Oberlander et al. report on 1) an analysis of prior studies which investigate the influence of elevated pH on phytoplankton growth rates and 2) an experiment aiming to assess the influence of elevated alkalinity on the viability and growth rate of two phytoplankton species. Both aspects of this study are novel and important aspects of research in understanding the ecological impacts of OAE for phytoplankton.

There are three main conclusions made within this study. The first is that there were no significant impacts on the viability or growth rate of the two species assessed within the short term exposure to elevated alkalinity levels. This is to be expected as levels of OAE that would likely result in an impact within 10 minutes of exposure would be significantly higher than what is logistically possible or safe in terms of secondary precipitation. The second is that longer term exposure to elevated alkalinity resulted in a decrease in growth rate. This is an interesting finding as many other studies thus far have found little evidence to suggest that there will be significant impacts to the growth of phytoplankton as a result of OAE. The third is that within the current literature evidence suggests that approximately 50% of species could be significantly impacted by pH increases in line with those expected as a result of OAE. This provides an excellent summary of the current knowledge of pH impacts however it is unclear as to whether these impacts are a result of pH (H⁺ concentrations) or CO₂ concentrations, of which the latter is expected to be the most important factor in regard to the ecological impacts of OAE on phytoplankton. The manuscript does an excellent job in referencing and discussing the influence of elevated pH on phytoplankton growth and viability. However, citations and discussion around OAE specifically are currently lacking. Further I found it difficult to disentangle exactly how the experiments were run within this manuscript and strongly recommend that the methods/results section be revised so that readers may easily understand what the authors have accomplished here.

1) Lines 8 - 9: “One proposed NET is Ocean Alkalinity Enhancement (OAE), which would mimic the ocean’s natural weathering processes, raising alkalinity and pH and sequestering carbon dioxide from the atmosphere.”

There are many methods for achieving OAE and only mineral based methods could be considered to “mimic” the natural weathering of alkali minerals. Furthermore, enhancing alkalinity does not lead to the sequestering of atmospheric CO₂ but decreases oceanic CO₂ concentrations allowing for atmospheric CO₂ to be sequestered under the correct conditions. I appreciate that this is within the abstract and concise wording is necessary but would advise the authors to consider rewording this sentence.

2) line 11-12: “…by experimental assessment of the pH-dependence of viability and growth rates in two near-shore isolates of phytoplankton”

This sentence is difficult to understand, consider rewording.

3) Line 16 – please provide the actual number of days or range of days.

4) Lines 18-19: “…there will be little to no impact on a variety of taxonomic groups of phytoplankton when OAE occurs in naturally flushed systems.”

Within this manuscript the authors have only looked at two species from two different taxonomic groups. This statement is too broad for the results of the experiment conducted here.

5) Line 31: “…ocean’s natural weathering processes while also restoring the oceanic pH and carbonate system to their natural state”

I caution the authors against the use of the word “natural”. All methods of CDR are anthropogenically motivated and furthermore depending on the method of OAE used it may be more or less similar to the natural weathering of alkali minerals (e.g. mineral based OAE vs electrochemical based OAE). Furthermore, it is highly unlikely that OAE would result in these changes as any increase in pH would ideally be negated by an influx of CO₂, resulting in an increase in DIC beyond current and pre-industrial concentrations.

6) Line 33 “The additional carbon would be stored in the form of bicarbonate (HCO-3), which has a residence time of c. 1,000 years in the ocean.”

Ideally this would be the case however additions of alkalinity and subsequent in gassing of atmospheric CO₂ will lead to increases of both carbonate and bicarbonate. This will depend on other variables, but without CO2 equilibration concentrations of carbonate would increase significantly more than bicarbonate.

7) Line 34“Implementation of OAE at large scale would like be through addition of hydroxide (OH-) to surface coastal oceans”.

“…would likely be…” . Also, it is not yet clear which method of OAE will be implemented at large scales. It is more likely that multiple methods will be implemented in different regions e.g. electrochemical in coastal regions and mineral based in pelagic regions.

