the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 08 Jul 2024
Response of Marine Primary Producers to Olivine Additions
Abstract. Carbon dioxide removal (CDR) technologies are gaining increasing attention as a potential solution to reduce atmospheric CO2 concentrations and combat climate change. Ocean alkalinity enhancement (OAE) seeks to enhance the ocean's CO2 absorption capacity by introducing powdered minerals or dissolved alkaline substances into the surface ocean. Nevertheless, the impact of OAE on marine ecosystems remains largely uncharted. In this study, we explored the impact of olivine on a diversity of cosmopolitan primary producers, including Coccolithophores, Diatoms, Dinophyceae, Micromonas sp., Prochlorococcus sp., and Synechococcus sp. Here, we show that most primary producers were not impacted negatively by the concentrations of olivine additions that were applied despite olivine additions increasing nickel concentrations in our cultures. Additions of olivine did not lead to growth inhibition but resulted in a slight increase in growth in most cultures, with picoplankton benefiting the most. However, phytoplankton responses were species-specific and subject to the media used in a combination with the olivine addition. Additionally, it is essential to mention the pitfalls and concerns associated with our experimental setup, particularly regarding the impact of the medias and considerations of carbonate chemistry. Our findings raise confidence in applying olivine for carbonation to generate CO2 removal without harming primary producers; however, future studies should include tests on an ecosystem level to investigate potential effects on different trophic levels and natural settings.
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Status: closed (peer review stopped)
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RC1: 'Comment on egusphere-2023-2884', Anonymous Referee #1, 01 Aug 2024
Review of Ronning et al., 2024:
Ronning et al. investigate the effect of olivine on various phytoplankton species. They investigate many phytoplankton species, a plus of the study. Unfortunately, however, there appear to be substantial methodological problems so that their data is implausible. It is unclear (unlikely?) that the authors can resolve these substantial issues, so that this dataset may not be publishable.
Critical issues:
- The main concern is the carbonate chemistry data. There were many unclarities with the methods (see other comments below) and based on that it appears likely that there were severe issues with the applied methodology so that the data may not be used. Just looking at the At data: The extremely large day-to-day variations of up to 400 micromol/kg cannot be explained in any meaningful way. At may in extreme cases gradually change by about perhaps 50 micromol/kg over the course of a bloom due to nitrate uptake. Or in the case of coccolithophores due to calcification. Likewise, the extremely high variance between replicates, which also varies on a day-to-day basis, cannot be explained in a meaningful way. Another issue is that there is no consistent effect of olivine on At. Sometimes At is higher in the treatment and sometimes in the control. It is unclear how this is possible, considering that At is usually not affected by biology by the extent as observed here. Taken together, there are many red flags in the At dataset, so that it is very questionable whether the data is robust. (On another note, the discussion reveals that the authors added HEPES to some of the cultures, which has not been described in the methods. HEPES is an organic buffer, which strongly interferes with the measurement but this is not described suggesting the authors were unaware of this. It was also noted that sodium bicarbonate was added, also not mentioned in the methods, which strongly affects carbonate chemistry.)
- The pH measurements also appear questionable. They were measured from At samples before titrations. Unlike At, pH is very sensitive to biological activity. It hasn’t been described whether the samples were poisoned to stop biology. The pH in the sample, may have little to do with the pH in the incubations after storage time. Furthermore, pH was measured on the NBS scale, and it is unclear whether temperature was controlled during measurements. All this is far from state of the art.
- Lastly, the DIC measurements at best roughly, sometimes not at all provide consistency with other datasets. For example, in T. weisflogii DIC goes slightly down during the early bloom but then 1000 micromol/kg up until the end, despite 3000 microg/L chla production. In Synechococcus, DIC goes down by ~800 micromol/kg, while ≪only≫ 800 microg/L of chlorophyll is formed. It is very unclear how all of this fits together.
- Just looking at the chlorophyll dataset provides another red flag. There are sometimes extremely high values, so that accumulation of phytoplankton biomass would be high enough to significantly alter growth conditions. Also, there are sometimes changes in chlorophyll on a day-to-day basis that are entirely implausible. For example, Micromonas increases chlorophyll from roughly 200 to 5000 microg/L within a day, just to lose the same amount on the next day. These are implausible changes, implying that the dataset is not robust and may not be able to be published.
- The design of the primary production assay is not ideal as it is unclear what is compared. The duration of the experiments differ and so does the build-up of biomass. The species may be in different bloom phases at the time they are sampled, not only across species but also between control and treatment. The authors would need to clarify how they can compare the snapshots of investigation.
In summary, there are numerous red flags in unfortunately all of the central datasets of the study, which may make it hard to publish the dataset.
Other comments:
Line 115: more details on the olivine source would be needed.
Line 113-140: reads like results/discussions.
Line 169: better to report micromole/m2/s.
Line 172: headspace in exchange with atmosphere implies that the bottles were open.
Line 186: unclear how many replicates were used for the control.
Line 197: time of storage would need to be provided since chlorophyll samples can rapidly decay.
Line 198: calibration method would need to be provided.
Line 209: Unclear what is meant by samples. Are these sub-samples from the incubation volume, and if so, unclear how much volume was incubated.
