Impacts of water advection and CO<sub>2</sub> exchanges on the carbon dioxide removal potential of ocean alkalinity enhancement

Moras, Charly A.; Saez Moreno, Matias; Bartsch, Peggy; Hartmann, Jens

doi:10.5194/egusphere-2025-6144

Preprints

https://doi.org/10.5194/egusphere-2025-6144

Preprints

16 Jan 2026

| 16 Jan 2026

Impacts of water advection and CO₂ exchanges on the carbon dioxide removal potential of ocean alkalinity enhancement

Charly A. Moras, Matias Saez Moreno, Peggy Bartsch, and Jens Hartmann

Abstract. Ocean alkalinity enhancement is a carbon dioxide removal strategy with high CO₂ uptake potential and rather low cost. Long term modelling studies have focused on this strategy, but most laboratory experiments focus on shorter term with strong advection, which may not be representative of natural systems. Hence, the long-term fate of alkalinity is yet to be addressed. Also, the role of CO₂ ingassing is still largely overlooked. In a new setup, 6-month experiments using solid Ca(OH)₂ and Mg(OH)₂, and liquid NaOH have been conducted with a constant supply of CO₂. Bottles were either kept stagnant or exposed to slow advection. All experiments revealed lower measured TA compared to expected, but bottles subjected to advection led to nearly twice as much TA generation in some cases and significantly faster CO₂ ingassing rates. This led to a quicker equilibration, decreasing the low CO₂ period, lately identified as a potential threat to living organisms, and a decreased critical alkalinity period (CAP) for CaCO₃ formation. Yet, CaCO₃ precipitated in most bottles, either as needles with Ca(OH)₂ or as “broccolis” with Mg(OH)₂. Such broccoli resulted most likely from precipitation on slowly dissolving Mg(OH)₂ particles. Once the CAP was over, conditions remained stable with no redissolution of the CaCO₃ precipitates. Using NaOH revealed buffering by Mg(OH)₂ precipitation, which ultimately redissolved in the bottles exposed to advection. Finally, the bottles exposed to advection represented open ocean conditions with wind speeds of ~3 m s^-1, which, given the calm state of the ocean, may serve as a lower threshold for implementation in global models.

Received: 09 Dec 2025 – Discussion started: 16 Jan 2026

Competing interests: Jens Hartmann is consulting the Planeteers GmbH.

Publisher's note: Copernicus Publications remains neutral with regard to jurisdictional claims made in the text, published maps, institutional affiliations, or any other geographical representation in this paper. While Copernicus Publications makes every effort to include appropriate place names, the final responsibility lies with the authors. Views expressed in the text are those of the authors and do not necessarily reflect the views of the publisher.

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Journal article(s) based on this preprint

26 Oct 2026

Impacts of water advection and CO₂ exchange on the carbon dioxide removal potential of ocean alkalinity enhancement

Charly Andre Moras, Matias Saez Moreno, Peggy Bartsch, and Jens Hartmann

Biogeosciences, 23, 7523–7544, https://doi.org/10.5194/bg-23-7523-2026,https://doi.org/10.5194/bg-23-7523-2026, 2026

Short summary

Charly A. Moras, Matias Saez Moreno, Peggy Bartsch, and Jens Hartmann

Interactive discussion

Status: closed

RC1:
'Comment on egusphere-2025-6144', Anonymous Referee #1, 11 Feb 2026

Dear authors,
Please find attached my reviewer comments.
Best regards

Citation: https://doi.org/10.5194/egusphere-2025-6144-RC1
- AC1: 'Reply on RC1', Charly Moras, 31 Mar 2026
  
  Dear Reviewer 1,
  Thank you for your review. We have worked on addressing every single one of your comments in the file attached.
  Kind regards,
  Charly Moras, on behalf of all co-authors
  
  Citation: https://doi.org/10.5194/egusphere-2025-6144-AC1
RC2:
'Comment on egusphere-2025-6144', Anonymous Referee #2, 01 Mar 2026

