the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 18 Sep 2023
Influence of Ocean Alkalinity Enhancement with Olivine or Steel Slag on a Coastal Plankton Community in Tasmania
Abstract. Ocean alkalinity enhancement (OAE) aims to increase atmospheric CO2 sequestration in the oceans through the acceleration of chemical rock weathering. This could be achieved by grinding rocks containing alkaline minerals and adding the rock powder to the surface ocean where it dissolves and chemically locks CO2 in seawater as bicarbonate. However, CO2 sequestration during dissolution coincides with the release of potentially bio-active chemicals and may induce side effects. Here, we used 53 L microcosms to test how coastal plankton communities from Tasmania respond to OAE with olivine (mainly Mg2SiO4) or steel slag (mainly CaO and Ca(OH)2) as alkalinity sources. Three microcosms were left unperturbed and served as a control, three were enriched with olivine powder (1.9 g L−1), and three with steel slag powder (0.038 g L−1). Phytoplankton and zooplankton community responses as well as some biogeochemical parameters were monitored for 21 days. Olivine and steel slag additions increased total alkalinity by 29 µmol kg−1 and 361 µmol kg−1 respectively, which corresponds to a theoretical increase of 0.9 % and 14.8 % of the seawater storage capacity for atmospheric CO2. Olivine and steel slag released silicate nutrients into the water column, but steel slag released considerably more and also significant amounts of phosphate. Both minerals released dissolved aluminium (> 400 nmol L−1). The slag addition increased dissolved manganese concentrations (784 nmol L−1), while olivine increased dissolved nickel concentrations (38 nmol L−1). The slag treatment increased the total particulate manganese concentrations (22 nmol L−1), while olivine increased the total particulate nickel (5 nmol L−1), which was consistent with the increase in the dissolved concentrations of these trace metals in seawater. There was no significant difference in total chlorophyll a concentrations between the treatments and the control, likely due to nitrogen limitation of the phytoplankton community. However, flow cytometry results indicated an increase in the cellular abundance of several smaller (~<20 µm) phytoplankton groups in the olivine treatment compared to the slag treatment and the control. The abundance of larger phytoplankton (~>20 µm) decreased much more in the control than in the mineral addition treatments after day 10. Furthermore, the maximum quantum yields of photosystem II (Fv/Fm) were higher in slag and olivine treatments, suggesting that mineral additions increased photosynthetic performance. The zooplankton community composition was also affected with the most notable changes being observed in the dinoflagellate Noctiluca scintillans and the appendicularian Oikopleura sp. Overall, steel slag is much more efficient for CO2 removal with OAE than olivine and appears to be induce less changes in the plankton community when relating the CO2 removal potential to the level of environmental impact that was observed here.
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RC1: 'Comment on egusphere-2023-2120', D. A. Hutchins, 20 Oct 2023
General comments
This paper presents an interesting and ambitious experiment examining the biological, chemical, and biogeochemical effects of adding olivine (Mg2SiO4) or steel slag (primarily CaO) to a Tasmanian estuarine plankton community. A particular strength of the experimental design is the use of complex natural plankton communities in relatively large volume mesocosms, which improves the ecological relevance of the experiment. The biological sampling regime included bacteria and zooplankton in addition to the main focus on the phytoplankton community, and chemical measurements like carbonate chemistry, nutrients and dissolved and particulate trace metals all add additional valuable dimensions to this study. The findings of this incubation experiment will be of great interest to researchers seeking to understand the impacts of proposed OAE mitigation strategies on coastal marine ecosystems.
One important qualification of this study is that Guo et al. must necessarily deal with something of an “apples and oranges” issue with the two alkalinity sources they used. CaO is well known to be a far more concentrated source of alkalinity and dissolves much more readily and rapidly than olivine, as their results also show. This means that it is virtually impossible to make rigorous, quantitative “apples to apples” comparisons between slag and olivine by using equivalent levels of added alkalinity, adding identical weights or volumes of total mineral particulates, adding the same amount of mineral-associated trace metals or nutrients, or by using uniform levels of any other property they have in common to make comparisons. Thus, amounts of each mineral added are necessarily rather arbitrary. This means that direct comparisons between the treatments are highly context-dependent, in that a somewhat different experimental design (i.e., adding more or less of either component) is likely to yield quite different relative outcomes for the chemistry, and perhaps the biology too. This doesn’t compromise the value of their experiments, since the general trends in each treatment are still well worth presenting and considering, but it does suggest that interpreting the results in terms of direct quantitative comparisons between the two addition treatments should be done cautiously, and be explicitly qualified in the text.
Specific comments
Abstract, lines 22-26: Results for aluminum, manganese and nickel are described here, but many readers will also be looking for the iron results. Perhaps briefly include these in the Abstract too?
Methods, Figure 1 and lines 123-126: Using heat belts wrapped around the base of the mesocosms is an interesting and innovative way to control temperatures and set up convective circulation to help keep the plankton community in suspension. Was there a persistent vertical thermal gradient inside the mesocosms? It is also notable that temperatures were fairly variable in some of the mesocosms, with differences of up to 2-2.5C between replicates in some treatments on several days (Fig 2b). Is it possible that this affected replicability of some of the biological parameters?
Lines 185-187. The authors should be commended for acknowledging that they are not presenting trace metal or phosphate results from several samples they considered contaminated, a workaround which has often been used in the trace metal literature. However, throwing out 7 of the 36 samples (~23%) is an unusually high proportion of the total. It would perhaps be a good idea to add a small table showing these excluded measurements in the SI so readers can judge the merits of this decision for themselves. Along these lines, it would be good to know what precautions were taken to facilitate trace metal clean water collections, incubations and sampling. Other than some brief description of acid-washing supplies and equipment, no specific precautions are described in the Methods section. I agree with the authors that in situ trace metals in this (quite contaminated) estuary are naturally elevated, and obviously the mineral additions push these even higher, but levels of some easily-contaminated metals like Fe or Zn could still be accidentally significantly increased by sub-optimal experimental protocols.
Lines 203-209: The flow cytometer is an excellent way to enumerate single-cell phytoplankton or stained bacteria. However, it doesn’t work at all well to count chain-forming, very large or very spiny species like many diatoms and some dinoflagellates, groups which tend to be quite prominent in the coastal ocean. Were any other methods (microscopy, flow cam) used to assess the abundance of these often important groups that are not easily counted with flow cytometry?
Line 237: Please add a citation to the original paper presenting the oxalate wash cell surface-wash method (Tovar-Sanchez et al. 2003, Marine Chemistry 82).
Line 245: The CHN analyses would have yielded numbers for PON as well as the POC discussed here in the Methods and presented later. Are these PON data interesting and potentially worth presenting (possibly in the SI)? The PON values would also allow calculation of changes in whole plankton community C:N ratios, which could be worth examining too. On the subject of ratios, it might be interesting to normalize the BSi values to the POC and the PON to get an idea of the relative degree of silicification of the communities, instead of presenting BSi only as volume-normalized values in Fig 5.
Line 257: I am concerned about the accuracy of the zooplankton abundance measurements made using the self-made plankton net, which apparently had a diameter of only 1.5cm. Zooplankton tend to be patchily distributed, as they discuss later, and such limited volume sampling is likely be especially problematic for larger, low-abundance groups like larvaceans and copepods. The latter also have issues with active net avoidance that may be quite difficult to deal with using such a small collecting aperture.
Lines 340-345: This text probably belongs in the Statistics section of the Methods, not the Results.
Lines 390-392 and Fig. S3: It is interesting that the olivine released Cu to the seawater, but it is then puzzling that Cu was not reported to be present in the mineral stock used in Table 1.
Fig. 3: It is surprising that adding only 2 grams of slag to a 53L mesocosm can enrich seawater concentrations of phosphate and silicate to this extent. Although these elevated nutrient additions didn’t seem to have much of an effect on the biota in this N-limited experiment, in other regimes where P or Si are scarce this could definitely have a large impact. This issue should be discussed somewhere in the Discussion.