Line 225: unclear what is meant by residues of CO2.
Line 227: The use of syringes creates pressure gradients which can affect pH and DIC. It is currently unclear how the effect of this was mitigated.
Line 229: unclear what pH scale was used.
Line 229: pH measurements have different requirements than At measurements because pH is critically susceptible to CO2 exchange with the atmosphere while At measurements are not. Currently unclear how this was mitigated.
Line 229: Unclear if temperature was measured during titrations as some electrodes cannot measure T.
Line 234: unclear if NaCl was added to sample or acid.
Line 245: Unclear how trace metals were sampled and if sampling was conducted under trace metal clean conditions.
Citation: https://doi.org/10.5194/egusphere-2023-2884-RC1 -
RC2: 'Comment on egusphere-2023-2884', Anonymous Referee #2, 15 Aug 2024
The manuscript “Response of Marine Primary Producers to Olivine Additions” by Rønning et al., explores the response of various phytoplankton groups to increased alkalinity resulting from olivine addition. The researchers examined 10 different species, including multiple strains of certain species. The species selected for this work are widely distributed across different geographical regions, which is a strength of the study. Through culture experiments, the authors report on the response to growth rates using Chl a biomass as a proxy and estimate carbon fixation rates from 13C stable isotope assays. The choice of species provides a globally relevant, and ecologically meaningful framework for understanding how ocean alkalinity enhancement might impact phytoplankton communities. This research is particularly significant, given the pressing need to evaluate the environmental implications of Ocean Alkalinity Enhancement.
However, the paper at this stage is not suitable for publication. The entire study from execution to data generation and reporting falls short in many key aspects (listed below) but especially methodologically to justify the conclusions made.
If the authors can address the underlying issues, I will be happy to review this paper again. However, some of the points I will raise, concern substantial weaknesses in the methodology of the experiments. Given that the major concerns surround the test variables on which effects are interpreted, I have doubts that these can be sufficiently solved to justify the publication of this work.
- Main points:
- Carbonate chemistry: one of my main concerns regarding this study is the unclear TA (or more generally the carbonate chemistry) dataset. In some cases, there are significant, unnatural day-to-day fluctuations in the dependent variables (TA, pH and DIC). This makes it almost impossible to quantitatively extract any meaningful conclusions from the experiment on the effect of OAE. For some species, there is a loss of alkalinity ranging from 400 to 1200 mmol/kg across the experiments which is puzzling and unclear. The reason/s for these large fluctuations and how they may affect the interpretations of the results are not addressed by the authors anywhere in the manuscript.
- The 10 different species/strains have very different TA (and pH and DIC) values already in the control treatments. The authors mentioned that they used different media for the different species to explain some of these differences (by the way this was mentioned only in the discussion and it is a big weak point that should be mentioned already in the mat&met part). However, even within the same groups (i.e., the three Synecochococcus strains) the starting points of the three controls differed sometimes by 100/150 mmol/kg. How is this possible? These irregularities have not been addressed in the manuscripts, but already indicate that the difference in starting conditions was sufficient evidence to either terminate or restart the experiments.
- The error bars are also huge indicating big uncertainties within the measurements and that the authors were not able to constrain the test variables to give a clear difference between the control and the olivine treatments. On top of that, the results display error bars overlapping indicating that there is no statistically significant difference between the control and olivine-based treatment. A true effect of the olivine treatment can therefore not be extracted. Therefore, any effect or lack thereof mentioned in the manuscript cannot be justified by either the experimental design or the results.
- Due to these big uncertainties, the authors should have established in a separate experimental unit, the potential of alkalinity generation from olivine under their experimental conditions without the biology. This would be helpful to tease out whether the significant changes in TA they observed over time are related to biological activity or not. In culture experiments, organic matter buildup is a significant component of the setup with potential impacts on the pH of the culture conditions. Was the TA increase on day one of the experiment significant? This is not clear from their experimental results.
- The descriptions of the development of TA, DIC, and pH are mostly inaccurate. Trends are described that do not appear to be real given the size of the error bars.
- Any type of statistical analysis is completely missing throughout the entire article. This is evident across all datasets, but it is even more evident in the carbon fixation rate data, where a simple ANOVA could have been performed.
- The authors used sodium bicarbonate to estimate carbon fixation. Sodium bicarbonate increases alkalinity and dissolved inorganic carbon (DIC) in the water, similar to the effects of olivine dissolution. Therefore, in their experiments where both DIC and TA are elevated due to olivine addition, the addition of sodium bicarbonate in the control to estimate carbon fixation is a deliberate introduction of bicarbonate ions that affect the carbonate chemistry. In such cases other methods to estimate primary production should have been used. The differences in TA due to olivine addition in these experiments seem quite subtle and the sodium bicarbonate could likely be obscuring the carbonate chemistry changes from olivine in the treatments and changing the control as well. The authors should therefore quantify the changes in DIC relative to the background from adding sodium bicarbonate to determine if the control can be useful to make comparisons of carbon fixation with the olivine treatments and if the results are not confounded.