General comments
The manuscript addresses an interesting topic; the potential of ocean alkalinity enhancement in removing CO₂ using laboratory experiments. However, in its current form, the manuscript requires substantial revision before it can be considered for publication.
The introduction would benefit from a more comprehensive and critical engagement with the existing literature. At present, it does not sufficiently synthesize prior work or clearly articulate how this study advances the field. Expanding the literature review, deepening the discussion of competing models, and broadening the citation base beyond a limited subset of recurring studies would significantly strengthen the manuscript. Currently the manuscript relies on a relatively small subset of studies, including multiple self-citations.
More broadly, while the authors introduce new experimental variables that move in a promising and appropriate direction, the methodological rigor with which these experiments were conducted and documented is currently insufficient to clearly demonstrate advancement beyond previous studies. As presented, it remains unclear whether the modifications—such as extended experimental duration and altered mixing conditions—translate into meaningful new insights or improved constraints on the processes under investigation. Strengthening the experimental design, documentation, and quantitative analysis would help clarify the extent to which this study advances our understanding of these issues.
Several aspects of terminology and conceptual framing require refinement. In multiple instances, terms are used in ways that may not align with their standard definitions. Improving precision in terminology and clarifying key concepts would enhance the scientific rigor of the manuscript. For example, “advection” and “laboratory stirring” are not the same thing. Similarly, phrases such as “due to the non-dissolution of CaCO3 in seawater” is both unclear and strange.
The experimental design and quality control procedures also require clearer documentation. Additional methodological detail and justification would strengthen confidence in the robustness and reproducibility of the results. There are certain aspects of the methodology that left me wondering if these experiments were done in the most rigorous way possible. For example, I was shocked to read that that MilliQ was added to compensate for evaporation. Why MilliQ and not seawater? How much was added? No documentation of this effect is presented. There are also no controls to compare to. These are all serious problems.
Another thing about the structure of the manuscript, I am unclear why the figures are placed in an Appendix rather than integrated into the main text. Presenting figures within the main manuscript would improve readability and allow readers to more easily follow the argument.
The section discussing wind speed and advection rate is a promising step toward connecting laboratory experiments with real-world conditions. However, this analysis currently feels incomplete. It would be valuable to fully develop this approach—potentially by solving the mentioned equations and presenting a figure that explicitly relates the experimental mixing conditions to realistic environmental scenarios. This would substantially strengthen the broader relevance of the study.

Detailed comments
Line 15 The terms “needles” and “broccolis” are informal and not standard terminology for crystal morphology. Please revise using conventional mineralogical or crystallographic terms.

Line 37 The description of “runaway precipitation” needs clarification. This term typically refers to the extent of reaction and the resulting decrease in total alkalinity, rather than necessarily implying an increase in precipitation rate over time. Please clarify whether there is direct evidence for changing reaction rates.

How was it determined that two hours of UV exposure was sufficient to prevent microbial growth? Were control experiments performed? Providing more detail on these points would strengthen the methodological rigor of the study.

Line 101 Please clarify the reference to “Carl Roth” (e.g., supplier name and location).

Line 123 The values reported here appear to represent variability rather than analytical error. Were samples analyzed in replicate? Please report the standard deviation (or other relevant metric) of replicate analyses.

Line 151 The discussion of quality control procedures is difficult to follow. Please clarify how analytical precision, accuracy, and reproducibility were assessed. I have no idea what the authors are talking about here.

Line 290 The statement regarding previous studies and the use of stir bars may need revision. Not all prior studies relied on stir bars, and the use of a shaking table may not constitute a substantial methodological innovation.

Citation: https://doi.org/10.5194/egusphere-2025-6144-RC2
- AC2: 'Reply on RC2', Charly Moras, 31 Mar 2026
  
  Dear Reviewer 2,
  Thank you for your review. We have worked on addressing every single one of your comments in the file attached.
  Kind regards,
  Charly Moras, on behalf of all co-authors
  
  Citation: https://doi.org/10.5194/egusphere-2025-6144-AC2

Peer review completion

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

ED: Reconsider after major revisions (31 Mar 2026) by Tina Treude

AR by Charly Moras on behalf of the Authors (04 May 2026) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (14 May 2026) by Tina Treude

RR by Gunter Flipkens (25 May 2026)

Suggestions for revision or reasons for rejection

The authors have carefully revised the manuscript by addressing the reviewers’ comments and conducting additional analyses (mineral grain size and specific surface area), which is appreciated. The manuscript has improved substantially. However, some methodological details remain unclear or insufficiently described, several interpretations would benefit from more nuanced wording, and I believe that the section linking laboratory results to modelling studies would benefit from restructuring to improve clarity and focus. Detailed comments are provided below.

Line 171: A space is missing between “50” and “mL”. Please carefully check the manuscript for additional spacing inconsistencies.