Lines 385- 405: This section on comparative trace metal releases from both alkalinity sources is a good example of my major general comment above. The relative amounts of metals released from each treatment are clearly a function of the relative amount of each material that was chosen to be added at the beginning: If (for instance) 3g slag had been added instead of 2g, or 50g olivine instead of 100g, the relative release results would likely look quite different. These results as presented are certainly valid, but are very context-dependent in that they only apply to the specific concentrations of each mineral that was added here. One way to deal with this issue would have been to test a range of concentrations of each of these two mineral sources, and examine the data in light of these two gradients. However, I recognize that in a large volume mesocosm experiment this many treatments is usually not practical. I do think some prominent qualifying text in the Discussion is needed to point this important caveat out to readers, though.
Line 419: Fig. 5 needs letters to differentiate the panels.
Lines 458-465: The trends in biovolume for these groups seem to be quite different from those of cell numbers reported in the previous paragraph. For instance, no differences in picoeukaryote, cyanobacteria or cryptophyte biovolumes were observed in any of the treatments relative to the control, whereas these groups were sometimes significantly higher in the olivine treatment when assessed using cell numbers. Why is this- were there changes in cell diameters and volumes in the treatments? The f.c. results should be able to show this, if so.
Lines 493-512: The much more noisy data for zooplankton than for phytoplankton is likely driven partly by greater patchiness of the former, as suggested here. I suggest this may have also been exacerbated by sampling error from the very small diameter plankton net used to make the collections, as detailed above.
Lines 549-554: I agree, it is hard to draw a direct cause and effect line between higher Fv/Fm and higher abundance.
Lines 596-609: To my knowledge, no one has shown that Mn or Ni additions can increase photosynthetic efficiency. If so, please cite appropriate references. In addition Mn, like Fe, is typically very abundant in coastal and riverine-influenced waters. I agree that it is puzzling that Fv/Fm increased in the slag and olivine additions despite ambient Fe levels of 100 nM or so, but attributing this response to other metals not known to influence photosynthetic efficiency is quite speculative.
Lines 617-626: Please see my comments above about patchiness of macrozooplankton and possible sampling artifacts, in view of these questions this paragraph on larvacean trends may be overinterpreting the data a bit.
Lines 719-730: Again, these concluding statements really apply only to the levels of slag and olivine chosen for this particular experiment, and some suggestion of the need for experiments comparing the two under other concentrations and initial conditions is probably needed. One of the reasons CaO sources like slag might have questionable environmental impacts is that they have the potential to cause extremely rapid and dramatic swings in the carbonate buffer system- for instance, pH increased ~0.5 units over just 4 days in the slag treatments here (Fig. 2a). This of course should drive a correspondingly large and rapid uptake of CO2 from the atmosphere, but could be potentially problematic for some marine organisms. It is reassuring that the plankton community used here was apparently able to accommodate to these major carbonate system swings with little sign of apparent stress. However, this is not necessarily going to be the case for marine metazoans including many invertebrates and fish, which as any aquarist knows are not very tolerant of rapid water chemistry changes. A few words about the need to examine impacts on other trophic levels of the marine food web in the concluding paragraphs would be in order.
Citation: https://doi.org/10.5194/egusphere-2023-2120-RC1 -
AC1: 'Reply on RC1', Jiaying Guo, 24 Oct 2023
Thank you for your valuable referee comments, which we greatly appreciate. We will thoroughly address each of your comments shortly. We also wish to extend our apologies for the error in our manuscript regarding the zooplankton net size unit. The correct size is "20cm height and 15cm width with a 210um mesh size" instead of "20mm height and 15mm width".
Citation: https://doi.org/10.5194/egusphere-2023-2120-AC1 -
RC2: 'Reply on AC1', D. A. Hutchins, 25 Oct 2023
That makes more sense!
Citation: https://doi.org/10.5194/egusphere-2023-2120-RC2 -
AC4: 'Reply on RC2', Jiaying Guo, 18 Dec 2023
Thank you for your comment and we are glad we could resolve the issue.
Citation: https://doi.org/10.5194/egusphere-2023-2120-AC4
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AC4: 'Reply on RC2', Jiaying Guo, 18 Dec 2023
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RC2: 'Reply on AC1', D. A. Hutchins, 25 Oct 2023
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AC3: 'Reply on RC1', Jiaying Guo, 11 Dec 2023
Dear referee,
Thank you for your comments on our manuscript. We appreciate the time and effort you have dedicated to providing your valuable feedback. Our point-by-point responses are included in the attached document. Please let me know if you have any questions.
Cheers,
Jiaying Guo
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AC1: 'Reply on RC1', Jiaying Guo, 24 Oct 2023
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RC3: 'Comment on egusphere-2023-2120', Anonymous Referee #2, 26 Oct 2023
The manuscript by Guo et al., presents a microcosm study on the influence of OAE on a Tasmanian estuarine plankton community, investigating two alkaline sources: olivine and steel slag. First of all, I want to compliment the authors of this ambitious study. The microcosm setup and the number of collected parameters are impressive.
The paper is generally well-written and well-organised. I truly enjoyed the reading.
I, however, found some weaknesses in the manuscript that I’m sure the authors will easily review it. I'm looking forward to seeing it accepted and published.
My comments are reported here under.
- The conclusion of this study is that the steel slag should be preferred to olivine. This is strongly stated in the abstract and in the conclusion. From my perspective, this comparison is risky and of little value because it contrasts two significantly different setups in which, from the outset, the release of alkalinity is extremely disparate between olivine and steel slag. I believe that this work does not lose its value by excluding this type of forced comparison. The difference in the quantity of the material added is one of the main aspects that makes this comparison hard to make. The experiment is still relevant and its solidity comes from the replicates but the lack of a gradient approach makes it pointless to compare the two tested materials. The authors should rephrase the abstract (Lines 34-35) and the conclusions considering this aspect and avoiding such a strong statement.
- Throughout the whole paper, there’s almost no discussion on the possible effect of the TA perturbation on the plankton community. The carbonate perturbation is quite mild with this set-up for the steel slag and even more for the olivine manipulation, but couldn’t the variation in pH or CO2 influence the phytoplankton community? For example, is it possible that some species were more influenced than others? This discussion is lacking throughout the text.
Methodology:
- Line 125: Can you provide temperature values? Was the temperature stable with the heat bell on throughout the experiment?
- Line 186: Don’t you have any data for particulate trace metals from other days? e.g. Day 13? That would be quite interesting to follow what happened just after the bloom. Said so, you mentioned 7 samples that were excluded from analyses and that 4 of them are coming from day 1. This number is quite high. Could you provide values? What does abnormal mean? And which other days/microcosms were excluded apart from the control ones?
Results:
- Lines: 320 -324 Considering the values reported at line 323, the turbidity was an important factor for the olive treatment. Here and in the discussion I think you should consider this aspect more. Were the particles still in suspension after day 5? Were the particles collected in the sediment trap or were they resuspended? The increase in turbidity hasn’t been considered enough as a potential negative effect of phytoplankton. I doubt and am extremely surprised that photosynthesis was not affected by a decline in light of about 20% on day 2…More discussion on that is needed.
- Line 333: The description of the increase in pH is misleading and the sentence should be rephrased. The increase in the olivine and control could be due to the blooming. The increase in the steel slag depends on the increase in TA. Please rephrase.
- Line 334: is the slightly higher pH in the olivine treatment compared to the control significant?
- Line 340-347: move this part to the method section (statistic analyses chapter)
- Lines 356-360 is the olivine significantly different from the control? I don’t get it for fCO2.
- Dissolved metals: Lines 385-390: you start this part mentioning Al and then Cu but none of them is reported in Figure 4. Can you move these graphs here from the supplementary? Since variations are described for the 2 treatments, it would be great to have the graphs here instead of opening the supplementary.
- Line 424 caption Figure 5: “The figure” delete one i.
- Line 433: I cannot follow the description of BSi. I cannot see the decline in the steel slag after peak 12 as described. The values are rather stable for the slag. Please check this description. In Figure 5b the lines are quite overlapping and hard to follow but the description is not precise.
- Line 437: the authors mention that they deleted BSi on day 2 and day 4 for olivine since they have outliers due to the presence of olivine particles. Did you keep days 2 and 4 for slag and control for the GAM analyses?
- Line 444: This description is misleading. You state that all the peaks of all groups happened on Day 4. Indeed you are right when you mentioned figures f-i. But for microphytoplankton, (Figure 5d) this peak is delayed (at days 6 or 8 depending on the treatment). Please check the text and the data and rephrase.