- I find no justification for the different durations of the experiments. Why is there such a significant difference? This discrepancy is also observed among different strains of the same species, so how is it possible to compare datasets that are so different from each other?
- For example: why did the experiment for Synechococcus A15-62 last 25 days while for the strain EUM- Syn 10 days only 10 and for WH8102 9 days? Why did you choose these lengths in these arbitrary ways? This is a very relevant aspect when you compare the primary production and therefore the biomass build-up.
- What about Scrippsiella? Why do you have these random data points and you don’t provide measurements from day 10 (I guess) until days 40 and 44?
- Figures:
- The X-axes of the figures are chaotic and not clear why the different measurements were not taken consistently over the same time interval during the experimental duration. The reasoning for this erratic frequency is unclear. The different intervals in the way the data are presented are very confusing and make it hard to match the response patterns with the test variables. Nevertheless, this inconsistency demonstrates some degree of carelessness in experimenting. The intervals on the x-axis in the TA, pH, DIC and Chl a plot should be consistent.
- The same for the y axes that represent different intervals for all parameters (TA, DIC, pH) and this makes it impossible to compare the results of the different species tested.
- I am guessing the runtime of experiments in Table 3 is also referring to the incubation time for the carbon fixation assays. It is not clear since the authors do not provide an equation on how carbon fixation rates were calculated. I assume therefore that the authors divided the rates by the number of experimental days to get to the daily rates. There are basic major flows to measuring carbon fixation rates over such long durations. In such long incubations, the culture conditions change significantly leading to shifts in the physiological conditions of the phytoplankton which alters their carbon uptake rates. Phytoplankton do not have a stable activity rate. This is not captured in the carbon fixation rates. The experiments also vary in length so we cannot compare the daily rates across phytoplankton groups and even within the same group. Additionally, the rates do not take into consideration the fluctuations in the POC or DIC pool over the experimental period which are relevant parameters in the calculations of carbon fixation rates. Not properly accounting for these issues is highly problematic to the interpretation of the carbon fixation. For most standard measurements of carbon fixation in phytoplankton cultures using sodium bicarbonate incubations, a duration of 1 to 4 hours is often ideal, as it provides a good balance between capturing sufficient carbon fixation and avoiding significant changes in the culture environment. These significant methodological aspects render the carbon fixation rates faulty and unusable for any interpretations.
- I suggest a careful reading of the manuscript before the next submission, as I found many typos such as unclear line breaks, missing periods, poor sentence structure, wrong use of tenses and repeated references in the same sentence.
- Minor specific comments:
The manuscript is long and tiresome to read, there are many redundant paragraphs, especially describing the methods that could be summarized to extract the important aspects for the reader. Some sections of the manuscript seemed to originate from a thesis and did not flow well within the text. An example concerns the discussions. Chapter 4.4, 'Where could ocean alkalinity enhancement be applied?' seems to be part of a thesis summary that suggests 'what's next,' but it is not supported by clear data and remains superficial.
Abstract:
Line 17: “Additions of olivine did not…… slight increase in growth” is ambiguous, was this slight increase statistically significant or practically relevant? The authors should clarify;
Line 17: “with Picoplankton benefitting”…..Picoplankton has not been defined which groups are being referred to here. Some specificity is required
Line 19: “the media used”: this aspect cannot be introduced in this way if it is so relevant to be able or not able to interpret the results.
Introduction: the introduction is not well structured. Several repetitions are present in the text.
Line 35: Rephrasing is needed. One aspect is that OAE is accelerating a natural process; another aspect is that OAE is a CDR. The link to EW afterwards is a bit confusing.
Line 44: is missing
Lines 41 – 46: “The permanence of CO2 removal”: what is the connection of this paragraph to the study?
Lines 49 – 53: “These changes cause….A change in the primary producer community”. The transition from OA to OAE is ambiguous in these two sentences. There is a connection that is needed to shift from the effects of OA to the effects of OAEs
Lines 53-57: This part can be shortened. It reads like an intro of a thesis and after some years of research on OAE, such a long introduction is not needed. I strongly suggest the authors talk mainly about the topic they are interested in. Therefore, mention the impact of olivine due to the increase in other TMs (like Si) and do not mention the white hypothesis. For example, in line 87 you mentioned again the impact of increased TMs from olivine on diatoms.
Line 77: Please add i.e. or e.g. since there are hundreds of studies on this topic
Lines 91-92: “It is a diverse group”: What is the relevance of this sentence?
Lines 101-103: Sounds like a repetition of what is written in the previous lines when the authors introduced the groups that they decided to test. So far, it’s not clear which species were tested.
Experimental methods:
Line 115: Norway: do you have more information? From which company or institute?
Lines 125-126: “(BET analysis) of 1.81”. Is correct this way? or please rephrase
Lines 134: This sentence and the sentence from line 137 about As and Cr should go in the discussion.
Lines 133 – 134: Olivine’ trace metal….. use of concentration is redundant. The phrase “was detected in olivine” is redundant since it is already established that the trace metal content is part of olivine at the beginning of the sentence. There are multiple sentences of this nature throughout the text that could be streamlined for clarity and ease of reading.