8) line 36 “The increased alkalinity, would react with CO2 in the surface ocean to form bicarbonate, leading to CO2 invasion from the atmosphere to compensate for the drawdown”

Again, enhancing alkalinity does not necessarily result in bicarbonate formation. For a parcel of water with TA 2100 µmol/kg, DIC 2000 µmol/kg, T 15⁰C and salinity 35 an increase in alkalinity of 500 µmol/kg would result in changes of bicarbonate – 316.93 µmol/kg, carbonate + 340 µmol/kg. Also, such changes in carbonate chemistry do not necessarily lead to CO₂ drawdown this is dependent on several other factors.

9) Lines 84 – 85: “Their protocols controlled nutrient stoichiometry to ensure DIC limitation of growth and most were in batch cultures without ventilation to replenish CO2”

The authors discuss changes in pH throughout this section but was there additional criteria to ensure that manipulations of pH resulted in changes in DIC that would be expected of OAE (particularly for those articles not by “Hansen and colleagues”)? For example, using varied additions of sodium carbonate and HCl one can achieve similar pH values but drastically different concentrations of TA and DIC. Given this and the expected ranges of pH in OAE one would expect CO₂ and not pH to be the driving factor to influence phytoplankton.

10) Figure 1.

The y axis of figure 1a/b are very hard to discern as they overlap and it is unclear which axis label is referring to which set of units on the axis.

11) Figure 1d. It is very difficult to see the median value for the 90% µ reduction. Consider changing the colour of this line and/or adjusting the alpha values in this plot.

12) lines 149 – 148: “For all of the species investigated (Figure 1), the median threshold pH is above 8.5, meaning about 50% of species would not be impacted by the anticipated maximum pH increase associated with OAE”

Is this anticipated maximum pH value for OAE based on changes in pH at the point of alkalinity addition or after dilution within a region?

13) lines 174: “Most prior work investigating the impacts of elevated pH on phytoplankton growth did not permit for DIC resupply, which is necessary for OAE to function as a NET.”

I recommend the authors adjust the wording of this sentence as OAE does not change DIC concentrations initially so there can be no “resupply” of DIC. More accurately this would be an influx of CO₂ increasing DIC beyond what it was prior to OAE.

14) lines 190 -192; “There is clear separation between the aerated and pH-drift cultures following the period of exponential growth (Days 0-1) with respect to both the carbonate system parameters (Figure 3c) and biological parameters describing abundance and physiological status (3d).”

If these observations are made on the basis of the Metric multidimensional scaling plots please state this.

15) Lines 195 – 196: “These results suggest that the responses to OAE cannot necessarily be inferred from pH drift experiments.”

This is a strong statement to be made from a relatively small comparison. Furthermore, there are various approaches to OAE that would not necessarily result in CO₂ influxes similar to those seen here e.g. in areas where CO₂ outgassing occurs, or where OAE is added in an equilibrated form. Could the authors provide some references to support this statement?

16) lines 209 – 213: “The cultures were grown in 40-mL volumes of f/2 (Guillard, 1975) or L1 (Guillard & Hargraves, 1993) seawater medium, and diluted into fresh media in mid-exponential phase in a laminar flow 210 hood. The seawater was collected, and tangential flow filtered at the National Research Council of Canada’s Marine Institute at Ketch Harbour, NS. It was refiltered through a 0.2-μm capsule filter (Cytiva Whatman Polycap Disposable Capsules: 75TC) and nutrient-enriched in autoclaved glassware or in sterile cell culture plates.”

Please make it clear to the reader at the start of this section whether the cultures were grown in filtered seawater with the addition of nutrients and trace metals? Also, it would be beneficial to disclose the exact location of water collection i.e. xxx kms offshore via boat or pump. In addition, it is stated that “…fresh media in mid-exponential phase…” is this for the experimental cultures or the maintenance of culture pre experiment?

17) line 250: “…after dark acclimation for 20 minute.”

The authors previously used a dark acclimation of 30 minutes, is there a reason for the change to 20 minutes?

18) It is not clear how the transient exposure cultures discussed in section 4.3.2 are setup. Are these setup the same as those for the chronic exposure experiment? The authors also mention cultures measured after 1-2 hours, are these the same cultures or separate to the chronic and transient exposure cultures? This confusion may come from the layout in which the methods/results are presented. I am hesitant to suggest changes to this but it would be beneficial to the reader if the authors could be overly obvious in the explanation of how cultures were setup and whether cultures measured after 1-2 hours, several days and/or 10 minutes are the same cultures or separate cultures.