- Line 449: what are you referring to with “two groups”? Can you make it explicit?
- Line 475: are the differences in fv/fm significant?
Discussion:
- Line 531: why a limited effect? I would say a “no effect” since there are no differences for Chla between the control and the mineral treatments.
- Line 538: can you provide a ref?
- Line 549-554: The differences between the treatments (slag + olivine) and the control are visible for microphytoplantkon abundances and biovolume and for Fv/Fm. However, there’s a mismatch with time. Fv/Fm generally shows a fast signal, much earlier than phytoplankton abundance variations. However, the biovolume of the control starts to decline/differentiate from the olivine and slag treatments only after D14. I think therefore that your statement needs to be revised.
- Line 560: can you explain why you have a second bloom only for cyanobacteria in the olivine treatment and not for other phytoplankton groups since silica + phosphorous were still available? You state that it might be due to a top-down effect from zooplankton. And you say that this will be discussed in chapter 4.3 but I couldn’t find any good explanation here. Maybe some more lines would be good (here on in 4.3).
- Lines 578-579 + 589-594 But was iron-limited in the control? The dissolved iron is quite abundant in the control at D23. There’s around 100 nnmol/L iron. I think that this is quite speculative. Do you have any ideas about the main and dominating phytoplankton group in this estuarine area? Are there studies on this community and do you know from these studies their TM and Fe requirements?
- Line 622 and 629: the number of individuals/L in both Oikopleura and Penilia are extremely low. I wonder if this interpretation is noteworthy.
- Line 650-662: I found this paragraph a little bit out of context since the topic of the paper was about the impact of steel slag and olivine OAEs on a Tasmanian estuarine plankton community, I don’t see the connection between the quality of drinking water…
- Chapter 4.5 it’s not a real discussion. I appreciate the opening to this topic but I think that most of these lines could go in the introduction or in the conclusion to open up to new future studies. From line 691, the text is somehow unrelated to this specific study. I think this chapter should be shortened or incorporated somewhere else.
Good luck!
Citation: https://doi.org/10.5194/egusphere-2023-2120-RC3 -
AC2: 'Reply on RC3', Jiaying Guo, 11 Dec 2023
Dear referees,
Thank you for your comments on our manuscript. We appreciate the time and effort that you have dedicated to providing your valuable feedback. Here are our point-by-point responses to these comments and concerns.
Comments from Reviewer 2:
The manuscript by Guo et al., presents a microcosm study on the influence of OAE on a Tasmanian estuarine plankton community, investigating two alkaline sources: olivine and steel slag. First of all, I want to compliment the authors of this ambitious study. The microcosm setup and the number of collected parameters are impressive.
The paper is generally well-written and well-organised. I truly enjoyed the reading.
I, however, found some weaknesses in the manuscript that I’m sure the authors will easily review it. I'm looking forward to seeing it accepted and published.
Response: Thank you for your constructive and kind comments. We appreciate your time and effort.
Comment: My comments are reported here under.
- The conclusion of this study is that the steel slag should be preferred to olivine. This is strongly stated in the abstract and in the conclusion. From my perspective, this comparison is risky and of little value because it contrasts two significantly different setups in which, from the outset, the release of alkalinity is extremely disparate between olivine and steel slag. I believe that this work does not lose its value by excluding this type of forced comparison. The difference in the quantity of the material added is one of the main aspects that makes this comparison hard to make. The experiment is still relevant and its solidity comes from the replicates but the lack of a gradient approach makes it pointless to compare the two tested materials. The authors should rephrase the abstract (Lines 34-35) and the conclusions considering this aspect and avoiding such a strong statement.
Response: Thank you for pointing this out. Your major comment is consistent with the major comment by Reviewer 1 (Dave Hutchins). We agree that the amount of olivine and slag powder added in the treatments were significantly different resulting in the issue of a quantitative. Our original goal was to yield somewhat similar amounts of detectable alkalinity enhancement in the dissolved phase from olivine and slag addition. However, olivine was much less efficient in releasing alkalinity as we expected so that even a 50- fold higher additions of olivine (in mass) did not compensate for this difference. Therefore, our discussion mainly relates the observed environmental effects with the alkalinity enhancement achieved.
We don’t think that a comparison which relates the environmental impacts of the olivine treatment and the slag treatment is generally pointless as the amount of alkaline mineral used for an OAE deployment would likely also differ in the real world. We added the following text to the beginning of the discussion 4.2 to point towards the issue and clarify how we dealt with it.
“The amount of olivine and slag powder added to the treatments differed significantly (100 g of olivine powder were added while only 2 g of slag powder were added to the 53L microcosms). Our rationale for these different mass additions were to yield somewhat similar amounts of detectable alkalinity enhancement in the dissolved phase, since we already knew from tests before the experiment that slag is much more rapidly elevating alkalinity than olivine. However, olivine was less efficient in releasing alkalinity as we had anticipated so that even a 50-fold higher addition of olivine (in mass) did not compensate for this difference. As such, our experiments are associated with an “apples and oranges issue” in that our perturbation with minerals and associated OAE differs. We argue that an adjusted addition of minerals depending on the alkalinity enhancement rate would be consistent with what OAE practitioners may do under real-world conditions. Presumably, OAE deployments may have to adjust the amounts of minerals in order to detect alkalinity enhancement in the dissolved phase for verification purposes. Nevertheless, to account for the “apples and oranges issue”, the following discussion mainly relates the observed environmental effects with the alkalinity enhancement achieved over the course of the study.”
Comment:
- Throughout the whole paper, there’s almost no discussion on the possible effect of the TA perturbation on the plankton community. The carbonate perturbation is quite mild with this set-up for the steel slag and even more for the olivine manipulation, but couldn’t the variation in pH or CO2 influence the phytoplankton community? For example, is it possible that some species were more influenced than others? This discussion is lacking throughout the text.
Response: Thank you for your comment. We agree that the changes in pH and carbon chemistry could have influence the phytoplankton. The olivine treatment only brought small changes in the total alkalinity and pH, and there were not significant changes in phytoplankton abundance compared with the control based on the chlorophyll a result. Surprisingly, the drastic increase in total alkalinity (361 µmol kg-1) and pH (~0.5) observed in the slag treatment did not appear to have a noticeable effect, either positive or negative, on phytoplankton abundance. However, our result is consistent with what was found in Federer et al., (2022) that the addition of around 500 µmol L-1 alkalinity from NaOH solution had little effect on phytoplankton abundance. Therefore, we believe the variations in pH or TA within the microcosms had minimal impact on the abundance of our coastal phytoplankton. We added this discussion in secttion 4.2.1 (line 573-582). In addition, the pH or alkalinity may have influenced phytoplankton photosynthesis, so we explained the possibility of enhanced bicarbonate concentrations elevating Fv/Fm values in line 664-668.
Comment on Methodology:
- Line 125: Can you provide temperature values? Was the temperature stable with the heat bell on throughout the experiment?
Response: The temperature of seawater in each microcosm was measured every day and the results are presented in Fig. 2b in the manuscript. The temperature of seawater shows some variation due to the different position of microcosm in the temperature-control room, but this issue was mitigated by shuffling the microcosm position every day. This could have increased variability amongst replicates. However, on average there was no statistically significant difference between control/treatments during the experiment. We added a statement emphasizing that the convective mixing method could have introduced noise in the biological response data (Line 354-356).
Comment:
- Line 186: Don’t you have any data for particulate trace metals from other days? e.g. Day 13? That would be quite interesting to follow what happened just after the bloom. Said so, you mentioned 7 samples that were excluded from analyses and that 4 of them are coming from day 1. This number is quite high. Could you provide values? What does abnormal mean? And which other days/microcosms were excluded apart from the control ones?
