates by wooden frames, which were inserted in the sediment (~10 cm) and protruded 2-3 cm from the ambient sediment surface to prevent dispersion of the mineral grains. According with our observations, as the pioneer vegetation zone is a very stable area with rather weak current velocities. We also observed that the substrates remained inside the frames during the entire experimental period. In addition, sediment samples collected from each treatment, to be used for analyses of benthic foraminiferal faunas, by using a transparent plastic push corer, clearly showed the surficial substrate layer with the same thickness as it has been deployed. To clarify this part a new sentence will be added to Subchapter 2.1.
The statistical treatment of the data and the presentation of results from statistical tests should be improved. Please ensure that summary tables for any relevant statistical tests, such as ANOVAs, are presented (at least in the supplementary materials). Also, consider the suitability of the statistical tests for the data. From certain parts of the text (e.g., L276-278), it appears that ANOVAs were conducted for each month. If this is the case, the tests do not permit conclusions about the overall impact of olivine and basalt over the year (only for each specific month), and the obtained p-values could be less reliable due to multiple comparisons. Furthermore, ANOVAs are generally not appropriate for time series data. I suggest that the authors consider using alternative statistical models, such as linear mixed models.
We believe this concern is based on a misunderstanding, and we thank the reviewer for the opportunity to clarify our approach. The two-way ANOVA was not conducted separately for each month. Instead, all ANOVA analyses were performed with data covering the full experimental period (either the first six months or the first year), including all treatments and plots. As described in the manuscript, time was defined as a categorical factor in the two-way ANOVA, allowing us to assess treatment effects over the long-term experimental scale, and to elucidate interactions between treatment and time. This approach accounts for repeated observations of the same plots over multiple months and avoids inflation of Type I error rates that would arise from conducting independent tests for each sampling time. A sentence in the revised version of this sub-section will clarify that two-way ANOVA with repeated measures was used, as an appropriate statistical analysis to our data.
In contrast, and to directly compare two treatments at a specific sampling month, we applied two-sample t-tests, which are appropriate for pairwise comparisons at individual sampling times. We are going to revise (Statistical analysis Subchapter) to explicitly state that two-way ANOVA was used exclusively for long-term analyses across the experimental period, whereas t-tests were applied only for direct, month-specific treatment comparisons. We agree that alternative statistical approaches, such as linear mixed-effects models, can be suitable for time-resolved datasets. However, given the experimental design, balanced sampling, and limited number of replicate plots, we consider the applied ANOVA framework (with repeated measures) to be appropriate for addressing the primary research questions of this study.
In general, the importance of the results needs to be scrutinised. There appears to be an issue with equation 10, which inflates the outwelling values. Throughout the text, there are statements about results from treatment being different, without it being clear whether the differences are statistically significant (in most cases, the figures suggest they are not). Because of these issues in data interpretation, the authors conclude that olivine and basalt drive OAE in this natural system. Based on the data, I currently do not agree that this claim is justified. If data do not show significant differences between treatments, please discuss why (since trends often are seen in laboratory experiments) – is it a question about natural variations masking the OAE, are the minerals dissolving too slowly, or is the TA lost somehow?
We believe this is a misunderstanding. We stated that olivine and basalt treatments increased the alkalinity of ambient waters, but only during a short period after deployment, and that the alkalinity generation decreased thereafter. We offered an explanation for why this could be the case. However, the material remains visible for the first six months after deployment. We have discussed this, and we also explained that the TA and DIC are outwelled to the channel and ultimately exported to the ocean.
Laboratory studies are a crucial first step for such experiments. However, trends observed under controlled laboratory conditions cannot always be replicated under natural conditions, where many other and also interacting factors play an important role. As our study is a field experiment conducted under natural environmental conditions, the observed results may therefore differ from those reported from laboratory-based studies.
Detailed comments:
L14-15: Please modify this statement to better represent the data. While the TA increased immediately after the addition of olivine and basalt (L14-15), this effect was transient, and no difference was observed between treatments after a few months.
We agree. The sentence will be reformulated for clarity.
L79-82: Did the addition of frames cause the plots to be constantly submerged by 2-3 cm of water, even though the soil/sediment would normally have been exposed ~70% of the time? If so, I would have expected the porewater chemistry to change substantially over the course of the experiment compared to “normal” conditions.