Line 143: The whole section on strains and cultivation conditions should be revised. Some information on how the algae were treated is unclear or missing. For example, it took me some time to understand (and I’m not entirely sure yet) that the olivine was poured directly inside the culture bottles. Am I right?
Table 3: Bigelow?
Line 144: Chlorophyta is used here for the first time, there should be consistency in whether the authors use the species name or the taxon for what they are referring to.
Line 145: It is not clear what the authors mean by abrupt exposure, the issue of time with regards to the OAE application was not mentioned until now.
Line 146: Which following strains are the authors referring to?
Line 153: There is no mention of dolomite addition anywhere else in the methods. The authors should clarify the relevance of this information
Line 156: It is not clear what the authors mean by “…involving division of the additions of components by two”
Lines 172-173: I don’t get this part. Do you mean that before the experiment you added 100 ml of the stock cultures to 400 ml of a new medium? In case yes, please change the text to make it more understandable
Lines 175- 180: 1. Can you explain why different approaches were used towards the different strains? 2. The strain codes make it quite difficult to follow the text. I get it was easier for the authors to use codes instead of full names but you should find some other ways to name the species/strains so that the readers can understand immediately if they are referring to a diatom or a coccolithophore or anything else.
Lines 177: “… conditions similar to those mentioned”. Which conditions are you referring to?
Lines 181-182: You asses: 1. Carbonate chemistry perturbation; 2. TMs release by Olivine addition. Why do you mention only carbonate chemistry here? It is confusing.
Lines 182: Which days were the preliminary phase? Until now it was not stated that there were phases to be considered.
Lines 183: “This amount”…. While this may be the case in the previous experiments in Rønning et al, it is not the case from the results of this manuscript that TA and pH were maintained throughout the experimental period. The authors should address the irreproducibility of their results and their implications.
Lines 188: This sentence is convoluted due to the way the order in which information is given. Revise for clarity.
Lines 195-197: The duration of storage for Chl a samples before analysis should be given.
Lines 209: The authors should also report the 13C isotopic enrichment of the carbon source in atom %.
Lines 220: Carbonate system is repeated in one sentence. The sentence could be improved for clarity
Lines 240 - 253: This description of trace metal methodology is incomplete. Were the experiments conducted following GEOTRACES protocol for trace metal clean conditions? The sampling procedure including sampled volume for trace metal analysis has not been given.
Lines 254 - 264: Nutrient methodology is provided but the results have not been shown. Additionally, the detection limits for the nutrient analysis should be reported.
Results
The entire results section could use some shortening and streamlining.
It is very descriptive but missing a red thread concerning what is important to pay attention to. The authors often lose the reader with so many details, convoluted sentences and redundancy in their way of writing. Some descriptions are not accurate.
Total Alkalinity:
Are the trends described in the text real? Due to the big error bars, most of the changes look not significant within the same (each treatment) and when comparing the control and the olivine treatments. The error bars are very expanded so I guess there was a big variability within the replicates.
Figure 1 & Figure 2: The TA data on the x-axis is inconsistent between the olivine treatment and the control. In some cases, the starting conditions are the same and, not. It is also not understandable why the control in the Prochlorococcus NATL plot is higher than the olivine treatment. The authors should maybe use delta TA to make this plot much clearer.
It’s hard to follow the increase in TA (but also pH and DIC) since the y-axes have different scales. Please make new graphs with the same scales for all strains/species.
Lines 268: What ability are the authors referring to?
Lines 296: as mentioned before: 1. Why are fewer days measured for this species? It should be mentioned. 2. A better description of the trends is mandatory here since there are also some hidden and not clear patterns.
pH changes:
For the pH fluctuations similarly to the TA, the description of the results should be revised carefully. Some trends are indeed not described and the focus is sometimes on the clearer pattern.
Line 316: incubation: More precise here. Which one?
Line 324: huxleyi
Line 355: Micromonas: it’s not true. Negative impact?
Line 363: But I think it is significantly different only on day 20.
Line 373: E. huxleyi: But also the control took a long time before Chl a started to increase. On top of that the error bars are also very long so I’m not convinced that the differences are significant even within the control
Line 382: between? I guess one number is missing
Line 383. 1. Delete for and it. 2. As mentioned before make it explicit which species are you referring to. So please in this case add Prochlorococcus before the strain code.
Line 386: Please make it explicit that you are referring to the olivine treatment
Carbon fixation
Line 401-403: values are very different for the three Synechococcus species. The three strains should be described separately.
Why no statistical analysis was performed? You have replicates for every treatment. A very simple ANOVA could have been performed to assess significant differences. Looking at standard errors I doubt that in WH8102 the control and the olivine treatments are significantly different
Line 433: something missing in this sentence
Lines 436- 438: but you should consider the error bar! The first measurement has a huge error bar
Figure 6: Since only two-time points were taken for the nickel concentrations, box plots may be a better representation of the data than a line plots. Error bars are huge! Figure 6d for example: from 750 to 1500? similarly for Fig. 6a at day 25: from less than 550 to almost 2000?