Response: Thank you for flagging this. Unfortunately, we only have particulate trace metal data from day 1 and day 22. As for the excluded dissolved trace metal samples, we list the raw data in supplementary materials highlighting the excluded abnormal samples (Table S1). The sample with abnormal trace metal values were excluded from the results, and the way we determined whether they were abnormal or not is through the interquartile range (IQR) criterion. For example, we calculate the IQR, quartiles 1 (Q1) and quartiles 3 (Q3) for dissolved Fe concentrations on day 1, and because mesocosm 4 and mesocosm 8 values are outside of the range (Q1-1.5IQR to Q3+1.5IQR), we treat these two values as outliers. We then find the outlier of other trace metals on the same day, then we remove the whole mesocosm results containing these outliers. As for data from replicates after day 1 (mineral were added), we exclude the values that are more than 10 times higher than the other replicates within a treatment. Please note that in previous manuscript, we removed microcosm 5 and 7 on day one because their phosphate (P) concentrations were higher than other samples excluding the outliers. The P concentrations from these two microcosms measured by ICP-MS were also higher than the P concentrations measured by the spectrometer. However, these values actually fall into the IQR zone which means they are not outliers determined by IQR methods. So we decide to keep them in the revised manuscript.
Comment on Results:
- Lines: 320 -324 Considering the values reported at line 323, the turbidity was an important factor for the olive treatment. Here and in the discussion I think you should consider this aspect more. Were the particles still in suspension after day 5? Were the particles collected in the sediment trap or were they resuspended? The increase in turbidity hasn’t been considered enough as a potential negative effect of phytoplankton. I doubt and am extremely surprised that photosynthesis was not affected by a decline in light of about 20% on day 2…More discussion on that is needed.
Response: Thank you for flagging this issue. As we mentioned in the results, the addition of olivine caused an initial reduction in light intensity of 18.5 % at 15 mins after addition, which declined to 7.4 %, 3.7 %, 3.7 % and 0 % after 1, 2, 3, and 4 days, respectively. Based on these results, we suggest that the bulk of olivine particles had settled in the sediment trap and were no longer in suspension after day 5. We argue that the suspended particles in the olivine treatment may have led to artifacts in the measuring of photophysiology by FRRf. If lower light affected photophysiology, we would not expect a decrease in Fv/Fm, which is typically maximal at sub-saturating light. The most parsimonious explanation for the simultaneous reduction of all 3 parameters (Fv/Fm, ETR, and α) is interference by suspended olivine particles (i.e., absorption / scattering of light) during the FRRf measurement. Note that blank correction would not remove this artifact. We added this discussion in line 623-625. After day 5, the difference of photosynthesis performance between the olivine and the slag treatment was small while the control had significantly lower values indicating limited influence from particles in the olivine treatment.
Comment:
- Line 333: The description of the increase in pH is misleading and the sentence should be rephrased. The increase in the olivine and control could be due to the blooming. The increase in the steel slag depends on the increase in TA. Please rephrase.
Response: We agree and have rephrased the sentence (line 348-353).
Comment:
- Line 334: is the slightly higher pH in the olivine treatment compared to the control significant?
Response: Thank you for pointing this out. The pH in olivine and the control were not statistically significant. We rephrased the sentence to avoid misleading information. (Line 350).
Comment:
- Line 340-347: move this part to the method section (statistic analyses chapter)
Response: We agree and moved the relative description to the method section.
Comment:
- Lines 356-360 is the olivine significantly different from the control? I don’t get it for fCO2.
Response: The fitted GAMs revealed that there was a significant difference between the olivine treatment and the control. The significance test of the results is now attached to the supplementary material and the paragraph is revised accordingly (line 376).
Comment:
- Dissolved metals: Lines 385-390: you start this part mentioning Al and then Cu but none of them is reported in Figure 4. Can you move these graphs here from the supplementary? Since variations are described for the 2 treatments, it would be great to have the graphs here instead of opening the supplementary.
Response: Thank you for your comment. Fig.4 shows paired dissolved and particulate trace metal results, but we do not have particulate Al and Cu data to present. To be consistent, and for the sake of figure clarity, we prefer to present the dissolved Al and Cu data in the supplementary material.
Comment:
- Line 424 caption Figure 5: “The figure” delete one i.
Response: Thank you, and we deleted it accordingly.
Comment:
- Line 433: I cannot follow the description of BSi. I cannot see the decline in the steel slag after peak 12 as described. The values are rather stable for the slag. Please check this description. In Figure 5b the lines are quite overlapping and hard to follow but the description is not precise.
Response: Thank you for your comment. We have rephased the description. (Line 458-461).
Comment:
- Line 437: the authors mention that they deleted BSi on day 2 and day 4 for olivine since they have outliers due to the presence of olivine particles. Did you keep days 2 and 4 for slag and control for the GAM analyses?
Response: Yes, we kept the day 2 and day 4 data from the slag treatment and the control for GAM models and data analysis. The amounts of added slag were 50 times lower so that we did not observe noticeable amounts of slag in the incubated seawater.
Comment:
- Line 444: This description is misleading. You state that all the peaks of all groups happened on Day 4. Indeed you are right when you mentioned figures f-i. But for microphytoplankton, (Figure 5d) this peak is delayed (at days 6 or 8 depending on the treatment). Please check the text and the data and rephrase.
Response: Thank you for pointing out this issue. We have rephased the sentence by adding more information for microphytoplankton and nanoeukaryotes2. (Line 470-471)
Comment:
- Line 449: what are you referring to with “two groups”? Can you make it explicit?
Response: Thank you. These two groups means “the slag treatment and the control”. We have rephrased the sentence (line 478).
Comment:
- Line 475: are the differences in fv/fm significant?
Response: The change in Fv/Fm was significantly different between either treatment and the control. We have added the significance test results in the description (line 504-505).
Comment on Discussion:
- Line 531: why a limited effect? I would say a “no effect” since there are no differences for Chla between the control and the mineral treatments.
Response: Thank you for your comment. We have changed it into “no effect” (line 576).
Comment:
- Line 538: can you provide a ref?
Response: We moved the this sentence to line 590 and added a reference to improve the clarity of our argument. (line 591)
Comment:
- Line 549-554: The differences between the treatments (slag + olivine) and the control are visible for microphytoplantkon abundances and biovolume and for Fv/Fm. However, there’s a mismatch with time. Fv/Fm generally shows a fast signal, much earlier than phytoplankton abundance variations. However, the biovolume of the control starts to decline/differentiate from the olivine and slag treatments only after D14. I think therefore that your statement needs to be revised.
Response: Thank you for pointing this issue out. We agree that the decline of Fv/Fm was earlier than the decline of microphytoplankton cell abundance in the control. We have revised this description (Line 602-604).
Comment:
- Line 560: can you explain why you have a second bloom only for cyanobacteria in the olivine treatment and not for other phytoplankton groups since silica + phosphorous were still available? You state that it might be due to a top-down effect from zooplankton. And you say that this will be discussed in chapter 4.3 but I couldn’t find any good explanation here. Maybe some more lines would be good (here on in 4.3).
Response: Thank you for your feedback. We have added a sentence at line 688-690 that addresses this top-down effect: “The sectionhe second bloom of cyanobacteria in olivine is likely to be the results of decreased predators, like Penilia sp. and Oikopleura sp., although the changes in their abundance were not statistically significant between treatments and the control.”
Comment:
- Lines 578-579 + 589-594 But was iron-limited in the control? The dissolved iron is quite abundant in the control at D23. There’s around 100 nnmol/L iron. I think that this is quite speculative. Do you have any ideas about the main and dominating phytoplankton group in this estuarine area? Are there studies on this community and do you know from these studies their TM and Fe requirements?
Response: We can only speculate why the addition of minerals would enhance phytoplankton photosynthesis when the background dissolved Fe concentrations were more than 100 nmol/L. As we discussed in line 648-651, it’s possible that the coastal region has much higher organic ligands which limits the bioavailability of Fe, and the addition of Fe from minerals elevated the bioavailable Fe for phytoplankton. Unfortunately, we don’t have the phytoplankton species information in our mesocosm so we can’t compare our study with lab culture research.
Comment:
- Line 622 and 629: the number of individuals/L in both Oikopleura and Penilia are extremely low. I wonder if this interpretation is noteworthy.
Response: The concentrations are low relative to smaller organisms like phytoplankton but for comparatively larger zooplankton they are within the expected range. We think the data and discussion particularly about Oikopleura are interesting and important for the OAE assessment, noting that there are currently few data on the zooplankton response to OAE. We would like to keep this discussion in the text.