As detailed above, the frames were only used to prevent the substrates from dispersing. The supernatant surface water was collected when the tide was falling. The natural sediment underneath is mainly composed of silt and fine sand, and water percolates through it very quickly. As such, the frames dried out a few minutes after emergence. Practically, the team had only 15–30 minutes to collect all the surface water samples from the 15 experimental fields.
Even though we have already mentioned the submergence times in the manuscript (Lines 80-81) We are going to put more emphasis on this fact in the revised manuscript and specify that we have taken submersion time into account for the flux calculations.
Sections 2.4-2.5: If I understand these sections correctly, it is assumed that no exchange of CO2 occurs while the soil/sediment is exposed. This is not correct, see e.g., Faber et al. (2012) and Migné et al. (2016).
We did not calculate the flux between the PW and the atmosphere during the period of emergence. We are aware that CO₂ is released from the sediments into the atmosphere, but this could not be captured with the experimental set-up and sampling procedure as explained above. Therefore, we only considered water samples. However and taken the reviewers' concern into account, we will add a new sentence to the respective sections in Subchapters 2.4 and 2.5, including the cited references.
L83-86: Why were different amounts of olivine (0.5 cm layer) and basalt (1 cm layer) added? What was the chemical/mineralogical composition of the rocks? This information is needed for a meaningful comparison of the OAE potential between olivine and basalt.
This is explained in our previously published paper Mendes et al., 2025 - https://doi.org/10.1029/2024JG008591, there Section 2.2.1. Grain Size and Mineralogical Composition of the Deployed Minerals.
L92-93: In the treated plots, the Rhizons were inserted into the mineral layer, is that correct? How did the mineral layer evolve over time? Were mineral grains mixed into deeper layers by animals? Were grains flushed away? Overgrowth by algae?
Yes, there was bioturbation, e.g. mm-sized worm borrows, and a transient overgrowth of filamentous algae in winter, but we had a stable layer of material where the rizhones were inserted. Therefore, these effects can be considered negligible.
L106-107: Is such a high accuracy really possible? Is it not supposed to be ±3.6 µM (±0.0036 mM)?
We reported the accuracy of triplicate measurements of the Dickson Alkalinity Standard not that of the actual measurements. We will change the sentence accordingly.
L148-149: Did the added mineral layer have the same porosity as the underlying sediment? If not, why was a 2 cm layer used for the porosity calculation?
The natural sediment porosity differs from the porosity of the deployed material. Because the experimental boxes provided only limited space and material volume, sediment sampling had to be restricted, and samples were re-used whenever possible. For diatom sampling, we used a standard sediment corer, and samples were weighed immediately after collection. The samples were then used to capture motile diatoms. After 24 hours, the samples were dried in an oven for 48 hours and weighed again. This approach allowed us to minimise sediment removal from the experimental boxes. The standard sampling depth for diatoms is 2 cm, which was applied in this study. Consequently, the samples contained a larger proportion of original sediment rather than only the surface layer. This also allows us to account for bioturbation, which naturally alters sediment porosity and promotes sediment mixing over time.
We assume a porosity of between 26 and 48 %, which is typical for any mineral sand with a narrow grain size range as our material has (e.g. Román-Sierra et al., 2014). The porosity of the natural surface sediment in the Spartina pioneer vegetation zone varies from 60 to 75 %. We observed numerous worm burrows and therefore consider that bioturbation has effected a higher permeability of the substrate-sediment interface, also leaving numerous voids in the mud underneath. As such it is justified to use the bulk sediment porosities of the 0-2 cm diatom samples for flux calculations. Their porosities were calculated from the known volume of 2.66 cm3 and their weight loss during drying in an oven for 48 hours.
Section 2.6: Equation 10 is written in a very unclear way. I assume that “DIC/TA” represents “DIC” or “TA”, but it could also mean the DIC concentration divided by the TA concentration. To avoid confusion, use a more generic form in the equation, e.g., C, and explain in the text that C is the concentration of DIC or TA. Furthermore, the outwelling calculation does not seem correct. Neubauer and Anderson (2003) based their calculations on hourly data of “marsh-produced DIC”; which in turn was calculated as the difference between the DIC concentration in the riverine input and the DIC concentration in one of the salt marsh creeks. In equation 10, the value used is not an excess DIC or TA concentration (produced in the marsh), but instead the total measured DIC or TA concentration. This assumes that water with 0 µM DIC enters the marsh, where ~2500 µM DIC is added and then exported to the ocean. The outwelling results are thereby highly overestimated.
