In my review of the original manuscript, I raised a number of concerns, which the authors have tried to address in their revised manuscript along with their response to the reviewers. They have dedicated much effort to this task, which is commendable. However, I still have some non-trivial concerns with the revised manuscript.
TWO MAJOR CONCERNS
In my original review, my concerns were listed in order of importance. My first concern was that the original manuscript did not consider potential misinterpretation of pH changes, which because of the log scale depend on the initial state of [H+] not just the change in [H+]. The authors response was to (1) mention H+ in the Introduction, (2) add a 4-line paragraph mentioning this concern, and (3) add Figure S17 and Table 7, which show trends in [H+]. In their response they also say "the pH variations in this study are relatively small, and our results do therefore not look significantly different if analyzing H+ instead". They also state that they "remade all our plots showing pH change to verify this", although they only show Figure S17. But in some of the pH maps in the revised manuscript, there are differences in pH across the Nordic Seas of about 0.1 for the preindustrial references state (Figure 4) and about 0.15 for the present-day reference state (Figure 8). These differences appear small, but they imply 30% to 40% differences in terms of the initial value of [H+]. These regional differences in the initial state of surface pH are much larger than the regional differences in the pH change between preindustrial and present (0.02, Fig. 4) and between present and future under RCP2.6 (0.04, Fig. 8); they are comparable to those between present and future under RCP8.5 (0.15, Fig. 10). Therefore differences in the pH reference state (preindustrial or present) shown in the maps of Figs. 4, 8, and 10 will have a substantial effect on the computed pH change. The authors have taken my previous comment too lightly. I asked for major revisions, but they did not comply. I did not ask that they not show pH in the revised manuscript, something they seem to imply in their response. This concern could be properly addressed if the authors would show changes in both H+ and pH on the same set of plots and if they would quantify how much of the regional differences in the pH change are due to differences in the initial state of [H+] and how much is due to the change in [H+].
My second concern expressed was that the authors were only using 1 model to make projections. In response, the revised manuscript now compares results from multiple CMIP5 Earth system models (ESMs) for some of the analyses. To make this comparison, the authors rely results from those models under emissions-driven, not concentration-driven scenarios. Unfortunately, the emission-driven scenarios mentioned by the authors are not part of the core set of CMIP5 experiments (Taylor et al., 2012). The concentration-driven scenarios were designed for CMIP and IPCC to be the standard way of comparing models because that way the atmospheric CO2 forcing, both radiative and geochemical, remains identical between models. Otherwise, with an emissions-driven scenario the choice of a terrestrial carbon-cycle component of an ESM, may lead to quite unrealistic atmospheric CO2 levels and thus have an undue influence on ocean carbon. That is why the concentration-driven scenarios have been used in the most cited previous studies that compare CMIP5 as well as CMIP6 Earth system models (Bopp et al. 2013, Kwiatkowski et al., 2020). Yes, an emission-driven scenario can be used IN ADDITION to a concentration driven scenario to study carbon-cycle feedbacks, but that is not the focus of the authors in this study. Therefore the authors comparison of the CMIP5 ESMs using emission-driven scenarios alone is poor experimental design.
The authors further confuse the subject by calling their emission-driven scenarios "RCPs" (Relative Concentration Pathways). Yes, CMIP5 provided emissions for the emission-driven scenarios, such as "esmrcp85", the same set of emissions used to drive the chosen integrated assessment model to come up with the common concentration pathway used by all ESMs under RCP8.5. But the authors cannot refer to their simulations as those from relative concentration pathways (RCPs). The best way to remedy this problem would be for the authors to compare results from the ESMs forced under the actual relative concentration pathways (experiments rcp26, rcp45, rcp85), as has previous work, instead of the emission-driven scenarios (esmrcp26, esmrcp45, esmrcp85).
Overall, it appears to me that this manuscript still would still require substantial revision, and thus I cannot recommend it for publication at this time.
OTHER CONCERNS (of moderate or minor importance, language suggestions)
Title: The title "Nordic Seas Acidification" does not quite work because "Nordic Seas acidifcation". For the same reason, we cannot say "Oceans Acidfication". Thus I suggest to change the title to "Acidification of the Nordic Seas".
ABSTRACT
L2: change "Nordic Seas is" to "Nordic Seas are"
L3-5: The second sentence is hard to understand because of too many clauses and commas. It should be rewritten. A solution that could work would be simply to delete ", and its impact on cold-water corals,". Moreover, this paper does not investigate impacts on cold-water corals, only the aragonite saturation state of the waters that corals may be exposed to. In addition, cold-water corals are mentioned later in the abstract so there is no need to try to squeeze that in here.
L6-7: The authors make contradictory statements about impacts of the shoaling ASH on cold-water corals (compare L6-7 to L14-15).
L8: "significant" should not be used here (or elsewhere) unless it is replaced by "statistically significant" and the authors tell us with respect to what it is statistically significant.