Comment:
- Line 650-662: I found this paragraph a little bit out of context since the topic of the paper was about the impact of steel slag and olivine OAEs on a Tasmanian estuarine plankton community, I don’t see the connection between the quality of drinking water…
Response: Thank you for your feedback. We listed the Australian Drinking Water Guidelines as a reference to the relatively safe trace metal concentrations for humans. We understand that this doesn’t mean the seawater with these OAE-related trace metal concentrations will be safe to all marine organisms, but it provides reference for readers when the marine trace metal safe standards are not available. Therefore, we prefer to keep this discussion to have some initial guidance of what government frameworks consider “safe”.
Comment:
- Chapter 4.5 it’s not a real discussion. I appreciate the opening to this topic but I think that most of these lines could go in the introduction or in the conclusion to open up to new future studies. From line 691, the text is somehow unrelated to this specific study. I think this chapter should be shortened or incorporated somewhere else.
Good luck!
Response: Thank you for your suggestions. We agree that this paragraph has less connection with our results and findings, but it also highlights a future OAE research direction. We have shortened this paragraph at section 4.2.4 to improve the flow of the article.
References:
Ferderer, A., Chase, Z., Kennedy, F., Schulz, K., Bach, L. T.: Assessing the influence of ocean alkalinity enhancement on a coastal phytoplankton community. Biogeosciences, 19, 5375-5399, https://doi.org/10.5194/bg-19-5375-2022, 2022.
Citation: https://doi.org/10.5194/egusphere-2023-2120-AC2
Status: closed
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RC1: 'Comment on egusphere-2023-2120', D. A. Hutchins, 20 Oct 2023
General comments
This paper presents an interesting and ambitious experiment examining the biological, chemical, and biogeochemical effects of adding olivine (Mg2SiO4) or steel slag (primarily CaO) to a Tasmanian estuarine plankton community. A particular strength of the experimental design is the use of complex natural plankton communities in relatively large volume mesocosms, which improves the ecological relevance of the experiment. The biological sampling regime included bacteria and zooplankton in addition to the main focus on the phytoplankton community, and chemical measurements like carbonate chemistry, nutrients and dissolved and particulate trace metals all add additional valuable dimensions to this study. The findings of this incubation experiment will be of great interest to researchers seeking to understand the impacts of proposed OAE mitigation strategies on coastal marine ecosystems.
One important qualification of this study is that Guo et al. must necessarily deal with something of an “apples and oranges” issue with the two alkalinity sources they used. CaO is well known to be a far more concentrated source of alkalinity and dissolves much more readily and rapidly than olivine, as their results also show. This means that it is virtually impossible to make rigorous, quantitative “apples to apples” comparisons between slag and olivine by using equivalent levels of added alkalinity, adding identical weights or volumes of total mineral particulates, adding the same amount of mineral-associated trace metals or nutrients, or by using uniform levels of any other property they have in common to make comparisons. Thus, amounts of each mineral added are necessarily rather arbitrary. This means that direct comparisons between the treatments are highly context-dependent, in that a somewhat different experimental design (i.e., adding more or less of either component) is likely to yield quite different relative outcomes for the chemistry, and perhaps the biology too. This doesn’t compromise the value of their experiments, since the general trends in each treatment are still well worth presenting and considering, but it does suggest that interpreting the results in terms of direct quantitative comparisons between the two addition treatments should be done cautiously, and be explicitly qualified in the text.
Specific comments
Abstract, lines 22-26: Results for aluminum, manganese and nickel are described here, but many readers will also be looking for the iron results. Perhaps briefly include these in the Abstract too?
Methods, Figure 1 and lines 123-126: Using heat belts wrapped around the base of the mesocosms is an interesting and innovative way to control temperatures and set up convective circulation to help keep the plankton community in suspension. Was there a persistent vertical thermal gradient inside the mesocosms? It is also notable that temperatures were fairly variable in some of the mesocosms, with differences of up to 2-2.5C between replicates in some treatments on several days (Fig 2b). Is it possible that this affected replicability of some of the biological parameters?
Lines 185-187. The authors should be commended for acknowledging that they are not presenting trace metal or phosphate results from several samples they considered contaminated, a workaround which has often been used in the trace metal literature. However, throwing out 7 of the 36 samples (~23%) is an unusually high proportion of the total. It would perhaps be a good idea to add a small table showing these excluded measurements in the SI so readers can judge the merits of this decision for themselves. Along these lines, it would be good to know what precautions were taken to facilitate trace metal clean water collections, incubations and sampling. Other than some brief description of acid-washing supplies and equipment, no specific precautions are described in the Methods section. I agree with the authors that in situ trace metals in this (quite contaminated) estuary are naturally elevated, and obviously the mineral additions push these even higher, but levels of some easily-contaminated metals like Fe or Zn could still be accidentally significantly increased by sub-optimal experimental protocols.
Lines 203-209: The flow cytometer is an excellent way to enumerate single-cell phytoplankton or stained bacteria. However, it doesn’t work at all well to count chain-forming, very large or very spiny species like many diatoms and some dinoflagellates, groups which tend to be quite prominent in the coastal ocean. Were any other methods (microscopy, flow cam) used to assess the abundance of these often important groups that are not easily counted with flow cytometry?
Line 237: Please add a citation to the original paper presenting the oxalate wash cell surface-wash method (Tovar-Sanchez et al. 2003, Marine Chemistry 82).
Line 245: The CHN analyses would have yielded numbers for PON as well as the POC discussed here in the Methods and presented later. Are these PON data interesting and potentially worth presenting (possibly in the SI)? The PON values would also allow calculation of changes in whole plankton community C:N ratios, which could be worth examining too. On the subject of ratios, it might be interesting to normalize the BSi values to the POC and the PON to get an idea of the relative degree of silicification of the communities, instead of presenting BSi only as volume-normalized values in Fig 5.
Line 257: I am concerned about the accuracy of the zooplankton abundance measurements made using the self-made plankton net, which apparently had a diameter of only 1.5cm. Zooplankton tend to be patchily distributed, as they discuss later, and such limited volume sampling is likely be especially problematic for larger, low-abundance groups like larvaceans and copepods. The latter also have issues with active net avoidance that may be quite difficult to deal with using such a small collecting aperture.
Lines 340-345: This text probably belongs in the Statistics section of the Methods, not the Results.
Lines 390-392 and Fig. S3: It is interesting that the olivine released Cu to the seawater, but it is then puzzling that Cu was not reported to be present in the mineral stock used in Table 1.
Fig. 3: It is surprising that adding only 2 grams of slag to a 53L mesocosm can enrich seawater concentrations of phosphate and silicate to this extent. Although these elevated nutrient additions didn’t seem to have much of an effect on the biota in this N-limited experiment, in other regimes where P or Si are scarce this could definitely have a large impact. This issue should be discussed somewhere in the Discussion.
Lines 385- 405: This section on comparative trace metal releases from both alkalinity sources is a good example of my major general comment above. The relative amounts of metals released from each treatment are clearly a function of the relative amount of each material that was chosen to be added at the beginning: If (for instance) 3g slag had been added instead of 2g, or 50g olivine instead of 100g, the relative release results would likely look quite different. These results as presented are certainly valid, but are very context-dependent in that they only apply to the specific concentrations of each mineral that was added here. One way to deal with this issue would have been to test a range of concentrations of each of these two mineral sources, and examine the data in light of these two gradients. However, I recognize that in a large volume mesocosm experiment this many treatments is usually not practical. I do think some prominent qualifying text in the Discussion is needed to point this important caveat out to readers, though.
Line 419: Fig. 5 needs letters to differentiate the panels.
Lines 458-465: The trends in biovolume for these groups seem to be quite different from those of cell numbers reported in the previous paragraph. For instance, no differences in picoeukaryote, cyanobacteria or cryptophyte biovolumes were observed in any of the treatments relative to the control, whereas these groups were sometimes significantly higher in the olivine treatment when assessed using cell numbers. Why is this- were there changes in cell diameters and volumes in the treatments? The f.c. results should be able to show this, if so.
Lines 493-512: The much more noisy data for zooplankton than for phytoplankton is likely driven partly by greater patchiness of the former, as suggested here. I suggest this may have also been exacerbated by sampling error from the very small diameter plankton net used to make the collections, as detailed above.
Lines 549-554: I agree, it is hard to draw a direct cause and effect line between higher Fv/Fm and higher abundance.