Line 175: Please elaborate on how Meas. TAloss and Max. TAloss were calculated. Based on the values reported in Table 1 and Figure 4 for the 600 µmol kg⁻¹ Mg(OH)₂ treatment, the calculations are not immediately clear. For example, for the 0 RPM Mg600 treatment, I would expect the measured TA loss to be approximately 770 µmol kg⁻¹ (target addition of 600 µmol kg⁻¹ minus an observed ΔTA of roughly −170 µmol kg⁻¹), assuming full dissolution of Mg(OH)₂. However, Table 1 reports values closer to ~230 µmol kg⁻¹. If Meas. TAloss is instead based on the dissolved fraction of Mg(OH)₂, please clarify how this fraction was derived, especially since some precipitation likely already occurred within the first day in the static high-concentration treatments, as suggested by the non-linear ΔTA response with increasing Mg(OH)₂ addition.

Materials & Methods: Please include a short subsection describing the statistical analyses performed taking into account my later comment about the statistics.

Line 214: Please specify what the error bars represent (e.g. standard deviation, standard error, or range).

Line 285: For consistency and clarity, also indicate here that values are presented as mean ± standard deviation.

Line 336: Add “within one day” after “92% of the expected TA”.

Line 371: I recommend citing your paper Moras et al. (2022) on runaway precipitation here, along with other relevant studies discussing this phenomenon. This would help readers unfamiliar with the concept locate the relevant background literature more easily.

Lines 435–437: These statements should be phrased more carefully. Persistent low-pCO₂ waters may still occur in nearfield regions around outfalls with continuous alkalinity dosing (assuming regulations permit such conditions). In addition, dilution/water mixing should play a larger role than atmospheric CO₂ uptake in restoring pCO₂ of an alkalinized seawater patch, since air–sea equilibration is comparatively slow. While dilution is mentioned later in the paragraph, I recommend already mentioning it earlier to provide a more balanced interpretation. A similar comment applies to lines 443–445.

Line 438: The sentence discussing literature mesocosm studies should be integrated into the preceding paragraph discussing literature results (lines 428–432) to improve coherence. The subsequent comparison with toxicological thresholds could then also be generalized, since the experimental pCO₂ values were higher than the toxicity thresholds (~100 µatm) observed in the other phytoplankton studies as well.

Line 389 onward + Figure 8: As a general rule, new experimental results should not be introduced in the discussion section. I therefore recommend moving Figure 8, together with a concise description of the DIC results, to the Results section.

Lines 495–539: This section currently combines elements of Materials & Methods (detailed equation descriptions), Results (presentation of calculated values), and Discussion (comparison with literature and broader implications). This weakens the overall focus and flow of the Discussion. I therefore recommend moving the calculated k values and DIC fluxes to the Results section, potentially together with Figure 8 and the DIC results. The calculations themselves should be briefly described in the Materials & Methods section, while the full equations can be included either in the Materials & Methods or in the Supplementary Information to improve readability and maintain a clearer narrative structure.

Line 515: Remove either “first” or “initial”, since both have the same meaning.

Lines 555–556: This sentence is somewhat difficult to follow. Consider reformulating it, for example by starting with “For the 125 RPM treatment, …” to avoid repetition and improve readability.

Lines 556–558: Here again, dilution likely plays an important role in limiting CAP persistence and should not be overlooked in the discussion.

Line 558: I would avoid the term “quick” before “CO₂ ingassing”. Several studies describe air–sea CO₂ equilibration as a relatively slow process that may take weeks to years (e.g. Zhou et al., 2025, Nature Climate Change, 15(1), 59–65). Using “quick” may unintentionally give the opposite impression to non-specialist readers.

Table A1: Given the large number of comparisons performed, please clarify whether p-value adjustment was applied. Conducting many independent two-sample t-tests across multiple concentrations and time points substantially increases the probability of type I errors (false positives). In addition, given the repeated-measures structure of the experiment (multiple observations from the same bottles over time), a linear mixed-effects model with post hoc comparisons and adjusted p-values would likely provide a statistically more robust approach than numerous independent t-tests.

Hide

RR by Anonymous Referee #3 (10 Jun 2026)

ED: Reconsider after major revisions (17 Jun 2026) by Tina Treude

AR by Charly Moras on behalf of the Authors (01 Aug 2026) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (05 Aug 2026) by Tina Treude

RR by Anonymous Referee #3 (17 Aug 2026)

RR by Gunter Flipkens (21 Aug 2026)

Suggestions for revision or reasons for rejection

The authors have put substantial effort into rewriting the manuscript and addressing the reviewers’ comments. Therefore, I only have a limited number of minor comments on the corrections, which are listed below.

Line 21: Add “these” after “but” for grammatical improvement.