Discussion:
Lines 485-486: not so true. Remember the study by Guo
Lines 499- 502: There is no statistical analysis that supports any of this conclusion
Lines 504-505: in your experiment? In case yes, not true and not always and with huge differences among the different 10 treatments
Lines 516-517: highly speculative...what does it mean? what is the connection? This is the species where the longest experiment was performed. The experiment lasted 44 days and you have fewer data points (for some unclear reasons). The decline of Ni could have been done to some kind of precipitation or any other process.
Lines 518-520: It's not clear that you refer to Xin et al., 2023
Line 529: in contrast?
Chapter 4.3: More an introduction chapter of the discussion...not adding anything relevant to the discussion.
Line 582: “And most likely also” ????
Line 596: are these refs related to the previous sentence?
Citation: https://doi.org/10.5194/egusphere-2023-2884-RC2
Status: closed (peer review stopped)
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RC1: 'Comment on egusphere-2023-2884', Anonymous Referee #1, 01 Aug 2024
Review of Ronning et al., 2024:
Ronning et al. investigate the effect of olivine on various phytoplankton species. They investigate many phytoplankton species, a plus of the study. Unfortunately, however, there appear to be substantial methodological problems so that their data is implausible. It is unclear (unlikely?) that the authors can resolve these substantial issues, so that this dataset may not be publishable.
Critical issues:
- The main concern is the carbonate chemistry data. There were many unclarities with the methods (see other comments below) and based on that it appears likely that there were severe issues with the applied methodology so that the data may not be used. Just looking at the At data: The extremely large day-to-day variations of up to 400 micromol/kg cannot be explained in any meaningful way. At may in extreme cases gradually change by about perhaps 50 micromol/kg over the course of a bloom due to nitrate uptake. Or in the case of coccolithophores due to calcification. Likewise, the extremely high variance between replicates, which also varies on a day-to-day basis, cannot be explained in a meaningful way. Another issue is that there is no consistent effect of olivine on At. Sometimes At is higher in the treatment and sometimes in the control. It is unclear how this is possible, considering that At is usually not affected by biology by the extent as observed here. Taken together, there are many red flags in the At dataset, so that it is very questionable whether the data is robust. (On another note, the discussion reveals that the authors added HEPES to some of the cultures, which has not been described in the methods. HEPES is an organic buffer, which strongly interferes with the measurement but this is not described suggesting the authors were unaware of this. It was also noted that sodium bicarbonate was added, also not mentioned in the methods, which strongly affects carbonate chemistry.)
- The pH measurements also appear questionable. They were measured from At samples before titrations. Unlike At, pH is very sensitive to biological activity. It hasn’t been described whether the samples were poisoned to stop biology. The pH in the sample, may have little to do with the pH in the incubations after storage time. Furthermore, pH was measured on the NBS scale, and it is unclear whether temperature was controlled during measurements. All this is far from state of the art.
- Lastly, the DIC measurements at best roughly, sometimes not at all provide consistency with other datasets. For example, in T. weisflogii DIC goes slightly down during the early bloom but then 1000 micromol/kg up until the end, despite 3000 microg/L chla production. In Synechococcus, DIC goes down by ~800 micromol/kg, while ≪only≫ 800 microg/L of chlorophyll is formed. It is very unclear how all of this fits together.
- Just looking at the chlorophyll dataset provides another red flag. There are sometimes extremely high values, so that accumulation of phytoplankton biomass would be high enough to significantly alter growth conditions. Also, there are sometimes changes in chlorophyll on a day-to-day basis that are entirely implausible. For example, Micromonas increases chlorophyll from roughly 200 to 5000 microg/L within a day, just to lose the same amount on the next day. These are implausible changes, implying that the dataset is not robust and may not be able to be published.
- The design of the primary production assay is not ideal as it is unclear what is compared. The duration of the experiments differ and so does the build-up of biomass. The species may be in different bloom phases at the time they are sampled, not only across species but also between control and treatment. The authors would need to clarify how they can compare the snapshots of investigation.
In summary, there are numerous red flags in unfortunately all of the central datasets of the study, which may make it hard to publish the dataset.
Other comments:
Line 115: more details on the olivine source would be needed.
Line 113-140: reads like results/discussions.
Line 169: better to report micromole/m2/s.
Line 172: headspace in exchange with atmosphere implies that the bottles were open.
Line 186: unclear how many replicates were used for the control.
Line 197: time of storage would need to be provided since chlorophyll samples can rapidly decay.
Line 198: calibration method would need to be provided.
Line 209: Unclear what is meant by samples. Are these sub-samples from the incubation volume, and if so, unclear how much volume was incubated.
Line 225: unclear what is meant by residues of CO2.
Line 227: The use of syringes creates pressure gradients which can affect pH and DIC. It is currently unclear how the effect of this was mitigated.
Line 229: unclear what pH scale was used.
Line 229: pH measurements have different requirements than At measurements because pH is critically susceptible to CO2 exchange with the atmosphere while At measurements are not. Currently unclear how this was mitigated.
Line 229: Unclear if temperature was measured during titrations as some electrodes cannot measure T.
Line 234: unclear if NaCl was added to sample or acid.
Line 245: Unclear how trace metals were sampled and if sampling was conducted under trace metal clean conditions.