Lines 596-609: To my knowledge, no one has shown that Mn or Ni additions can increase photosynthetic efficiency. If so, please cite appropriate references. In addition Mn, like Fe, is typically very abundant in coastal and riverine-influenced waters. I agree that it is puzzling that Fv/Fm increased in the slag and olivine additions despite ambient Fe levels of 100 nM or so, but attributing this response to other metals not known to influence photosynthetic efficiency is quite speculative.
Lines 617-626: Please see my comments above about patchiness of macrozooplankton and possible sampling artifacts, in view of these questions this paragraph on larvacean trends may be overinterpreting the data a bit.
Lines 719-730: Again, these concluding statements really apply only to the levels of slag and olivine chosen for this particular experiment, and some suggestion of the need for experiments comparing the two under other concentrations and initial conditions is probably needed. One of the reasons CaO sources like slag might have questionable environmental impacts is that they have the potential to cause extremely rapid and dramatic swings in the carbonate buffer system- for instance, pH increased ~0.5 units over just 4 days in the slag treatments here (Fig. 2a). This of course should drive a correspondingly large and rapid uptake of CO2 from the atmosphere, but could be potentially problematic for some marine organisms. It is reassuring that the plankton community used here was apparently able to accommodate to these major carbonate system swings with little sign of apparent stress. However, this is not necessarily going to be the case for marine metazoans including many invertebrates and fish, which as any aquarist knows are not very tolerant of rapid water chemistry changes. A few words about the need to examine impacts on other trophic levels of the marine food web in the concluding paragraphs would be in order.
Citation: https://doi.org/10.5194/egusphere-2023-2120-RC1 -
AC1: 'Reply on RC1', Jiaying Guo, 24 Oct 2023
Thank you for your valuable referee comments, which we greatly appreciate. We will thoroughly address each of your comments shortly. We also wish to extend our apologies for the error in our manuscript regarding the zooplankton net size unit. The correct size is "20cm height and 15cm width with a 210um mesh size" instead of "20mm height and 15mm width".
Citation: https://doi.org/10.5194/egusphere-2023-2120-AC1 -
RC2: 'Reply on AC1', D. A. Hutchins, 25 Oct 2023
That makes more sense!
Citation: https://doi.org/10.5194/egusphere-2023-2120-RC2 -
AC4: 'Reply on RC2', Jiaying Guo, 18 Dec 2023
Thank you for your comment and we are glad we could resolve the issue.
Citation: https://doi.org/10.5194/egusphere-2023-2120-AC4
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AC4: 'Reply on RC2', Jiaying Guo, 18 Dec 2023
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RC2: 'Reply on AC1', D. A. Hutchins, 25 Oct 2023
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AC3: 'Reply on RC1', Jiaying Guo, 11 Dec 2023
Dear referee,
Thank you for your comments on our manuscript. We appreciate the time and effort you have dedicated to providing your valuable feedback. Our point-by-point responses are included in the attached document. Please let me know if you have any questions.
Cheers,
Jiaying Guo
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AC1: 'Reply on RC1', Jiaying Guo, 24 Oct 2023
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RC3: 'Comment on egusphere-2023-2120', Anonymous Referee #2, 26 Oct 2023
The manuscript by Guo et al., presents a microcosm study on the influence of OAE on a Tasmanian estuarine plankton community, investigating two alkaline sources: olivine and steel slag. First of all, I want to compliment the authors of this ambitious study. The microcosm setup and the number of collected parameters are impressive.
The paper is generally well-written and well-organised. I truly enjoyed the reading.
I, however, found some weaknesses in the manuscript that I’m sure the authors will easily review it. I'm looking forward to seeing it accepted and published.
My comments are reported here under.
- The conclusion of this study is that the steel slag should be preferred to olivine. This is strongly stated in the abstract and in the conclusion. From my perspective, this comparison is risky and of little value because it contrasts two significantly different setups in which, from the outset, the release of alkalinity is extremely disparate between olivine and steel slag. I believe that this work does not lose its value by excluding this type of forced comparison. The difference in the quantity of the material added is one of the main aspects that makes this comparison hard to make. The experiment is still relevant and its solidity comes from the replicates but the lack of a gradient approach makes it pointless to compare the two tested materials. The authors should rephrase the abstract (Lines 34-35) and the conclusions considering this aspect and avoiding such a strong statement.
- Throughout the whole paper, there’s almost no discussion on the possible effect of the TA perturbation on the plankton community. The carbonate perturbation is quite mild with this set-up for the steel slag and even more for the olivine manipulation, but couldn’t the variation in pH or CO2 influence the phytoplankton community? For example, is it possible that some species were more influenced than others? This discussion is lacking throughout the text.
Methodology:
- Line 125: Can you provide temperature values? Was the temperature stable with the heat bell on throughout the experiment?
- Line 186: Don’t you have any data for particulate trace metals from other days? e.g. Day 13? That would be quite interesting to follow what happened just after the bloom. Said so, you mentioned 7 samples that were excluded from analyses and that 4 of them are coming from day 1. This number is quite high. Could you provide values? What does abnormal mean? And which other days/microcosms were excluded apart from the control ones?
Results:
- Lines: 320 -324 Considering the values reported at line 323, the turbidity was an important factor for the olive treatment. Here and in the discussion I think you should consider this aspect more. Were the particles still in suspension after day 5? Were the particles collected in the sediment trap or were they resuspended? The increase in turbidity hasn’t been considered enough as a potential negative effect of phytoplankton. I doubt and am extremely surprised that photosynthesis was not affected by a decline in light of about 20% on day 2…More discussion on that is needed.
- Line 333: The description of the increase in pH is misleading and the sentence should be rephrased. The increase in the olivine and control could be due to the blooming. The increase in the steel slag depends on the increase in TA. Please rephrase.
- Line 334: is the slightly higher pH in the olivine treatment compared to the control significant?
- Line 340-347: move this part to the method section (statistic analyses chapter)
- Lines 356-360 is the olivine significantly different from the control? I don’t get it for fCO2.
- Dissolved metals: Lines 385-390: you start this part mentioning Al and then Cu but none of them is reported in Figure 4. Can you move these graphs here from the supplementary? Since variations are described for the 2 treatments, it would be great to have the graphs here instead of opening the supplementary.
- Line 424 caption Figure 5: “The figure” delete one i.
- Line 433: I cannot follow the description of BSi. I cannot see the decline in the steel slag after peak 12 as described. The values are rather stable for the slag. Please check this description. In Figure 5b the lines are quite overlapping and hard to follow but the description is not precise.
- Line 437: the authors mention that they deleted BSi on day 2 and day 4 for olivine since they have outliers due to the presence of olivine particles. Did you keep days 2 and 4 for slag and control for the GAM analyses?
- Line 444: This description is misleading. You state that all the peaks of all groups happened on Day 4. Indeed you are right when you mentioned figures f-i. But for microphytoplankton, (Figure 5d) this peak is delayed (at days 6 or 8 depending on the treatment). Please check the text and the data and rephrase.
- Line 449: what are you referring to with “two groups”? Can you make it explicit?
- Line 475: are the differences in fv/fm significant?
Discussion:
- Line 531: why a limited effect? I would say a “no effect” since there are no differences for Chla between the control and the mineral treatments.
- Line 538: can you provide a ref?
- Line 549-554: The differences between the treatments (slag + olivine) and the control are visible for microphytoplantkon abundances and biovolume and for Fv/Fm. However, there’s a mismatch with time. Fv/Fm generally shows a fast signal, much earlier than phytoplankton abundance variations. However, the biovolume of the control starts to decline/differentiate from the olivine and slag treatments only after D14. I think therefore that your statement needs to be revised.
- Line 560: can you explain why you have a second bloom only for cyanobacteria in the olivine treatment and not for other phytoplankton groups since silica + phosphorous were still available? You state that it might be due to a top-down effect from zooplankton. And you say that this will be discussed in chapter 4.3 but I couldn’t find any good explanation here. Maybe some more lines would be good (here on in 4.3).
- Lines 578-579 + 589-594 But was iron-limited in the control? The dissolved iron is quite abundant in the control at D23. There’s around 100 nnmol/L iron. I think that this is quite speculative. Do you have any ideas about the main and dominating phytoplankton group in this estuarine area? Are there studies on this community and do you know from these studies their TM and Fe requirements?