Line 30: The conversion “1 Gt CO₂ = 10¹⁵ g CO₂” can be omitted. Readers can look up unit conversions themselves. You would also not state that 2350 µmol kg⁻¹ corresponds to 2.35 × 10⁻³ mol kg⁻¹, for example.

Line 32: Add “the question” before “whether”.

Line 39: Is the 500 µmol kg⁻¹ threshold only applicable under average ocean conditions, or is it also valid for regions with elevated temperature and/or salinity? Please briefly clarify this in the sentence.

Line 48: Add “formation” after “inhibit CaCO₃”.

Line 53: Since this is a newly introduced term in the OAE field, I think the definition of the CAP could be formulated somewhat more sharply. I would suggest something along the following lines:

“This transient period following alkalinity addition, during which carbonate chemistry remains substantially perturbed relative to ambient conditions, potentially promoting secondary mineral precipitation and affecting biological processes, is hereafter referred to as the critical alkalinity period (CAP).”

I think explicitly stating that the perturbations are relative to the background conditions, as well as mentioning the potential implications of the CAP (i.e., secondary precipitation and adverse effects on biological processes), would make the definition clearer.

Line 51: I feel that the comment from Reviewer 3 regarding biological risk has not yet been fully addressed. As far as I understand, Bach et al. (2019) discusses changes in the overall water-column carbonate chemistry rather than the diffusive boundary layer (DBL) surrounding feedstock particles. These represent different exposure scenarios and may therefore entail different ecological risks. A transient 500 µmol kg⁻¹ increase in TA within the microenvironment surrounding a dissolving particle is a very different exposure scenario from a 500 µmol kg⁻¹ increase throughout a large water parcel.

I therefore reiterate Reviewer 3’s question: What is the biological risk associated with perturbed microenvironments around feedstock particles? My understanding is that the risk is likely to be relatively low, except perhaps for particle-associated microorganisms that may experience these conditions directly. Please rephrase this sentence to clearly indicate whether you refer to biological effects resulting from changes in bulk water-column carbonate chemistry or those associated with changes within the DBL surrounding feedstock particles.

Section “TA manipulations and sampling procedure”: I would briefly reiterate here that two sets of experimental bottles were used for static and advected conditions, respectively. I would also mention this in the header of Table 1 to make the experimental setup clearer.

Line 227: Remove “after six months” and add “Furthermore,”. Additionally, add “at the end of the experiment” after “and mineral analyses” in line 228. This would improve clarity. Otherwise, the current wording could suggest that the TA budget was derived only after six months, whereas I understand that it was derived from the data obtained at the final sampling point.

Lines 239–241: The sentence states twice that TA generation was higher in the advected bottles than in the static bottles. Please make this more concise.

Line 262: I would move the reference to Figure 3 to the first sentence of this paragraph, since this sentence already presents the main results shown in the figure. The same applies to the first reference to Figure 2 in the first Results section, “Differences between expected and measured alkalinity using solid feedstocks.”

Line 296: “Respectively” suggests that two different ranges or values are being given for the two feedstocks (Ca(OH)₂ and Mg(OH)₂), which does not appear to be the case. I would therefore remove “respectively” and instead explicitly state when the lowest pCO₂ was observed (I.e. after 1 day).

Line 298: Please add a reference to Figure 7 here, since the NaOH results are discussed in the text but are not shown in Figure 4, which is the figure currently discussed in this paragraph.

Line 341: The k values have relatively large uncertainties due to variability in the experimental data. This uncertainty does not appear to be propagated into the calculated wind speeds (U), although I think it should be, or at least the variability in k should be acknowledged when discussing the calculated wind speeds. If you prefer to present only average values, I suggest mentioning this variability explicitly in the Discussion.

Line 580: The calculated wind speeds here do not appear to match those reported in line 341. Please verify these values.

Lines 407–409: These sentences could be formulated more clearly. In the current version, the second sentence seems to imply that a thicker DBL reduces the concentration gradient driving diffusion and lowers particle dissolution rates. I do not think this is correct. A thicker DBL would primarily reduce the diffusive flux of dissolution products away from the particle surface, potentially resulting in higher concentrations of dissolved species at the particle surface (i.e. not a lower concentration gradient as mentioned in the text). This could, in turn, increase the local saturation state and reduce the thermodynamic driving force for further particle dissolution as identified by the authors. Please revise these sentences to clarify this mechanism.

Line 411: “At 0 RPM, TA generation was up to 50% lower” — lower compared with what? Please specify the reference condition.