19) lines 294 - 296: “The average value Fv/Fm for D. lutheri was 0.43, indistinguishable from the values in the untreated parent culture, and there was no significant trend (p>0.05) with the transient elevation in pH (Figure 4c). There was a significant trend for T. pseudonana (Figure 4c).”

The authors state “…there was no significant trend with the transient elevation in pH transient elevation in pH (Figure 4c).” However, the figure caption for figure 4 states “…measured after exposure to elevated alkalinity and pH for 1-2 hours…”. Is the transient elevated alkalinity assessing the effect after 10 minutes as stated in line 286 or 1-2 hours?

20) Figures should be introduced in the order they appear in the text e.g. figure 5 is introduced in line 287 while figure 4c is introduced in line 296.

21) lines 310-311: “The mechanism of OAE turns on CO2 invasion to restore the equilibrium concentration of CO2 after conversion of existing CO2 to bicarbonate.”

This sentence needs to be revised in line with comment 8.

22) Lines 311 – 314: “Comparisons of alkalized cultures with high DIC (semi-continuous cultures or aerated batch cultures) and those in which there was a drawdown (sealed pH drift cultures) show that in some cases there is no difference in the resulting growth rates (the dinoflagellates Ceratium furca and C. fusus; Figure 2) but in others it is pronounced (the dinoflagellate C. tripos and the diatom Thalassiosira pseudonana; Figures 2 and 3).”

It would be beneficial if the authors could provide some reasoning behind why there are differences between these methods and how to abate these differences.

23) lines 354 – 356: “We note that at the pH in our experiments, the dominant carbon species would be carbonate and calcite would begin precipitating; the reductions in bicarbonate available for the CCM might account for the reductions in growth rates observed in Figure 4.”

This sentence is confusing particularly “…the dominant carbon species would be carbonate and calcite would begin precipitating…”. Do the authors mean that carbonate is the dominant form of carbon and would precipitate into calcite? Traditionally when discussing precipitation omega values are provided, this would be beneficial here as many other articles discuss calcite precipitation in this form see Moras et al. (2022) and Schulz et al. (2023).

24) lines 256 – 257: “Elevating the pH this high is highly undesirable from the perspective of OAE, as calcite precipitation releases CO2 rather than traps it.”

It would be beneficial to cite some of the many article’s discussing the efficiency of OAE and impacts of calcite precipitation here.

25) There have been numerous studies assessing the impact of OAE on natural assemblages of phytoplankton and cultures in recent years e.g. Gately et al. (2023) and Guo et al. (2023). Although the authors discuss changes in pH there is no significant discussion surrounding the numerous papers on the impact of OAE on phytoplankton. The manuscript is significantly lacking in this regard and inclusion and discussion of such articles within the introduction and/or discussion would help to improve this manuscript.

26) The authors discuss initial pH values, were there also end measurements for pH or prior to media refreshment? Volumes used were relatively low and cultures were grown into stationary phase, as such a significant change in pH over the duration of the experiment would be expected. I understand that during the SDC – MPN assay it would be expected that in gassing occurred maintaining pH at a relatively stable level, however this is not clear for the other experiments.

27) line 241-242: “These additions increased the initial concentration of total alkalinity, 2168 μmol L-1, by 0–1084 μmol L-1.”

Was alkalinity measured or was it calculated? If it was calculated was this based on the additions of NaOH or another measured carbonate chemistry parameter? It would be beneficial to the manuscript to add measured or alkalinity values calculated from a second carbonate chemistry parameter, as many articles discuss OAE in terms of alkalinity increases (µmol/kg) and not pH increases.

28) The quality of Figure S1 is extremely poor and makes it difficult to read. In addition, Figures S1 c,d appear to be concentrations of carbon species (CO₂, HCO^-₃ and CO3^2-) not DIC as stated in the figure caption.

