Both reviewers seemed to agree that there was a need for major revisions. In a sense, the authors treat the response to the reviews as if they are answering single, simple questions, and not as if the issues raised are questions that will also come up for a wide number of readers. The changes to the manuscript are fairly minimal. A number of the responses to the reviewers are much more thorough than what appears in the text, and a few changes suggested in the response do not actually occur in the manuscript. There are also a number of sloppy mistakes in the newly added text.
One of the main issues, raised by both reviewers, was what we are learning from this modeling exercise. Some of the language changes in the revised text hit on this importantly – for instance, the clear passage now about this being an idealized ice sheet that resembles Antarctica rather than necessarily trying to fit Antarctica exactly. However, because so much of the text throughout and especially the figures relies on comparison with observations, it is really important for the authors to better refine their manuscript to either a) treat this as an idealized case where they are testing some fundamental understanding, or b) treat this as attempting to simulate reality and in that case inform their/our understanding based upon model-observation comparison. I would argue that they cannot have it both ways. My first read of the manuscript was that the authors were taking approach b) and as such I raised concerns about better validating the model. This was raised over specific issues such as accumulation rate and boundary layer height, the latter of which the authors make a good argument as to why this is not easy to addess. I also suggested focusing a model-obs comparison in the few places where validation can be performed (e.g., Dome C, South Pole, WAIS, Neumayer), and then the scaling up of the model to the whole Antarctic ice sheet is grounded in that the model performs well and therefore simulating the larger scale patterns that are not yet captured by observations is informative. The authors took the approach of removing comparison with observations in the discussion of the robustness of the model (it is “idealized”), but keep comparison with observations as an important point in discussing certain results (it matches the broad scale patterns therefore its right). So in the end, we are left with a mismatch between the approach and how the discussion and conclusions actually come together.
I still find myself, at the end of the manuscript, not sure we have learned something new in this study. There are many knobs to turn, and while I am supportive of the approach of developing sensitivity studies as a way to better assess what should be important in reality, the way the manuscript approaches the comparison with observations has me consistently fact checking the work and finding important differences between the model and reality such that I question whether the conclusions are at all important. Again, I think an important change in approach and therefore language throughout the text is warranted to better address whether this is an idealized approach such that we aim to understand the sensitivity of the system based on changes in the model, or whether the goal is to interpret the model based upon comparison with observations. For example, the model is used to quantify the potential impact on boundary layer chemistry, but the boundary layer chemistry is incomplete (not everything that can be affected by photochemistry in the snow is included), the model is not compared with gas phase or particulate phase concentrations where data does exist, and therefore how realistic is to consider the boundary layer changes. The authors argue in the response that they are simply performing simulations with and without the added nitrate photochemistry to evaluate the potential impact of gas phase chemistry. But again, the suite of figures comparing with snow observations then leaves a lacking hole of no comparison with boundary layer observations except we should just accept the conclusions that this is highly important for ozone and OH concentrations (for example). Does the inclusion of nitrate photochemistry improve the model when compared to boundary layer observations? If this does not matter, than throughout the whole manuscript the approach of an idealized model to test our understanding in general needs to be better framed and needs to be consistent with this approach (or vice versa).
The Erbland et al., 2015 study was still in review when this manuscript was submitted. But it has been published now in the peer-reviewed literature and as such, should be more thoroughly discussed in the Introduction since it is the only other model to attempt to match isotopic observations and it takes a very different approach than that herein. (For instance, it is definitely important that the 3-D model allows for transport based upon real meteorology since that is such a key factor to the redistribution of recycled nitrate.)
Some attempt needs to be made to quantify the influence of accumulation rate. As pointed out by the authors, the model results represent a range of accumulation rates (which may or may not appear at the right rates in the right places along with the right concentrations of nitrate and BC). A more complete discussion in the text about the range of values predicted, rather than relying on careful inspection of the many figures would be helpful. As suggested by the authors in the response, but not well detailed in the text in sum, is that the influence of accumulation rate is because it influences photic zone depth, nitrate concentration and partitioning (wet v dry), and the concentration of impurities (or what’s actually important is more scattering by the snow and less absorption by the impurities). This is an important point - most of the other literature that suggests that accumulation rate is an important factor in determining nitrate preservation seems to make the assumption that this is because of the photic zone depth alone.