- Line 622 and 629: the number of individuals/L in both Oikopleura and Penilia are extremely low. I wonder if this interpretation is noteworthy.
- Line 650-662: I found this paragraph a little bit out of context since the topic of the paper was about the impact of steel slag and olivine OAEs on a Tasmanian estuarine plankton community, I don’t see the connection between the quality of drinking water…
- Chapter 4.5 it’s not a real discussion. I appreciate the opening to this topic but I think that most of these lines could go in the introduction or in the conclusion to open up to new future studies. From line 691, the text is somehow unrelated to this specific study. I think this chapter should be shortened or incorporated somewhere else.
Good luck!
Citation: https://doi.org/10.5194/egusphere-2023-2120-RC3 -
AC2: 'Reply on RC3', Jiaying Guo, 11 Dec 2023
Dear referees,
Thank you for your comments on our manuscript. We appreciate the time and effort that you have dedicated to providing your valuable feedback. Here are our point-by-point responses to these comments and concerns.
Comments from Reviewer 2:
The manuscript by Guo et al., presents a microcosm study on the influence of OAE on a Tasmanian estuarine plankton community, investigating two alkaline sources: olivine and steel slag. First of all, I want to compliment the authors of this ambitious study. The microcosm setup and the number of collected parameters are impressive.
The paper is generally well-written and well-organised. I truly enjoyed the reading.
I, however, found some weaknesses in the manuscript that I’m sure the authors will easily review it. I'm looking forward to seeing it accepted and published.
Response: Thank you for your constructive and kind comments. We appreciate your time and effort.
Comment: My comments are reported here under.
- The conclusion of this study is that the steel slag should be preferred to olivine. This is strongly stated in the abstract and in the conclusion. From my perspective, this comparison is risky and of little value because it contrasts two significantly different setups in which, from the outset, the release of alkalinity is extremely disparate between olivine and steel slag. I believe that this work does not lose its value by excluding this type of forced comparison. The difference in the quantity of the material added is one of the main aspects that makes this comparison hard to make. The experiment is still relevant and its solidity comes from the replicates but the lack of a gradient approach makes it pointless to compare the two tested materials. The authors should rephrase the abstract (Lines 34-35) and the conclusions considering this aspect and avoiding such a strong statement.
Response: Thank you for pointing this out. Your major comment is consistent with the major comment by Reviewer 1 (Dave Hutchins). We agree that the amount of olivine and slag powder added in the treatments were significantly different resulting in the issue of a quantitative. Our original goal was to yield somewhat similar amounts of detectable alkalinity enhancement in the dissolved phase from olivine and slag addition. However, olivine was much less efficient in releasing alkalinity as we expected so that even a 50- fold higher additions of olivine (in mass) did not compensate for this difference. Therefore, our discussion mainly relates the observed environmental effects with the alkalinity enhancement achieved.
We don’t think that a comparison which relates the environmental impacts of the olivine treatment and the slag treatment is generally pointless as the amount of alkaline mineral used for an OAE deployment would likely also differ in the real world. We added the following text to the beginning of the discussion 4.2 to point towards the issue and clarify how we dealt with it.
“The amount of olivine and slag powder added to the treatments differed significantly (100 g of olivine powder were added while only 2 g of slag powder were added to the 53L microcosms). Our rationale for these different mass additions were to yield somewhat similar amounts of detectable alkalinity enhancement in the dissolved phase, since we already knew from tests before the experiment that slag is much more rapidly elevating alkalinity than olivine. However, olivine was less efficient in releasing alkalinity as we had anticipated so that even a 50-fold higher addition of olivine (in mass) did not compensate for this difference. As such, our experiments are associated with an “apples and oranges issue” in that our perturbation with minerals and associated OAE differs. We argue that an adjusted addition of minerals depending on the alkalinity enhancement rate would be consistent with what OAE practitioners may do under real-world conditions. Presumably, OAE deployments may have to adjust the amounts of minerals in order to detect alkalinity enhancement in the dissolved phase for verification purposes. Nevertheless, to account for the “apples and oranges issue”, the following discussion mainly relates the observed environmental effects with the alkalinity enhancement achieved over the course of the study.”
Comment:
- Throughout the whole paper, there’s almost no discussion on the possible effect of the TA perturbation on the plankton community. The carbonate perturbation is quite mild with this set-up for the steel slag and even more for the olivine manipulation, but couldn’t the variation in pH or CO2 influence the phytoplankton community? For example, is it possible that some species were more influenced than others? This discussion is lacking throughout the text.
Response: Thank you for your comment. We agree that the changes in pH and carbon chemistry could have influence the phytoplankton. The olivine treatment only brought small changes in the total alkalinity and pH, and there were not significant changes in phytoplankton abundance compared with the control based on the chlorophyll a result. Surprisingly, the drastic increase in total alkalinity (361 µmol kg-1) and pH (~0.5) observed in the slag treatment did not appear to have a noticeable effect, either positive or negative, on phytoplankton abundance. However, our result is consistent with what was found in Federer et al., (2022) that the addition of around 500 µmol L-1 alkalinity from NaOH solution had little effect on phytoplankton abundance. Therefore, we believe the variations in pH or TA within the microcosms had minimal impact on the abundance of our coastal phytoplankton. We added this discussion in secttion 4.2.1 (line 573-582). In addition, the pH or alkalinity may have influenced phytoplankton photosynthesis, so we explained the possibility of enhanced bicarbonate concentrations elevating Fv/Fm values in line 664-668.
Comment on Methodology:
- Line 125: Can you provide temperature values? Was the temperature stable with the heat bell on throughout the experiment?
Response: The temperature of seawater in each microcosm was measured every day and the results are presented in Fig. 2b in the manuscript. The temperature of seawater shows some variation due to the different position of microcosm in the temperature-control room, but this issue was mitigated by shuffling the microcosm position every day. This could have increased variability amongst replicates. However, on average there was no statistically significant difference between control/treatments during the experiment. We added a statement emphasizing that the convective mixing method could have introduced noise in the biological response data (Line 354-356).
Comment:
- Line 186: Don’t you have any data for particulate trace metals from other days? e.g. Day 13? That would be quite interesting to follow what happened just after the bloom. Said so, you mentioned 7 samples that were excluded from analyses and that 4 of them are coming from day 1. This number is quite high. Could you provide values? What does abnormal mean? And which other days/microcosms were excluded apart from the control ones?
Response: Thank you for flagging this. Unfortunately, we only have particulate trace metal data from day 1 and day 22. As for the excluded dissolved trace metal samples, we list the raw data in supplementary materials highlighting the excluded abnormal samples (Table S1). The sample with abnormal trace metal values were excluded from the results, and the way we determined whether they were abnormal or not is through the interquartile range (IQR) criterion. For example, we calculate the IQR, quartiles 1 (Q1) and quartiles 3 (Q3) for dissolved Fe concentrations on day 1, and because mesocosm 4 and mesocosm 8 values are outside of the range (Q1-1.5IQR to Q3+1.5IQR), we treat these two values as outliers. We then find the outlier of other trace metals on the same day, then we remove the whole mesocosm results containing these outliers. As for data from replicates after day 1 (mineral were added), we exclude the values that are more than 10 times higher than the other replicates within a treatment. Please note that in previous manuscript, we removed microcosm 5 and 7 on day one because their phosphate (P) concentrations were higher than other samples excluding the outliers. The P concentrations from these two microcosms measured by ICP-MS were also higher than the P concentrations measured by the spectrometer. However, these values actually fall into the IQR zone which means they are not outliers determined by IQR methods. So we decide to keep them in the revised manuscript.
Comment on Results:
- Lines: 320 -324 Considering the values reported at line 323, the turbidity was an important factor for the olive treatment. Here and in the discussion I think you should consider this aspect more. Were the particles still in suspension after day 5? Were the particles collected in the sediment trap or were they resuspended? The increase in turbidity hasn’t been considered enough as a potential negative effect of phytoplankton. I doubt and am extremely surprised that photosynthesis was not affected by a decline in light of about 20% on day 2…More discussion on that is needed.