We agree with the reviewer that the formulation of Equation 10 can be misunderstood. To avoid any ambiguity, we are going to modify the equation by replacing “DIC/TA” with the generic term C, and we will state in the text that C represents either DIC or TA concentration, depending on the parameter being evaluated. We acknowledged in Lines 164 and 165 that our outwelling calculation represents an adaptation of the approach proposed by Neubauer and Anderson (2003) to fit the specific design of our experimental setup. In their study, outwelling was estimated using the difference between riverine input concentrations and concentrations measured within salt-marsh creeks, with the objective of determining whether the marsh acts as a source or sink of DIC. Following the same conceptual framework, our aim was to assess whether our experiment or the salt marsh in general acts as a net source or sink of TA or DIC with reference to the adjacent channel. To do so, we compared surface water within the experimental boxes, which interacted with porewater and the applied substrates during low tide, with the incoming tidal water, which has chemical characteristics similar to the Atlantic water. We agree that this approach does not quantify marsh-produced excess DIC or TA in the strict sense used by Neubauer and Anderson (2003), but rather provides an estimate of the net exchange of TA and DIC between the experiment and the tidal water. A sentence will be added to the respective paragraph in the revised version of the paper in order to explain the above mentioned limitations.
Section 2.7: Both DIC and CO2 are used and compared throughout the manuscript. To facilitate comparison, I suggest that (1) the sediment-water flux is shown as DIC, and (2) that the water-atmosphere CO2 flux is given in mols instead of grams.
This is probably a misunderstanding. Subchapter 2.7 belongs to the Methods section of the paper and not to the Results. We estimated the annual mass budget of CO₂ in grams per year of our considerable small experimental area to facilitate a comparison with other studies that discuss how much atmospheric CO₂ can be sequestered in terms of tonnes per year.
L219-221: It is unclear whether the numbers given across the different cases represent average values or the variation (or range) of values for the specified time points.
The values reported represent the range of total alkalinity (TA) values obtained at a specific sampling time (i.e. the highest value minus the lowest value recorded each month) over the first year of the experiment, rather than mean values. We acknowledge that the original wording was unclear and may have led to misinterpretation. We are therefore going to revise the sentence to explicitly state that the reported values refer to variation of TA at a specific sampling time.
L244-245: Please add a reference here; anaerobic respiration processes produce both DIC and TA.
We will cite Raymond et al. (2000) here.
Section 3.5: Were any statistical tests done on the outwelling results? Based on Figure 6, I highly doubt that the outwelling of TA and DIC from the treated plots was generally higher than from the controls.
Yes, statistical analyses were performed on the outwelling estimates. We applied a two-way ANOVA with repeated measurements including treatment and replicate plot as factors to test for differences in TA and DIC outwelling between control and treated plots over the experimental period. The analyses showed no statistically significant differences in outwelling of either TA or DIC between the treated plots and the controls (p > 0.05). We agree with the reviewer that this is consistent with the patterns shown in Figure 6. We are going to revise Section 3.5 and report the statistical results. Within the duration of this field experiment, outwelling from treated plots was not significantly higher than from the controls.
Section 3.6: Here, water-atmosphere CO2 fluxes are presented, but they are consistently described as “mass”. Please correct.
We thank the reviewer for pointing this out and apologise for the confusion. In Section 3.6, we calculated the mass of CO2 produced in our experimental boxes by integrating the water-atmosphere CO2 fluxes, following the approach described in Section 2.8. To avoid misinterpretations, we will correct the CO2 fluxes to mass fluxes of CO2 when expressed in g per year.
L350-354: This passage is hard to follow and seems to be partly incorrect. The reoxidation of sulfide consumes the TA that was produced during sulfate reduction, but this is not the main reason for the differences in TA:DIC ratio between porewater and overlying water in marsh systems. While considerable amounts of DIC are produced in the porewater, lowering the ratio, the overlying water is often mixed with water from other sources with a TA:DIC ratio >= 1 (Reithmaier et al., 2023).