29) It was difficult to distinguish between the experiments, variables measured and methods used here. I strongly recommend the authors increase the clarity of the text discussing the experimental methods. For example, lines 209 – 210 “The cultures were grown in 40-mL volumes of f/2 (Guillard, 1975) or L1 (Guillard & Hargraves, 1993) seawater medium, and diluted into fresh media in mid-exponential phase in a laminar flow hood.” Was this done for all experimental culture’s transient, chronic and those in the SDC-MPN assay? Or was this only prior to the experiment during the acclimation? Am I correct to understand that there are separate cultures with separate maintenance methods i.e. the SDC-MPN cultures, the chronic and transient? A strict section or table outlining the experiments conducted and their common and/or differences in methodology would be greatly beneficial, as it is currently difficult to tease apart exactly how this experiment was conducted.

30) lines 10-12: “The potential impacts of OAE were assessed through an analysis of prior studies investigating the effects of elevated pH on phytoplankton growth rates and by experimental assessment of the pH-dependence of viability and growth rates in two near-shore isolates of phytoplankton.”

The authors introduce the analysis of prior studies here but fail to state any results from this within the abstract. This is a major component of the manuscript and requires a section detailing the results within the abstract.

I read with pleasure the paper: “Assessing the impacts of simulated Ocean Alkalinity Enhancement on viability and growth of near-shore species of phytoplankton” by J. Oberlander and coauthors. This manuscript is of high interest for the assessment of OAE. The author digs into the available data set from the previous study that investigated the impact of increased pH on phytoplankton (outside the context of OAE) and performs culture experiments on two species, Thalassiosira pseudonana and Diacronema lutheri with two different approaches (batch culture and semi-continuous) to trace the (very) short impact of increase pH and the long(er) impact in the context of OAE.

That said, I think the manuscript needs significant revision before it is suitable for publication.

In general: it was hard to follow the structure of the article. Some chapters and subchapters do not follow the standard structure of an article to the point that methodologies, statistics analyses and results are mixed.

The analysis of previous studies is almost at the beginning of the article, but it is not discussed adequately in the discussion and conclusion chapters. Some literature is omitted throughout the article. What about other studies made for ocean acidification that tested however higher pH values e.g. Bach et al., 2015? Or some of the Riebesell et al., studies on coccolithophore?

In the discussions previous articles related to the response of phytoplankton to the perturbation induced by OAE are not mentioned (e.g. Gately et al., 2023) and in general many references are missing throughout the text.

I hope this article will be accepted and published even if some work is still needed.

 So good luck.

More comments in the following lines:

Abstract:

The abstract should be strongly revised. On top of some inaccuracies that I will report in the following lines, the reasons why studying the impact of high pH on phytoplankton is lost within the lines. Moreover, the study is based on two specific species that are important components of the phytoplankton community in specific marine contexts (i.e. near-shore, temperate waters). The final statement (lines 18-19) is therefore too general and misleading. The author should consider the findings of this study and not generalise their results to other taxonomic groups. The analysis of the prior study is lacking in the abstract even if it’s an important part of this study. It should be mentioned.

• Lines 7-8: technologies used twice.
• Line 9: OAE is not only mimicking but is enhancing/accelerating the process. Moreover, it should be made more explicit why CO2 is ultimately sequestered from the atmosphere. The link is missing.
• Lines 10-11 As mentioned before, the aim of the study and the need to understand the impact of increased pH on primary producers should be better expressed.

Introduction

In general: many references are missing throughout the whole introduction. Just a few examples: at line 36 after “drawdown”; at line 37 after “dominates”. There’s a huge literature to cite in the whole introduction that is completely missing.

• Lines 22-27 The first lines are out of topic. It seems more like an introduction to a thesis than an article. I suggest to find another way to introduce the study. This paragraph seems non-correlated to the next one.
• Line 24: Galland et al., 2012: I guess many more references can be added here.

• Line 29: I disagree. NETs are not developed to combat rising atmCO2. See also recent literature on the need to reduce CO2 emission and on the minor role of CDR in this context. Please delete the first part of this sentence or try to put it in a different context.

• Line 31: here and through the text take care about wording. Is OAE going to restore the pH and the carbonate system to their natural state? Why then study the impact of high pH if you consider OAE as a “restoring process”? This is a provocative question. I think this way of summarising the process is incorrect.

• Line 33-38 there are different ways to apply OAE. Not all of them change the pH (i.e. increase the pH). In an equilibrated OAE for example, DIC is increasing while pH is rather stable. Please be cautious with this description and try to rephrase it. In the whole article, CO2 limitation is also barely mentioned.