Line 434: Add “There,” before “the maximum” to establish a clearer link with the preceding sentence.

Lines 456–460: I am still missing a more quantitative discussion of the importance of CO₂ ingassing for secondary precipitation. I think your calculated Ω values for the bulk solution would be useful to refer to here. In the 125 RPM treatment, for example, Ω decreases from approximately 4–5 toward the control value of approximately 2.5 somewhat more rapidly than in the 0 RPM treatment, although the difference does not appear to be very large.
Given that the difference in saturation state is relatively modest, my interpretation is that the effect of advection on the DBL is likely (much) more important than the effect of CO2 ingassing for the risk and extent of secondary precipitation. If you agree with this interpretation, I suggest making the sentences revolving around the general conclusion I seem to get from this paragraph that faster CO₂ ingassing leads to substantially less secondary precipitation more nuanced.

Line 478: How could particle settling have affected CO₂ invasion? Wouldn’t advection be the more direct factor affecting CO₂ invasion? Please rephrase this sentence.

Line 539: “Addresses” should be “addressed”.

Hide

ED: Publish subject to minor revisions (review by editor) (27 Aug 2026) by Tina Treude

AR by Charly Moras on behalf of the Authors (06 Sep 2026) Author's response Author's tracked changes Manuscript

ED: Publish subject to technical corrections (25 Sep 2026) by Tina Treude

AR by Charly Moras on behalf of the Authors (01 Oct 2026) Author's response Manuscript

Interactive discussion

Status: closed

RC1:
'Comment on egusphere-2025-6144', Anonymous Referee #1, 11 Feb 2026

Dear authors,
Please find attached my reviewer comments.
Best regards

Citation: https://doi.org/10.5194/egusphere-2025-6144-RC1
- AC1: 'Reply on RC1', Charly Moras, 31 Mar 2026
  
  Dear Reviewer 1,
  Thank you for your review. We have worked on addressing every single one of your comments in the file attached.
  Kind regards,
  Charly Moras, on behalf of all co-authors
  
  Citation: https://doi.org/10.5194/egusphere-2025-6144-AC1
RC2:
'Comment on egusphere-2025-6144', Anonymous Referee #2, 01 Mar 2026

General comments
The manuscript addresses an interesting topic; the potential of ocean alkalinity enhancement in removing CO₂ using laboratory experiments. However, in its current form, the manuscript requires substantial revision before it can be considered for publication.
The introduction would benefit from a more comprehensive and critical engagement with the existing literature. At present, it does not sufficiently synthesize prior work or clearly articulate how this study advances the field. Expanding the literature review, deepening the discussion of competing models, and broadening the citation base beyond a limited subset of recurring studies would significantly strengthen the manuscript. Currently the manuscript relies on a relatively small subset of studies, including multiple self-citations.
More broadly, while the authors introduce new experimental variables that move in a promising and appropriate direction, the methodological rigor with which these experiments were conducted and documented is currently insufficient to clearly demonstrate advancement beyond previous studies. As presented, it remains unclear whether the modifications—such as extended experimental duration and altered mixing conditions—translate into meaningful new insights or improved constraints on the processes under investigation. Strengthening the experimental design, documentation, and quantitative analysis would help clarify the extent to which this study advances our understanding of these issues.
Several aspects of terminology and conceptual framing require refinement. In multiple instances, terms are used in ways that may not align with their standard definitions. Improving precision in terminology and clarifying key concepts would enhance the scientific rigor of the manuscript. For example, “advection” and “laboratory stirring” are not the same thing. Similarly, phrases such as “due to the non-dissolution of CaCO3 in seawater” is both unclear and strange.
The experimental design and quality control procedures also require clearer documentation. Additional methodological detail and justification would strengthen confidence in the robustness and reproducibility of the results. There are certain aspects of the methodology that left me wondering if these experiments were done in the most rigorous way possible. For example, I was shocked to read that that MilliQ was added to compensate for evaporation. Why MilliQ and not seawater? How much was added? No documentation of this effect is presented. There are also no controls to compare to. These are all serious problems.
Another thing about the structure of the manuscript, I am unclear why the figures are placed in an Appendix rather than integrated into the main text. Presenting figures within the main manuscript would improve readability and allow readers to more easily follow the argument.
The section discussing wind speed and advection rate is a promising step toward connecting laboratory experiments with real-world conditions. However, this analysis currently feels incomplete. It would be valuable to fully develop this approach—potentially by solving the mentioned equations and presenting a figure that explicitly relates the experimental mixing conditions to realistic environmental scenarios. This would substantially strengthen the broader relevance of the study.