This is a misunderstanding induced by unclear wording. The last part of the Line 351-351 sentence rather should read: "sulphate and thereby reduces the TA by its proportion of sulphidic compounds." We are going to amend this in the revised version of the manuscript as following “Once the sulphide passes the near-surface oxic zone, it is oxidized to sulphate and thereby reduces the TA by its proportion of sulphidic components”.
L370-373: Are these differences between treatments statistically significant? Figure 5 shows a considerable spread in the data. Do you still see trends if these error bars are considered?
Yes, the differences between treatments were statistically significant during the first six months of the experiment (p < 0.05). After this initial period, the differences were no longer significant, which is consistent with the patterns shown in Figure 5, although the Figure shows a considerable data spread.
L401-404: Based on the data presented and considering the statistics, I do not believe that this can be concluded.
Indeed, there is no significant difference after one year, but during the first 6 months, the basalt treatments performed better.
L406: Previously, “BF” has been used rather than “Durubas”.
Durubas is the commercial designation for BF. This is specified in Lines 85-86 but we will add BF between brackets in the revised version of the manuscript.
Figure 2: Please add uncertainties to values that are averages of multiple replicates.
We appreciate the reviewer’s suggestion. Figure 2 is intended to provide contextual background conditions (control and tidal waters) rather than to illustrate treatment effects. Variability in alkalinity and pH is already presented in detail in Figure 3 and in the supplementary Figure S4. To avoid redundancy and overcrowding in Figure 2, we have therefore retained the original presentation, and we have clarified this rationale in the figure caption.
Figure 4: I suggest the authors add a horizontal line at TA:DIC = 1.
This line is going to be added in the revised version of Figure 4.
Figure 6: Panel b is on top of panel a; consider changing this for a more logical flow.
We accept the reviewer suggestion. We are going to change this.
Figure 7: According to the text, the graphs do not show the mass but the fluxes – the y-axis titles should be corrected accordingly. Please add uncertainties on the bars.
We thank the reviewer for this comment. Figure 7 presents CO₂ mass fluxes, which was calculated by integrating the water–atmosphere CO₂ fluxes over time, as described in Section 2.8. We acknowledge that the y-axis labels were unclear and may have suggested fluxes rather than mass fluxes. The axis titles are therefore to be corrected to clearly indicate the CO₂ mass produced and the appropriate units (g/m2/year).
Figure S5: The unit for the DIC is µmol/kg, whereas µM (µmol/L) is used for TA in the main text. Please be consistent and ensure that the TA:DIC ratios are calculated using the same units.
We thank the reviewer for spotting this inconsistency in units. Total alkalinity (TA) was measured in µM (µmol L⁻¹), whereas dissolved inorganic carbon (DIC) was calculated using CO2SYS (version 25b06; Lewis and Wallace, 1998) from TA, pH, temperature, salinity, and nutrient concentrations, and is reported by default in µmol kg⁻¹. For the calculation of TA:DIC ratios, both parameters were converted to the same units to ensure consistency.
References
Faber, P. A., Kessler, A. J., Bull, J. K., McKelvie, I. D., Meysman, F. J. R., and Cook, P. L. M.: The role of alkalinity generation in controlling the fluxes of CO2 during exposure and inundation on tidal flats, Biogeosciences, 9, 4087–4097, https://doi.org/10.5194/bg-9-4087-2012, 2012.
Migné, A., Davoult, D., Spilmont, N., Ouisse, V., and Boucher, G.: Spatial and temporal variability of CO2 fluxes at the sediment–air interface in a tidal flat of a temperate lagoon (Arcachon Bay, France), J. Sea Res., 109, 13–19, https://doi.org/10.1016/j.seares.2016.01.003, 2016.
Raymond, P., Bauer, J., and Cole, J.: Atmospheric CO2 evasion, dissolved inorganic carbon production, and net heterotrophy in the York River Estuary, Limnology and Oceanography, 45, 1707–1717, https://doi.org/10.4319/lo.2000.45.8.1707, 2000.