• Line 41: I would rephrase this part since at the moment we don’t know how the regulations might change. There are ongoing projects that are trying to evaluate efficiency, efficacy and env. impact in the open ocean (ship). I would mind the words again and avoid saying: “almost certainly” I would suggest the authors refer to your possible case scenarios instead (i.e. land-based, coastal release of TA).

• Line 46: I would delete “especially” since the impact at different trophic levels is equally important
• Lines 49-64: some sentences are disconnected. Line 53-54: what does that mean? Why in this context do you think is important? References are missing and a big range of pH is put in the loop. This sentence it’s a bit of a: “and then what?” sentence.
• Lines 56-64: almost no references. They should be added.
• Line 66: it is not only Hansen, 2002. There’s a lot of literature on the response of phytoplankton to changes in pH in the optic of OA studies. Some of them tested also higher pH values!
• Line 71: the aim of the study should be better clarified and underlined and not with an “en passant” sentence like this one.

2 A review of the pH-dependence of growth rates

2.1 Literature Review & Data Digitization

• Line 83 Since the literature review is not only based on Hansen 2022, this way of citing the studies is not correct. Please refer to the table in the supplementary. On top of that: why other studies that tested high pH on diatoms and or coccolithophores were excluded? The choice of the considered study is not clear to me.

3 Examining the impact of prolonged, elevated pH on phytoplankton with and without DIC resupply

• Line 174: The description of OAE is incorrect. First, there are different ways to apply OAE (equilibrated and non-equilibrated). DIC in a non-equilibrated approach is rather stable at the very beginning.
• Line 192-194 This is more a method than a description of the results
• It’s not clear what this paragraph is about.
• I don’t know if this is the right paragraph but the way pH and the other carbonate chemistry parameters are not clear to me. What did you measure? DIC or TA on top of pH? And how?
• Lines 195-196: I strongly disagree with this statement. I would tone it down to the specific case that you are considering.

4 Assessing the effects of short- and long-term alkalization on viability, growth, and photosynthetic competence in two coastal phytoplankton

• I found the whole of chapter 4 quite hard to follow. Methods and results are mixed in a way that makes the reading quite challenging. I strongly encouraged the authors to rethink the structure of the whole chapter 4 to make it easier to follow by the reader.

Discussion

• Line 305-306: the first sentence of the Discussion is out of topic as mentioned by the way by the authors. Why mention it as the first sentence MRV if it is unrelated to the aim of the study?
• The very first sentence mentions the increase in pH. However, OAE could be applied in different ways (not only with the addition of NaOH) that could impact less the ecosystem. I mean the equilibrated approach that would not induce an increase in pH but in DIC. On top of that, even if the aim of the study is the impact of high pH on phytoplankton, what about CO2 limitation?
• Line 308: a variation from 8.2-8.3 is it by the way in the natural range of variation in a marine context, meaning that phytoplankton is by definition able to cope with this (and even bigger) pH variations. Should we then be surprised that this shift is not making any impact on the studied species?
• Line 315: with cautions in which sense and why?
• In general, if OAE is applied in a non-equilibrated way as in the case of NaOH solutions, the authors should consider that equilibration will take time. Therefore, the perturbation of the carbonate chemistry could last relatively longer in the water
• Line 310- 315: I strongly disagree. Equilibration could take time to happen. It is not such a fast process at least not in every oceanic/marine context. Ingassing could take longer, therefore, the pH-drift effect must be considered. I value the long/semi-continuous studies that should give us information on the long(er) response of the phytoplankton. But I disagree with the limited value of short(er) batch experiments that within some minutes/hours/days can give us a hint of how a species responds to the carbonate chemistry perturbation induced by increased TA
• Line 318: references missing after others
• Line 321: what is likely to be a high mean?
• Line 322: compared to what? (i.e. which group?)
• Line 336: this is the authors’ idea since there are studies there that are now trying to apply OAE simulating the release from a ship in the open waters. I would suggest that the authors will use the opportunity to relate their study to the specific case of coastal water and/or basin OAE.
• Line 355 London protocol see comment above
• Line 342-345: how accurate are these pH numbers? How were they calculated?
• In the discussion, most of the studies on the impact of OAE on phytoplankton are not mentioned. The article is lacking in putting its results into a broader context considering studies like Gately et al, 2023.