Second review of "Arctic Sea Ice Loss Amplifies Local Evaporation Influence on Water Vapor Isotopes: Insights from Cruise Observations" by Zhang et al, submitted to ACP
This is my second review of this manuscript. In the revision, the authors have improved the manuscript in several points, in particular regarding clarifying some aspects of the methods. Otherwise few more substantial changes have been made. Clarifying the methods has revealed more clearly some of the deficiencies of the approach. I recommend more substantial revisions of the presentation and interpretation of the results.
Major comments
1. Uncertainty of moisture source appointment: In the abstract and conclusions, numbers from the source appointment of 18.6 % and 48.3 % are given without uncertainties. However, the uncertainties in obtaining these numbers are manyfold, and need more quantification. How sensitive is this result to the choice of the high-latitude and mid-latitude end member? How sensitive is the 95 % range to choices of the Bayesian mixing model? A systematic uncertainty analysis is needed, also to justify that the Bayesian model is a sensible choice over a simple linear mixing model.
2. The authors have used the global closure equation of Merlivat and Jouzel (1979) in calculating the surface vapour, which is only valid if precipitation balances evaporation (Jouzel and Koster, 1996). The authors acknowledge that their results are biased due to this choice, but instead the evaporation flux should be calculated using a more complete model which takes mixing with local vapour into account (Craig and Gordon, 1965). This is important because the Bayesian source appointment will be affected by this choice.
3. The precision of the isotope species is given with a number of digits that is not possible to achieve with available analytical methods. δ18O is commonly given with 2 decimals, and δD with 1 decimal in liquid analysis, but the total uncertainty has not been quantified here.
4. The δD data are never shown. It would be useful to show a short time segment where both δD and δ18O are seen at high time resolution for a period where strong variations are present to ascertain that the two main isotope co-vary on the same time scales and are not affected differently by inlet memory effects in the unheated inlet.
5. Some more details of the methodology are missing: what was the flow rate in the inlet, what was the uncertainty of secondary standards, what tubing material was used, what brand/type of filter was used, at what delta value was correction determined?
6. Some of the findings remain overstated or do not seem to follow as the only possible conclusion (see detailed comments), these should be modified. The significance of the uniqueness and novelty are also overstated. There have been extensive cruises with isotope measurements in the Arctic before, including R/V Polarstern (Bonne et al., 2019), but also during the MOSAiC drift (Brunello et al., 2023, 2024). In these papers, the interpretations put forward here in terms of sea ice influencing the vapour already exist in the literature. This manuscript confirms previous findings with a new dataset.
7. I find the interpretation of the data in terms of sea ice categories questionable. The data does not separate well according to the 3 categories of ice free, transitional, ice covered. In particular the transitional category looks just like the sea ice category. Instead, it seems that air temperature or SST would be the more stringent separator, that divides the data into two categories (Fig. 4). And since SST is available, RH(SST), which is indeed most influential for the kinetic fractionation during evaporation, can be calculated from the dataset. It would be interesting to see if RH(SST) stratifies the data, such as SST itself does. A critical rethinking and discussion of the categories that are now used for analysing the data is recommended.
8. In the writing, a 'framework' is used that deals with the opposing pairs 'Rayleigh fractionation' and 'kinetic fractionation'. I am not convinced that this dichotomy is really matching to the processes at hand. Rayleigh models are an entire family of models, that describe isotope fractionation with or without removal of condensate during a continuous cooling process. Depending on how the removal is simulated, there could be super-saturation and thus kinetic fractionation in a Rayleigh model. Is not the main difference between (super)saturation/condensation and sub-saturation/evaporation? Maybe the authors wanted to emphasise that there is predominantly equilibrium fractionation in the long-range transport? In any case it should be justified better that the chosen antipoles are indeed meaningful opposites.
9. The description of the choices of the Bayesian model is now much more detailed, which is good. However, the choices are not justified, or supported by references. The impact of these choices on the source appointment remains unclear, and the workings of the method itself is still opaque. Some sentences explaining the working concept would be useful here.