Citation: https://doi.org/10.5194/egusphere-2023-2884-RC1 -
RC2: 'Comment on egusphere-2023-2884', Anonymous Referee #2, 15 Aug 2024
The manuscript “Response of Marine Primary Producers to Olivine Additions” by Rønning et al., explores the response of various phytoplankton groups to increased alkalinity resulting from olivine addition. The researchers examined 10 different species, including multiple strains of certain species. The species selected for this work are widely distributed across different geographical regions, which is a strength of the study. Through culture experiments, the authors report on the response to growth rates using Chl a biomass as a proxy and estimate carbon fixation rates from 13C stable isotope assays. The choice of species provides a globally relevant, and ecologically meaningful framework for understanding how ocean alkalinity enhancement might impact phytoplankton communities. This research is particularly significant, given the pressing need to evaluate the environmental implications of Ocean Alkalinity Enhancement.
However, the paper at this stage is not suitable for publication. The entire study from execution to data generation and reporting falls short in many key aspects (listed below) but especially methodologically to justify the conclusions made.
If the authors can address the underlying issues, I will be happy to review this paper again. However, some of the points I will raise, concern substantial weaknesses in the methodology of the experiments. Given that the major concerns surround the test variables on which effects are interpreted, I have doubts that these can be sufficiently solved to justify the publication of this work.
- Main points:
- Carbonate chemistry: one of my main concerns regarding this study is the unclear TA (or more generally the carbonate chemistry) dataset. In some cases, there are significant, unnatural day-to-day fluctuations in the dependent variables (TA, pH and DIC). This makes it almost impossible to quantitatively extract any meaningful conclusions from the experiment on the effect of OAE. For some species, there is a loss of alkalinity ranging from 400 to 1200 mmol/kg across the experiments which is puzzling and unclear. The reason/s for these large fluctuations and how they may affect the interpretations of the results are not addressed by the authors anywhere in the manuscript.
- The 10 different species/strains have very different TA (and pH and DIC) values already in the control treatments. The authors mentioned that they used different media for the different species to explain some of these differences (by the way this was mentioned only in the discussion and it is a big weak point that should be mentioned already in the mat&met part). However, even within the same groups (i.e., the three Synecochococcus strains) the starting points of the three controls differed sometimes by 100/150 mmol/kg. How is this possible? These irregularities have not been addressed in the manuscripts, but already indicate that the difference in starting conditions was sufficient evidence to either terminate or restart the experiments.
- The error bars are also huge indicating big uncertainties within the measurements and that the authors were not able to constrain the test variables to give a clear difference between the control and the olivine treatments. On top of that, the results display error bars overlapping indicating that there is no statistically significant difference between the control and olivine-based treatment. A true effect of the olivine treatment can therefore not be extracted. Therefore, any effect or lack thereof mentioned in the manuscript cannot be justified by either the experimental design or the results.
- Due to these big uncertainties, the authors should have established in a separate experimental unit, the potential of alkalinity generation from olivine under their experimental conditions without the biology. This would be helpful to tease out whether the significant changes in TA they observed over time are related to biological activity or not. In culture experiments, organic matter buildup is a significant component of the setup with potential impacts on the pH of the culture conditions. Was the TA increase on day one of the experiment significant? This is not clear from their experimental results.
- The descriptions of the development of TA, DIC, and pH are mostly inaccurate. Trends are described that do not appear to be real given the size of the error bars.
- Any type of statistical analysis is completely missing throughout the entire article. This is evident across all datasets, but it is even more evident in the carbon fixation rate data, where a simple ANOVA could have been performed.
- The authors used sodium bicarbonate to estimate carbon fixation. Sodium bicarbonate increases alkalinity and dissolved inorganic carbon (DIC) in the water, similar to the effects of olivine dissolution. Therefore, in their experiments where both DIC and TA are elevated due to olivine addition, the addition of sodium bicarbonate in the control to estimate carbon fixation is a deliberate introduction of bicarbonate ions that affect the carbonate chemistry. In such cases other methods to estimate primary production should have been used. The differences in TA due to olivine addition in these experiments seem quite subtle and the sodium bicarbonate could likely be obscuring the carbonate chemistry changes from olivine in the treatments and changing the control as well. The authors should therefore quantify the changes in DIC relative to the background from adding sodium bicarbonate to determine if the control can be useful to make comparisons of carbon fixation with the olivine treatments and if the results are not confounded.
- I find no justification for the different durations of the experiments. Why is there such a significant difference? This discrepancy is also observed among different strains of the same species, so how is it possible to compare datasets that are so different from each other?
- For example: why did the experiment for Synechococcus A15-62 last 25 days while for the strain EUM- Syn 10 days only 10 and for WH8102 9 days? Why did you choose these lengths in these arbitrary ways? This is a very relevant aspect when you compare the primary production and therefore the biomass build-up.
- What about Scrippsiella? Why do you have these random data points and you don’t provide measurements from day 10 (I guess) until days 40 and 44?