Response: Thank you for flagging this issue. As we mentioned in the results, the addition of olivine caused an initial reduction in light intensity of 18.5 % at 15 mins after addition, which declined to 7.4 %, 3.7 %, 3.7 % and 0 % after 1, 2, 3, and 4 days, respectively. Based on these results, we suggest that the bulk of olivine particles had settled in the sediment trap and were no longer in suspension after day 5. We argue that the suspended particles in the olivine treatment may have led to artifacts in the measuring of photophysiology by FRRf. If lower light affected photophysiology, we would not expect a decrease in Fv/Fm, which is typically maximal at sub-saturating light. The most parsimonious explanation for the simultaneous reduction of all 3 parameters (Fv/Fm, ETR, and α) is interference by suspended olivine particles (i.e., absorption / scattering of light) during the FRRf measurement. Note that blank correction would not remove this artifact. We added this discussion in line 623-625. After day 5, the difference of photosynthesis performance between the olivine and the slag treatment was small while the control had significantly lower values indicating limited influence from particles in the olivine treatment.
Comment:
- Line 333: The description of the increase in pH is misleading and the sentence should be rephrased. The increase in the olivine and control could be due to the blooming. The increase in the steel slag depends on the increase in TA. Please rephrase.
Response: We agree and have rephrased the sentence (line 348-353).
Comment:
- Line 334: is the slightly higher pH in the olivine treatment compared to the control significant?
Response: Thank you for pointing this out. The pH in olivine and the control were not statistically significant. We rephrased the sentence to avoid misleading information. (Line 350).
Comment:
- Line 340-347: move this part to the method section (statistic analyses chapter)
Response: We agree and moved the relative description to the method section.
Comment:
- Lines 356-360 is the olivine significantly different from the control? I don’t get it for fCO2.
Response: The fitted GAMs revealed that there was a significant difference between the olivine treatment and the control. The significance test of the results is now attached to the supplementary material and the paragraph is revised accordingly (line 376).
Comment:
- Dissolved metals: Lines 385-390: you start this part mentioning Al and then Cu but none of them is reported in Figure 4. Can you move these graphs here from the supplementary? Since variations are described for the 2 treatments, it would be great to have the graphs here instead of opening the supplementary.
Response: Thank you for your comment. Fig.4 shows paired dissolved and particulate trace metal results, but we do not have particulate Al and Cu data to present. To be consistent, and for the sake of figure clarity, we prefer to present the dissolved Al and Cu data in the supplementary material.
Comment:
- Line 424 caption Figure 5: “The figure” delete one i.
Response: Thank you, and we deleted it accordingly.
Comment:
- Line 433: I cannot follow the description of BSi. I cannot see the decline in the steel slag after peak 12 as described. The values are rather stable for the slag. Please check this description. In Figure 5b the lines are quite overlapping and hard to follow but the description is not precise.
Response: Thank you for your comment. We have rephased the description. (Line 458-461).
Comment:
- Line 437: the authors mention that they deleted BSi on day 2 and day 4 for olivine since they have outliers due to the presence of olivine particles. Did you keep days 2 and 4 for slag and control for the GAM analyses?
Response: Yes, we kept the day 2 and day 4 data from the slag treatment and the control for GAM models and data analysis. The amounts of added slag were 50 times lower so that we did not observe noticeable amounts of slag in the incubated seawater.
Comment:
- Line 444: This description is misleading. You state that all the peaks of all groups happened on Day 4. Indeed you are right when you mentioned figures f-i. But for microphytoplankton, (Figure 5d) this peak is delayed (at days 6 or 8 depending on the treatment). Please check the text and the data and rephrase.
Response: Thank you for pointing out this issue. We have rephased the sentence by adding more information for microphytoplankton and nanoeukaryotes2. (Line 470-471)
Comment:
- Line 449: what are you referring to with “two groups”? Can you make it explicit?
Response: Thank you. These two groups means “the slag treatment and the control”. We have rephrased the sentence (line 478).
Comment:
- Line 475: are the differences in fv/fm significant?
Response: The change in Fv/Fm was significantly different between either treatment and the control. We have added the significance test results in the description (line 504-505).
Comment on Discussion:
- Line 531: why a limited effect? I would say a “no effect” since there are no differences for Chla between the control and the mineral treatments.
Response: Thank you for your comment. We have changed it into “no effect” (line 576).
Comment:
- Line 538: can you provide a ref?
Response: We moved the this sentence to line 590 and added a reference to improve the clarity of our argument. (line 591)
Comment:
- Line 549-554: The differences between the treatments (slag + olivine) and the control are visible for microphytoplantkon abundances and biovolume and for Fv/Fm. However, there’s a mismatch with time. Fv/Fm generally shows a fast signal, much earlier than phytoplankton abundance variations. However, the biovolume of the control starts to decline/differentiate from the olivine and slag treatments only after D14. I think therefore that your statement needs to be revised.
Response: Thank you for pointing this issue out. We agree that the decline of Fv/Fm was earlier than the decline of microphytoplankton cell abundance in the control. We have revised this description (Line 602-604).
Comment:
- Line 560: can you explain why you have a second bloom only for cyanobacteria in the olivine treatment and not for other phytoplankton groups since silica + phosphorous were still available? You state that it might be due to a top-down effect from zooplankton. And you say that this will be discussed in chapter 4.3 but I couldn’t find any good explanation here. Maybe some more lines would be good (here on in 4.3).
Response: Thank you for your feedback. We have added a sentence at line 688-690 that addresses this top-down effect: “The sectionhe second bloom of cyanobacteria in olivine is likely to be the results of decreased predators, like Penilia sp. and Oikopleura sp., although the changes in their abundance were not statistically significant between treatments and the control.”
Comment:
- Lines 578-579 + 589-594 But was iron-limited in the control? The dissolved iron is quite abundant in the control at D23. There’s around 100 nnmol/L iron. I think that this is quite speculative. Do you have any ideas about the main and dominating phytoplankton group in this estuarine area? Are there studies on this community and do you know from these studies their TM and Fe requirements?
Response: We can only speculate why the addition of minerals would enhance phytoplankton photosynthesis when the background dissolved Fe concentrations were more than 100 nmol/L. As we discussed in line 648-651, it’s possible that the coastal region has much higher organic ligands which limits the bioavailability of Fe, and the addition of Fe from minerals elevated the bioavailable Fe for phytoplankton. Unfortunately, we don’t have the phytoplankton species information in our mesocosm so we can’t compare our study with lab culture research.
Comment:
- Line 622 and 629: the number of individuals/L in both Oikopleura and Penilia are extremely low. I wonder if this interpretation is noteworthy.
Response: The concentrations are low relative to smaller organisms like phytoplankton but for comparatively larger zooplankton they are within the expected range. We think the data and discussion particularly about Oikopleura are interesting and important for the OAE assessment, noting that there are currently few data on the zooplankton response to OAE. We would like to keep this discussion in the text.
Comment:
- Line 650-662: I found this paragraph a little bit out of context since the topic of the paper was about the impact of steel slag and olivine OAEs on a Tasmanian estuarine plankton community, I don’t see the connection between the quality of drinking water…
Response: Thank you for your feedback. We listed the Australian Drinking Water Guidelines as a reference to the relatively safe trace metal concentrations for humans. We understand that this doesn’t mean the seawater with these OAE-related trace metal concentrations will be safe to all marine organisms, but it provides reference for readers when the marine trace metal safe standards are not available. Therefore, we prefer to keep this discussion to have some initial guidance of what government frameworks consider “safe”.
Comment:
- Chapter 4.5 it’s not a real discussion. I appreciate the opening to this topic but I think that most of these lines could go in the introduction or in the conclusion to open up to new future studies. From line 691, the text is somehow unrelated to this specific study. I think this chapter should be shortened or incorporated somewhere else.
Good luck!
Response: Thank you for your suggestions. We agree that this paragraph has less connection with our results and findings, but it also highlights a future OAE research direction. We have shortened this paragraph at section 4.2.4 to improve the flow of the article.
References:
Ferderer, A., Chase, Z., Kennedy, F., Schulz, K., Bach, L. T.: Assessing the influence of ocean alkalinity enhancement on a coastal phytoplankton community. Biogeosciences, 19, 5375-5399, https://doi.org/10.5194/bg-19-5375-2022, 2022.
Citation: https://doi.org/10.5194/egusphere-2023-2120-AC2
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