10. The "inverse temperature effect" is proposed as a terminology. I think it is not beneficial to add another term to the set of established terms describing precipitation isotopes, also since this study deals with water vapour and not with precipitation. It becomes more confusing to a reader, also since the proposed term is the negation of another "effect".
11. The cruise period needs to be specified in the methods section and in the abstract. This is essential information missing from the manuscript. A short description of the cruise with harbour times should also be included.
12. Please make the dataset available to the reviewers before manuscript publication.
Detailed comments:
L. 43: I don't think this is an accurate representation of Klein et al (2015). They observed a short spike in water vapour isotopes over land which they interpreted in terms of a cyclone signal. You might rephrase as "In contrast, Klein et al., (2015) proposed that local evaporation..."
L. 54: "diverse" -> "contrasting" or "different"
L. 55: "unique": This data set is not unique, given previous Arctic cruises where similar observations were made and are described in publications (Bonne et al., 2019; Brunello et al., 2023, 2024). Maybe rephase as "new".
L. 74: The time interval for which this measurement precision is valid needs to be specified. How was this determined?
L. 75: It is recommended to publish the dataset with 1 min resolution. The analyzer should have sampled at even higher frequency of 1 Hz or so. Was the d-excess calculated from the hourly data, or from the 1 min data?
L. 81: What were the delta values of the standards, was it actual VSMOW?
L. 90: Uncertainties of the calibration standards need to be provided. Check number of digits and justifiable precision.
L. 97: Is the weather station data included with the isotope dataset? At which height was the weather station acquiring data?
L. 107: The ice-free category may include extensive regions with drift ice. This should be considered in the interpretation/discussion of the results.
L. 118: The assumption of δD = δ18O = 0 permil for arctic ocean sea water may be violated frequently, for example in regions influenced by Siberian river outflow, or where brine rejection/sea ice melt take place. What uncertainty is added by this assumption?
L. 129: Were all levels used in the subsequent analysis? How much difference is there actually between the different elevations? If the trajectories are calculated using pressure level output from GDAS, there are not enough constraints in the boundary data to justify 10, 20, 30, 40 and 50 m trajectories to contain independent or additional information.
L. 141: What is N?
L. 145: What does Rhat stand for in this context?
L. 159-161: Make consistent with measurement precision
L. 178: "The results suggest...": This strong statement is not justified given Fig. 2. There is some degree of non-overlap, but predominantly the PDFs overlap. Adjust the statement to reflect what is seen in the figure.
L. 185: "This distinct d-excess pattern...": I don't see how this statement can be derived from Fig. 2b. The PDFs overlap strongly, except for a separate peak for the transition region. Adjust the statement to reflect what is seen in the figure.
L. 193: "Highlighting the growing role of...": The statement suggests some linear relation between SIC and kinetic fractionation, but what the figure shows is that there is a more binary distinction between the part of the cruise around 29. August and the rest of the cruise. It would be useful to show the δD as well for maybe a limited period in the Appendix. The co-variation between δ18O and d-excess is quite strong, which possibly suggests a surprisingly flat δD. Showing the δD would clarify that aspect.
L. 210: "Above this threshold, δ18O ...": Rephrase "equilibrium-driven fractionation" as "equilibrium fractionation". It would be useful to clarify that you talk about a water vapour mixture here with different contributions, one of them being local evaporation under sub-saturated conditions.
L. 213: Please provide the p-level or avoid using "significant"
L. 216: not clear what exactly is meant by "dominant fractionation regime"
L. 220: "Collectively, these patterns indicate...": Again, this indicates a gradual transition, which is not shown by the data. The pattern is quite clearly bi-modal according to Fig. 4. The claimed control by the sea ice extent is not convincing.
L. 222: "further modulates": This statement is confusing and probably wrong. RH quantifies the deficit above the surface, but does not control it. Sub-saturation leads to ("controls") the degree of kinetic fractionation during evaporation. RH(SST) more exactly quantifies the sub-saturation during evaporation, and is negatively correlated to d-excess in the evaporation flux. Rephrase for clarity.