- Figures:
- The X-axes of the figures are chaotic and not clear why the different measurements were not taken consistently over the same time interval during the experimental duration. The reasoning for this erratic frequency is unclear. The different intervals in the way the data are presented are very confusing and make it hard to match the response patterns with the test variables. Nevertheless, this inconsistency demonstrates some degree of carelessness in experimenting. The intervals on the x-axis in the TA, pH, DIC and Chl a plot should be consistent.
- The same for the y axes that represent different intervals for all parameters (TA, DIC, pH) and this makes it impossible to compare the results of the different species tested.
- I am guessing the runtime of experiments in Table 3 is also referring to the incubation time for the carbon fixation assays. It is not clear since the authors do not provide an equation on how carbon fixation rates were calculated. I assume therefore that the authors divided the rates by the number of experimental days to get to the daily rates. There are basic major flows to measuring carbon fixation rates over such long durations. In such long incubations, the culture conditions change significantly leading to shifts in the physiological conditions of the phytoplankton which alters their carbon uptake rates. Phytoplankton do not have a stable activity rate. This is not captured in the carbon fixation rates. The experiments also vary in length so we cannot compare the daily rates across phytoplankton groups and even within the same group. Additionally, the rates do not take into consideration the fluctuations in the POC or DIC pool over the experimental period which are relevant parameters in the calculations of carbon fixation rates. Not properly accounting for these issues is highly problematic to the interpretation of the carbon fixation. For most standard measurements of carbon fixation in phytoplankton cultures using sodium bicarbonate incubations, a duration of 1 to 4 hours is often ideal, as it provides a good balance between capturing sufficient carbon fixation and avoiding significant changes in the culture environment. These significant methodological aspects render the carbon fixation rates faulty and unusable for any interpretations.
- I suggest a careful reading of the manuscript before the next submission, as I found many typos such as unclear line breaks, missing periods, poor sentence structure, wrong use of tenses and repeated references in the same sentence.
- Minor specific comments:
The manuscript is long and tiresome to read, there are many redundant paragraphs, especially describing the methods that could be summarized to extract the important aspects for the reader. Some sections of the manuscript seemed to originate from a thesis and did not flow well within the text. An example concerns the discussions. Chapter 4.4, 'Where could ocean alkalinity enhancement be applied?' seems to be part of a thesis summary that suggests 'what's next,' but it is not supported by clear data and remains superficial.
Abstract:
Line 17: “Additions of olivine did not…… slight increase in growth” is ambiguous, was this slight increase statistically significant or practically relevant? The authors should clarify;
Line 17: “with Picoplankton benefitting”…..Picoplankton has not been defined which groups are being referred to here. Some specificity is required
Line 19: “the media used”: this aspect cannot be introduced in this way if it is so relevant to be able or not able to interpret the results.
Introduction: the introduction is not well structured. Several repetitions are present in the text.
Line 35: Rephrasing is needed. One aspect is that OAE is accelerating a natural process; another aspect is that OAE is a CDR. The link to EW afterwards is a bit confusing.
Line 44: is missing
Lines 41 – 46: “The permanence of CO2 removal”: what is the connection of this paragraph to the study?
Lines 49 – 53: “These changes cause….A change in the primary producer community”. The transition from OA to OAE is ambiguous in these two sentences. There is a connection that is needed to shift from the effects of OA to the effects of OAEs
Lines 53-57: This part can be shortened. It reads like an intro of a thesis and after some years of research on OAE, such a long introduction is not needed. I strongly suggest the authors talk mainly about the topic they are interested in. Therefore, mention the impact of olivine due to the increase in other TMs (like Si) and do not mention the white hypothesis. For example, in line 87 you mentioned again the impact of increased TMs from olivine on diatoms.
Line 77: Please add i.e. or e.g. since there are hundreds of studies on this topic
Lines 91-92: “It is a diverse group”: What is the relevance of this sentence?
Lines 101-103: Sounds like a repetition of what is written in the previous lines when the authors introduced the groups that they decided to test. So far, it’s not clear which species were tested.
Experimental methods:
Line 115: Norway: do you have more information? From which company or institute?
Lines 125-126: “(BET analysis) of 1.81”. Is correct this way? or please rephrase
Lines 134: This sentence and the sentence from line 137 about As and Cr should go in the discussion.
Lines 133 – 134: Olivine’ trace metal….. use of concentration is redundant. The phrase “was detected in olivine” is redundant since it is already established that the trace metal content is part of olivine at the beginning of the sentence. There are multiple sentences of this nature throughout the text that could be streamlined for clarity and ease of reading.
Line 143: The whole section on strains and cultivation conditions should be revised. Some information on how the algae were treated is unclear or missing. For example, it took me some time to understand (and I’m not entirely sure yet) that the olivine was poured directly inside the culture bottles. Am I right?
Table 3: Bigelow?
Line 144: Chlorophyta is used here for the first time, there should be consistency in whether the authors use the species name or the taxon for what they are referring to.
Line 145: It is not clear what the authors mean by abrupt exposure, the issue of time with regards to the OAE application was not mentioned until now.
Line 146: Which following strains are the authors referring to?