Reithmaier, G. M. S., Cabral, A., Akhand, A., Bogard, M. J., Borges, A. V., Bouillon, S., Burdige, D. J., Call, M., Chen, N., Chen, X., Cotovicz, L. C., Eagle, M. J., Kristensen, E., Kroeger, K. D., Lu, Z., Maher, D. T., Pérez-Lloréns, J. L., Ray, R., Taillardat, P., Tamborski, J. J., Upstill-Goddard, R. C., Wang, F., Wang, Z. A., Xiao, K., Yau, Y. Y. Y., and Santos, I. R.: Carbonate chemistry and carbon sequestration driven by inorganic carbon outwelling from mangroves and saltmarshes, Nat. Commun., 14, 8196, https://doi.org/10.1038/s41467-023-44037-w, 2023.
Román-Sierra,J., Muñoz-Perez, J.J., and Navarro-Pons, M.: Beach nourishment effects on sand porosity variability, Coastal Engineering, 83, 221–232, https://doi.org/10.1016/j.coastaleng.2013.10.009.
Citation: https://doi.org/10.5194/egusphere-2025-4555-AC3
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AC3: 'Reply on RC3', Isabel Mendes, 07 Jan 2026
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Overview
The manuscript “Evaluating ocean alkalinity enhancement for carbon dioxide removal: evidence from a one-year saltmarsh field experiment” tests basalt and olivine for their suitability for OAH in-situ at a saltmarsh. While the manuscript presents an interesting and comprehensive dataset, some of the calculations rely on very simplified approaches e.g..CO2 emissions are calculated based on TA and pH measurements, and outwelling based on concentration differences between inside and outside the plots. This information is still valuable, but authors have to be more careful when presenting and comparing this data. See comments below.
General comments
Your abstract/discussion and title are not well aligned. Introducing CO2 fluxes and outwelling independently seems disconnected. Put them always into perspective to OAH .
Calculating CO2 fluxes based on calculated pCO2 from alkalinity and pH seems like a stretch. Saltmarshes likely have high organic alkalinity messing up co2sys calculations and pH measurements tend to be very unreliable. You could make a sensitivity analysis to see how calculated pCO2 values change when assuming organic alkalinity to be 1-5% (remove from TA when calculating CO2) and accounting for the pH precision (use pH plus and minus precision). Then you could report a range for pCO2 and corresponding fluxes. Same for calculated DIC.
Outwelling/lateral flux calculations ignore porewater/groundwater fluxes, which are a major drivers of carbon outwelling in saltmarshes. Your calculations are still interested but be more specific in the abstract and discussion. E.g., “Saltmarshes were source of TA at low tide as indicated by elevated TA concentrations inside the plots compared to external seawater.” Right now abstract reads as if you did ecosystem scale measurement. To report outwelling in mmol/m2/d when you only calculated for such a short amount of time is not valid. You have to report in per hour and always add “at ebb tide”.
Comments by line
L15 Set this into context of the basalt/olivine addition or remove.
L16-17 Why did control have lower CO2 fluxes despite higher TA?
L17-18 Was outwelling different between treatments?
L24 Change to “might” be necessary
L49 km2 superscript
L47 – 64 This should be under Methods: 2.1 Study site
L64-70 Reduce methodological details. Describe aims and hypothesis.
L71 Not entire caption in bold. Nice map!
L91 Remove minus before ” - ml”
L91 For which parameters which vials/beakers?
L93 Why porewater extracted so shallow? Top 1 cm likely mixture of porewater and water sitting on top.
L97 remove ) after YSI‐381
L98 Need accuracy of instrument not the buffer solution.
L106 What is precision?
L109 Report constants.
L190 Split section in smaller paragraphs. Some for rest of manuscript to improve readability.
L211 Remove variability and comma before from.
Fig 3. I wonder of delta TA (treatment – control) would be more informative. Maybe you could add two more subplots. For panel a, could you use a shorter y scale. It is very hard so see differences. Same for all other figures. Would adapt y axis to data of each plot.
Round to significant digits throughout results.
L314-316 This is interesting and could be mentioned in abstract.
L322-330 Repetition of results. Shorten.
L330 Or is the alkalinity decrease just caused by substrate being washed away over time. If not over the surface maybe over porewater fluxes.
L385-399 Outwelling would not be order of magnitude higher if fluxes from high tide would be accounted for. Cannot compare your fluxes to other sites that measured ecosystem scale outwelling. Focus more on the differences between treatments than on actual numbers.
L400-401 Important finding should be in the abstract.