L. 264: "Rayleigh equilibrium pattern": Unclear what this means, rephrase. The proposed antipoles "Rayleigh distillation" and "local kinetic fractionation" might be better framed as long-range transport and condensation and local evaporation.
L. 281: "organized Rayleigh behaviour": unclear what is meant by this
L. 285: Again, some degree of influence is proposed that is not backed up by the mostly bi-modal variation seen in the dataset, stemming from differences in the ice free Barents Sea and elsewhere during the cruise.
L. 291: "directly implicates": This confirms previous findings and the theoretical understanding of isotope fractionation.
L. 293-298: "distinct processes that shift with the state of sea ice", "sea ice ... shapes the balance": These formulations imply a control of sea ice that is not backed up by the data. No convincing evidence is provided for a gradual influence of sea ice state. Rephrase to be in line with the presented evidence, or clearly identify these statements as speculative and move to the discussion section.
L. 300: Unclear what is meant by "anomalous isotopic behaviour", rephrase
L. 313: The deficiencies of MJ79 are known and the model is not valid for local evaporation calculations.
L. 330: Why sublimation?
L. 348-354: Make consistent with actual measurement precision.
L. 363: Without a sensitivity analysis, these numbers can hardly be seen as robust. The error bars overlap for all but the last category. A systematic sensitivity analysis is needed, taking the different assumptions of end member delta values into account.
L. 371: "resolves a longstanding Arctic paradox": This is clearly an overstatement of the presented results. I think the measurements and interpretation are useful, but not novel to the extent that this statement is justified given other published work in the region.
L. 373: What is meant by "boundary-layer thermodynamics"? Maybe "surface fluxes" or "surface evaporation" would fit better here?
L. 375: Samuels-Crow et al. 2014 did not make measurements in the Arctic, please remove citation. The sentence lumps together precipitation and vapour measurements, which skews the comparison. Peng et al (2019) reports measurements from Antarctica which seems out of context here.
L. 376: "These apparently conflicting results...ice-controlled humidity": This sentence again implies a continuity/control of sea ice that is not made evident in the data.
L. 386: Rephrase this taking into account that your dataset is also limited in terms of time and extent: "During the cruise period/for our dataset, we find that..."
L. 400: "Nevertheless ... remain robust": Near surface temperature can be much colder than SST in near the ice edge on short time scales. Unless the authors have investigated this, the claim remains without evidence.
L. 403: The definition of an "anti-temperature effect" does not seem to add value, but seems rather confusing.
L. 410: "spatial fractionation over the heterogeneous ice surface": Unclear what is meant with this statement.
L. 412: Warm-air intrusions may be more of a spring phenomenon. How much of a limitation is it for your study/interpretation that it only covers the summer season?
L. 430: "intrinsically tied to sea-ice state": The evidence provided here is not sufficient/consistent with this claim. Rephrase as speculation, and propose what is needed to more firmly make this claim.
L. 433: "These results provide the first in-situ isotopic observational constraints for evaluating ...": This sentence is a clear overstatement of the results from this manuscript, and not in line with the fact that there are other publications and datasets available that presented similar results. The sentence should be removed.
L. 441: "We advocate a regime-informed dual-proxy framework": Unclear what is meant by that, simplify/clarify sentence.
L. 445-451: This paragraph would benefit from some moderation of the impacts of this study, given all limitation indicated so far.
L. 452: "systematically regulated by sea ice regime": This claim is unfounded. What the presented evidence shows, is that there is a bimodality in the measurements in clearly ice-free and ice influenced regions.