Line 153: There is no mention of dolomite addition anywhere else in the methods. The authors should clarify the relevance of this information
Line 156: It is not clear what the authors mean by “…involving division of the additions of components by two”
Lines 172-173: I don’t get this part. Do you mean that before the experiment you added 100 ml of the stock cultures to 400 ml of a new medium? In case yes, please change the text to make it more understandable
Lines 175- 180: 1. Can you explain why different approaches were used towards the different strains? 2. The strain codes make it quite difficult to follow the text. I get it was easier for the authors to use codes instead of full names but you should find some other ways to name the species/strains so that the readers can understand immediately if they are referring to a diatom or a coccolithophore or anything else.
Lines 177: “… conditions similar to those mentioned”. Which conditions are you referring to?
Lines 181-182: You asses: 1. Carbonate chemistry perturbation; 2. TMs release by Olivine addition. Why do you mention only carbonate chemistry here? It is confusing.
Lines 182: Which days were the preliminary phase? Until now it was not stated that there were phases to be considered.
Lines 183: “This amount”…. While this may be the case in the previous experiments in Rønning et al, it is not the case from the results of this manuscript that TA and pH were maintained throughout the experimental period. The authors should address the irreproducibility of their results and their implications.
Lines 188: This sentence is convoluted due to the way the order in which information is given. Revise for clarity.
Lines 195-197: The duration of storage for Chl a samples before analysis should be given.
Lines 209: The authors should also report the 13C isotopic enrichment of the carbon source in atom %.
Lines 220: Carbonate system is repeated in one sentence. The sentence could be improved for clarity
Lines 240 - 253: This description of trace metal methodology is incomplete. Were the experiments conducted following GEOTRACES protocol for trace metal clean conditions? The sampling procedure including sampled volume for trace metal analysis has not been given.
Lines 254 - 264: Nutrient methodology is provided but the results have not been shown. Additionally, the detection limits for the nutrient analysis should be reported.
Results
The entire results section could use some shortening and streamlining.
It is very descriptive but missing a red thread concerning what is important to pay attention to. The authors often lose the reader with so many details, convoluted sentences and redundancy in their way of writing. Some descriptions are not accurate.
Total Alkalinity:
Are the trends described in the text real? Due to the big error bars, most of the changes look not significant within the same (each treatment) and when comparing the control and the olivine treatments. The error bars are very expanded so I guess there was a big variability within the replicates.
Figure 1 & Figure 2: The TA data on the x-axis is inconsistent between the olivine treatment and the control. In some cases, the starting conditions are the same and, not. It is also not understandable why the control in the Prochlorococcus NATL plot is higher than the olivine treatment. The authors should maybe use delta TA to make this plot much clearer.
It’s hard to follow the increase in TA (but also pH and DIC) since the y-axes have different scales. Please make new graphs with the same scales for all strains/species.
Lines 268: What ability are the authors referring to?
Lines 296: as mentioned before: 1. Why are fewer days measured for this species? It should be mentioned. 2. A better description of the trends is mandatory here since there are also some hidden and not clear patterns.
pH changes:
For the pH fluctuations similarly to the TA, the description of the results should be revised carefully. Some trends are indeed not described and the focus is sometimes on the clearer pattern.
Line 316: incubation: More precise here. Which one?
Line 324: huxleyi
Line 355: Micromonas: it’s not true. Negative impact?
Line 363: But I think it is significantly different only on day 20.
Line 373: E. huxleyi: But also the control took a long time before Chl a started to increase. On top of that the error bars are also very long so I’m not convinced that the differences are significant even within the control
Line 382: between? I guess one number is missing
Line 383. 1. Delete for and it. 2. As mentioned before make it explicit which species are you referring to. So please in this case add Prochlorococcus before the strain code.
Line 386: Please make it explicit that you are referring to the olivine treatment
Carbon fixation
Line 401-403: values are very different for the three Synechococcus species. The three strains should be described separately.
Why no statistical analysis was performed? You have replicates for every treatment. A very simple ANOVA could have been performed to assess significant differences. Looking at standard errors I doubt that in WH8102 the control and the olivine treatments are significantly different
Line 433: something missing in this sentence
Lines 436- 438: but you should consider the error bar! The first measurement has a huge error bar
Figure 6: Since only two-time points were taken for the nickel concentrations, box plots may be a better representation of the data than a line plots. Error bars are huge! Figure 6d for example: from 750 to 1500? similarly for Fig. 6a at day 25: from less than 550 to almost 2000?
Discussion:
Lines 485-486: not so true. Remember the study by Guo
Lines 499- 502: There is no statistical analysis that supports any of this conclusion
Lines 504-505: in your experiment? In case yes, not true and not always and with huge differences among the different 10 treatments
Lines 516-517: highly speculative...what does it mean? what is the connection? This is the species where the longest experiment was performed. The experiment lasted 44 days and you have fewer data points (for some unclear reasons). The decline of Ni could have been done to some kind of precipitation or any other process.
Lines 518-520: It's not clear that you refer to Xin et al., 2023
Line 529: in contrast?
Chapter 4.3: More an introduction chapter of the discussion...not adding anything relevant to the discussion.
Line 582: “And most likely also” ????
Line 596: are these refs related to the previous sentence?
Citation: https://doi.org/10.5194/egusphere-2023-2884-RC2
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