Detailed comments
Line 15 The terms “needles” and “broccolis” are informal and not standard terminology for crystal morphology. Please revise using conventional mineralogical or crystallographic terms.

Line 37 The description of “runaway precipitation” needs clarification. This term typically refers to the extent of reaction and the resulting decrease in total alkalinity, rather than necessarily implying an increase in precipitation rate over time. Please clarify whether there is direct evidence for changing reaction rates.

How was it determined that two hours of UV exposure was sufficient to prevent microbial growth? Were control experiments performed? Providing more detail on these points would strengthen the methodological rigor of the study.

Line 101 Please clarify the reference to “Carl Roth” (e.g., supplier name and location).

Line 123 The values reported here appear to represent variability rather than analytical error. Were samples analyzed in replicate? Please report the standard deviation (or other relevant metric) of replicate analyses.

Line 151 The discussion of quality control procedures is difficult to follow. Please clarify how analytical precision, accuracy, and reproducibility were assessed. I have no idea what the authors are talking about here.

Line 290 The statement regarding previous studies and the use of stir bars may need revision. Not all prior studies relied on stir bars, and the use of a shaking table may not constitute a substantial methodological innovation.

Citation: https://doi.org/10.5194/egusphere-2025-6144-RC2
- AC2: 'Reply on RC2', Charly Moras, 31 Mar 2026
  
  Dear Reviewer 2,
  Thank you for your review. We have worked on addressing every single one of your comments in the file attached.
  Kind regards,
  Charly Moras, on behalf of all co-authors
  
  Citation: https://doi.org/10.5194/egusphere-2025-6144-AC2

Peer review completion

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

ED: Reconsider after major revisions (31 Mar 2026) by Tina Treude

AR by Charly Moras on behalf of the Authors (04 May 2026) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (14 May 2026) by Tina Treude

RR by Gunter Flipkens (25 May 2026)

Suggestions for revision or reasons for rejection

Hide

RR by Anonymous Referee #3 (10 Jun 2026)

ED: Reconsider after major revisions (17 Jun 2026) by Tina Treude

AR by Charly Moras on behalf of the Authors (01 Aug 2026) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (05 Aug 2026) by Tina Treude

RR by Anonymous Referee #3 (17 Aug 2026)

RR by Gunter Flipkens (21 Aug 2026)

Suggestions for revision or reasons for rejection

Hide

ED: Publish subject to minor revisions (review by editor) (27 Aug 2026) by Tina Treude

AR by Charly Moras on behalf of the Authors (06 Sep 2026) Author's response Author's tracked changes Manuscript

ED: Publish subject to technical corrections (25 Sep 2026) by Tina Treude

AR by Charly Moras on behalf of the Authors (01 Oct 2026) Author's response Manuscript

Journal article(s) based on this preprint

26 Oct 2026

Impacts of water advection and CO₂ exchange on the carbon dioxide removal potential of ocean alkalinity enhancement

Charly Andre Moras, Matias Saez Moreno, Peggy Bartsch, and Jens Hartmann

Biogeosciences, 23, 7523–7544, https://doi.org/10.5194/bg-23-7523-2026,https://doi.org/10.5194/bg-23-7523-2026, 2026

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Charly A. Moras, Matias Saez Moreno, Peggy Bartsch, and Jens Hartmann

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Ocean alkalinity enhancement has gained popularity to capture carbon dioxide. Yet, most laboratory experiments were run for short term, with strong mixing and without carbon dioxide exchange. In this research, a new setup tried to reproduce a more natural mixing. Overall, alkalinity remained stable for 6 months, thanks to the carbon dioxide invasion which differs from previous research. Hence, potential pitfalls identified in laboratory studies may not be at play in real world application.


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Impacts of water advection and CO2 exchanges on the carbon dioxide removal potential of ocean alkalinity enhancement

Journal article(s) based on this preprint

Interactive discussion

Peer review completion

Suggestions for revision or reasons for rejection

Suggestions for revision or reasons for rejection

Suggestions for revision or reasons for rejection

Suggestions for revision or reasons for rejection

Interactive discussion

Peer review completion

Suggestions for revision or reasons for rejection

Suggestions for revision or reasons for rejection

Suggestions for revision or reasons for rejection

Suggestions for revision or reasons for rejection

Journal article(s) based on this preprint

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Impacts of water advection and CO₂ exchanges on the carbon dioxide removal potential of ocean alkalinity enhancement