L. 459: "These results establish": Again, this claim is not backed up by the results. |
Review of “Arctic sea ice loss amplifies local evaporation influence on water vapor isotopes: Insights from cruise observations” by Zhang et al., submitted to EGUsphere
The study by Zhang et al 2025 reports ship-based measurements of water stable vapour isotopes from an extensive cruise on the Chinese research vessel Xuelong 2, spanning across the arctic seas, from northern Norway to the Bering Strait. Combined with meteorological data, the authors use a Bayesian mixing model and Lagrangian trajectory analysis to quantify contributions of local (from the Arctic ice-free region) and remote (from lower latitudes) moisture sources in this area. The main conclusion of this manuscript is that sea ice change is a key modulator or Arctic water vapour isotopic variations. The presented dataset is a valuable and forms an important set of observations in an in general under sampled region. However, there are some aspects of this paper concerning the methods, presentation, and interpretation of results that should be addressed before publication in ACP.
Major comments
Minor comments:
Detailed comments:
Line 12: ‘ice-phase processes’. You mean ‘in cloud ice phase processes’?
Line 21: Change ‘These parameters’ to ‘these isotopes fractionate’
Line 31: Add reference to these studies after the words ‘ice-free ocean’
Line 35: Which sources are meant here, local or lower latitude sources?
Line 42: This is not consistent with Thurnherr and Aemisegger (2022) who observed negative d-excess in extra-tropics.
Line 130: What sources were used as input.
Line 130 (paragraph 2.5): But this uses water stable isotopes as passive tracers? Why not use ensemble trajectory analysis HYSPLIT as tracer option rather than statistical mixing method?
Line 133: ‘Figure 1 shows the’, this comes a bit unexpected and is posed as a conclusion while the ‘co-variation’ has not been introduced to the reader and is also not clear from this figure. Rather reword to something like: Figure 1 suggests/shows a that there may be a co-variation…..
Line 179: no more so on relative humidity refer to Pfahl and Sodeman (2014)
Line 204: The word ‘trajectory’ is confusing in this context, you mean ‘curve’?
Line 231: you mean d-excesss in surrounding vapour
Line 236: supersaturation was only mentioned in relation to cloud processes?
Line 278: supersaturation is not a process but a condition? You mean crystal formation under supersaturated conditions?
Line 281: It is usually the opposite, air masses from the south are warm and moist in general, please explain.
Line 301: (single) 10m trajectory arrival does not necessarily represent the moisture source.
References
Brunello, C.F., Gebhardt, F., Rinke, A., Dütsch, M., Bucci, S., Meyer, H., et al. (2024). Moisture transformation in warm air intrusions into the Arctic: Process attribution with stable water isotopes. Geophysical Research Letters, 51, e2024GL111013. https://doi.org/10.1029/2024GL111013
Thurnherr, I., & Aemisegger, F. (2022). Disentangling the impact of air–sea interaction and boundary layer cloud formation on stable water isotope signals in the warm sector of a Southern Ocean cyclone. Atmospheric Chemistry and Physics, 22(15), 10353-10373.
Sodemann, H., Weng, Y., Touzeau, A., Jeansson, E., Thurnherr, I., Barrell, C., et al. (2024). The cumulative effect of wintertime weather systems on the ocean mixed-layer stable isotope composition in the Iceland and Greenland Seas. Journal of Geophysical Research: Atmospheres, 129, e2024JD041138. https://doi.org/10.1029/2024JD041138.
Thurnherr, I., Kozachek, A., Graf, P., Weng, Y., Bolshiyanov, D., Landwehr, S., Pfahl, S., Schmale, J., Sodemann, H., Steen-Larsen, H. C., Toffoli, A., Wernli, H., and Aemisegger, F., 2020: Meridional and vertical variations of the water vapour isotopic composition in the marine boundary layer over the Atlantic and Southern Ocean, Atmos. Chem. Phys., 20 (9), 5811–5835.
Thurnherr, I., Hartmuth, K., Jansing, L., Gehring, J., Boettcher, M., Gorodetskaya, I., Werner, M., Wernli, H., and Aemisegger, F.: The role of air–sea fluxes for the water vapour isotope signals in the cold and warm sectors of extratropical cyclones over the Southern Ocean, Weather Clim. Dynam., 2, 331–357, https://doi.org/10.5194/wcd-2-331-2021, 2021