L10: same problem as L8
L14: change "to be lifted to" to "to shoal by"
L16-17: delete the qualitative ending ", which to some extent is opposed by increasing alkalinity".
INTRODUCTION
The objectives at end of Introduction (just before subsection 1.1) should be refined. Is the justification for this study just that the authors want to look at rates of acidification in both models and observations? Would they expect those rates to be so different from previous estimates. If so, why would they differ substantially. Unfortunately, the authors fail to return to this so-called gap in the Discussion, i.e., by comparing their results to the previous estimates of Skogen et al. (2014, 2018).
L34: change "its" to "their"
L35: It would be clearer if the authors changed "characterized" by "dominated"
L39: change "comes as a result of" to "results from"
L42: change "and consequently help" to ", helping"
L44-45: Confusing. I think the authors should replace "would ultimately lead to early and relatively large detection" with "leads to higher".
L46: change the verbose "have negative impacts on" to "degrade"
L52. "Acidification rates" is ambiguous. All readers will not get that you mean pH change. Please refer to pH change explicitly.
SUBSECTION 1.1
- You cannot have a subsection 1.1 if you do not have a subsection 1.2
- This section seems to be a repetition of well-known CO2 system chemistry in the ocean. It is largely textbook material.
Because it is not novel, please just to delete it and cite references where readers can go if they are unfamiliar with seawater CO2 chemistry.
- Equation (4): I think that if the authors are going to actually give equations with [H+] or pH, they should also mention that in seawater oceanographers have different pH scales, while also pointing out the pH scale that they have adopted for this study (presumably the total scale).
L115: Is it a Norwegian or EU program. Please state.
L123-124: What does "considered consistent" mean? The last part of the sentence could be shortened to "4 umol kg-1 for both Ct and At"
L139: shorten last part of sentence as suggested just above.
Section 2.1.2: see 2nd major comment
Section 2.2.2
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L204:
- change the verbose "It is important to keep in mind that" to "Because"
- delete "and that"
L207: Why say "are relatively small". Cannot the authors be more quantitative?
Present
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L209-210: Why mention temperature twice in the same sentence?
L217-218: suggest to change " (they are" with ", being" and to remove the final ")".
L222: comma fault: remove the comma
L227: change "generally is" to "are generally"
L235 (Equation (7)): The authors need to explicitly state how they calculate the partial derivatives.
L239: what is meant by "it"?
L248-249: The rates of change of atmospheric xCO2 (ppm) and atmospheric pCO2 (uatm) will not be identical unless the correction factor between them is 1 (e.g., atmospheric pressure of 1 atm and no humidity). In the cold high latitudes the atmospheric pressures are substantially less than 1 on average. The authors could say though that the rates of change of those two variables are proportional.
Section 2.2.3
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L270: in the "MATLAB version of" CO2SYS?
L280-281: While systematic uncertainties would tend to cancel out when calculating differences, random uncertainties would not.
L296: Delete "We note that"
RESULTS
line 315:
- suggest to change "model ensemble range" to "CMIP5 model range". The word ensemble as used by modelers is ambiguous (multiple simulations with the same model or multiple models).
- The CMIP5 model range in final pH is actually quite large. It would be much tighter if the authors would have compared results from the concentration driven pathways rather than the emission driven pathways.
line 324: Delete "Note that". How much lower?
line 325: change "the one" to "that"
line 329: The reference to Dai et al. (2019, Nature Comm.) confuses the issue. Consistent with previous studies, Dai et al. define Arctic amplification in terms of surface air temperature, not surface ocean temperature. In the Arctic there has been little warming of surface sea surface temperature because of ice cover; conversely, there has been enhanced warming of surface air temperature, i.e., about twice the global average. But what about the Nordic Seas that are largely ice free even during winter? I would expect the authors to focus on the Nordic Seas, given the title of the paper. Is the historical SST change there higher than the global average?
Lines 327-330: To make this statement, the authors would need to demonstrate that the SST change in the Nordic Seas is actually higher than the global average. Or it could be documented with appropriate references.
line 334: delete "its"
line 337: It would be simpler and clearer if the authors could write "from southeast to northwest".
line 337-338: I do not see evidence in Figure S15 for the authors statement here that CT increases with decreasing T in the Atlantic water. Furthermore, CT is a conservative property with respect to changes in temperature, so the authors would need to be clearer about the processes that make surface CT increase with temperature.
lines 338-339: Please explain why the CT of polar waters is lower than that of Atlantic waters?
lines 341-343: I have some problems with this statement:
* The statement that "pH decreases with increasing temperature, salinity, CT and AT (... Fig. S16)" is not clear in Fig S16. For Atlantic waters there seems little correlation, while for polar waters, there are vastly different relationships
* The use of "strong" and "significant" in this sentence does not seem to be supported by Fig S16.
* The correlations of pH vs salinity, pH vs CT, and pH vs AT look extremely similar, suggesting that the latter two are also driven by changes in salinity.
lines 343-345:
* The authors seem to infer that if the drivers were perfectly orthogonal it would be possible to calculate the contributions of each driver from such correlation plots (Fig. S16). But even in this ideal case, I do not think that is possible.
* Is not the conclusion at the end of the sentence something we could not already say before this analysis? I think the authors could do better than make this weak statement.
Line 349:
- change "to the picture" to "contributions"
- the parenthetical statement "(temperature, CT and AT explain all together 89%)" is redundant. It should be deleted.
Line 361: remove the comma
line 362: change "relation" to "relationship"
line 371: delete "are counteracting, they"
line 372: "solubility of OmegaAr"? Do the authors mean "solubility product"?
line 390: What is "Fig. 4.1"? The same problem is found in the title to Table 5.
line 413:
* "this period of time"? Please be more specific.
* "we detect trends in the uncertainties". Some detail is needed.
line 442: The authors refer to "The strong positive trend in pCO2", but it seems they actually mean to refer to Delta pCO2. Unclear.
line 469 and 471: missing Figure number
line 497: "salinity decomposition" is ambiguous. I would recommend to change that to ""more detailed freshwater decomposition".
lines 498-500: I disagree with the authors statement here that seems to say that the uncertainties of freshwater component compromise the assessment of the so-called biogeochemical component. The uncertainties concerning the freshwater component may be large but the freshwater contributions of AT and CT counterbalance one another, making their combined contribution negligible. The uncertainties will typically affect freshwater contributions from AT and CT in equal an opposite ways and thus they don't really matter for the BGC component.
line 516: What does "reduces/amplify" mean? Please use the word or words you mean instead of the slash, which is ambiguous.
line 535: change "4.5" to "RCP4.5"
line 549: It would be better to begin the sentence with "Assuming a Redfield ratio of O2:C = 132:106,"
line 553: The errors in the way the authors approximate the partial derivatives (sensitivities) are not mentioned, but are probably as large or larger than the other factors mentioned.
line 589: ambiguous. What does upper bound mean? shallower or deeper?
SUMMARY AND CONCLUSIONS
It is not clear in the Discussion nor in the Conclusions how the authors have filled the gap they pointed out in the Introduction, namely the advances made by this study relative to the previous work by Skogan et al. Indeed the findings of Skogan et al. were never really mentioned, so we don't have anything to compare this work to. The authors need to bring this up in the Conclusions. To what extent do the findings of this study confirm or contradict previous work. To what extent do they embark on completely new territory. How has our knowledge been incremented by this study. The Conclusions section mostly just reiterates what was said in previous sections and ends with a caveat, a detail about a minor part of the work. The big picture seems to be missing.
line 611: What is meant by "careful estimates"? Do the authors mean "conservative estimates"? If so, I am surprised. Since NorESM1-ME tends to simulate an ASH that is too shallow, does that not imply a bias in the opposite direction, i.e., corals will be projected to be exposed too soon to undersaturated waters. This it seems not a conservative estimate but rather the opposite.
line 614-615: The authors state "The effects of increasing CT is slightly opposed by increasing AT , which partly comes as a result of the increasing salinities". But I find this statement puzzling. Based on their freshwater Taylor expansion (Fig. S19), the change in salinity has an equal and opposite effect on CT and AT. These effects cancel out. The same figure shows that it is the changes in the biogeochemical AT term that partly counterbalances the changes in the biogeochemical CT term. Salinity changes have nothing to do with that.
line 616: I am confused by this phrase: "the impact of temperature in the surface is ambiguous, and even shows a cooling in some places". What is meant by "ambiguous"? Could that phrase be replaced by something simpler such as "at the surface, there is cooling in some places."
line 629: change the first "to" to "too"
FIGURES
Figure 10: change "rates of" to "the". To the GLODAP estimate for the present, the authors added the change, not the rates of change.
Fig. 11: I think that this figure and the simple Taylor expansion should NOT be included in this paper. It offers no added value and only makes the paper longer. Only the freshwater Taylor expansion should be shown and discussed. Yes the latter is slightly more complex, but it is better because it is able to show that the combined contribution of salinity-driven changes in AT and CT terms is negligible for pH. Focusing on the simple Taylor expansion will confuse readers (see my comment just above concerning lines 614-615). Thus Fig. 11 should be replaced with Fig. S19, and only on the freshwater Taylor expansion should be shown. There is no reason to show the simple Taylor expansion if the freshwater Taylor expansion is presented.
Fig. S14: What do the colors mean. There is no information about color codes in the caption nor the legend.
Fig. S16: in the legend, please change "single grid" to "one grid cell".
TABLES
Table 4: delete the 2nd header line that is in the middle of the table
Tables in the Supplement should include an S before the number, but some do not do so
REFERENCES
Taylor, K. E., Stouffer, R. J., & Meehl, G. A. (2012). An overview of CMIP5 and the experiment design. Bulletin of the American Meteorological Society, 93(4), 485-498. |
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