Specific comments:
(Line numbers throughout refer to the revised, not tracked changes version]
This is not comprehensive, and includes minor suggestions and a few more important issues:
Double check all mentions in text, figures and tables of Chu and Anastasio values – they seem to vary throughout the text.
Table 1 still includes the dependence of NRF on time that has now been changed/removed.
Lines 54-58: Please be clear in these sentences (see CAPS) – the lifetime of NOx against oxidation to nitrate is EXPECTED TO BE 1-3 days [Levy et al., 1999]. NO3- is lost from the atmosphere through…and has A GLOBAL atmospheric lifetime of roughly 5 days [Xu and Penner, 2012]. This may seem like nitpicking, but these are important distinctions. Logan, Levy et al., and Xu and Penner are all different modeling studies and could easily disagree with GEOS-Chem’s calculated lifetimes (if they were calculated!), especially in the polar regions.
Line 87: “is” in this sentence should be removed
Line 114: change “are” to “can be” since NO2 and NO are only efficiently transported under certain conditions
Line 119: change “is” to “can be”…recent work by Savarino (in review, ACPD) suggests that dominant OH chemistry in summer does not fit with isotope results in Antarctica and this is also suggested in Greenland (Fibiger et al., GRL, 2014).
Line 141: This is a rapidly changing field at the moment – update the reference here since a number of new observations of fossil fuel combustion sourced d15N-NOx disagree with the Geng et al., 2014a assumptions. Perhaps use W. Walters et al., Environmental Science & Technology, 2015.
Lines 143-149: I’ve raised this before – why mention D17O here since this is not the subject of the paper? On the hand, since much of the work that is referenced in this paper include d18O and/or D17O it makes more sense to mention the complete oxygen isotopic composition (d18O AND D17O), rather than D17O alone?
Line 154: The epsilon value here should be listed as “e.g.” or “for example” since a larger range is reported in the literature.
Line 275-276: If it is in the gas phase, it is not in the LLR…rephrase this just to focus on the assumption that all NOx formed in E7 is released into the boundary layer.
Line 341: Can you report the actual range of depth resolution, in other words “The median value of sub-surface snow NO3- concentrations from the ITASE campaign is 60 ng g-1 over depths ranging from X cm below the surface to Y cm, across Antarctica. It is frustrating that generally, when it comes to data, the text is not specific.
Lines 365-366: The addition of “designed to take nitrate recombination into account…” makes no sense as it has no context here. This is a good example of what I refer to above in my general comments. This text was added to deal with issues raised in review regarding that recombination within the snow may take place, and several references were given based on both laboratory and field studies. But the addition of that text is inconsistent with the rest of the paragraph, since the rest of the paragraph is written to justify the treatment of wet deposition as capturing nitrate inside the snow grain, while dry deposition positions it at the surface. It seems that the assumptions made are based on making only a portion of the nitrate photoavailable, not in order to take into account recombination. Further, there is no context in this section about recombination – this term is only used once before, in the Introduction. In the response, the authors argue that the “cage effect” or “buried NO3-“ effect will have an influence on oxygen isotopes but not nitrogen isotopes. Is there evidence for this? The fraction of nitrate that remains in the snow will isotopically reflect that which was lost from the snowpack; it is an assumption that the recombination reaction(s) have no isotope effect associated with them. In the current modeling framework there are two separate pools of nitrate – one that is photolyzed and one that is not touched. The untouched portion does not take recombination into account – this would require some portion of loss and some portion of recombination and the isotopes would therefore change (for d15N, d18O and D17O).
Line 444-445: move (f) to follow the word “fraction”
Line 553-554: Why not use the actual mean of observations from Shi et al.? Erbland et al. 2013 do not have observations below the photic zone in most cases (or only a single observation) and therefore they predict the values at depth. A primary finding of Shi et al. 2014 is that the asymptotic relationship does NOT well describe the actual observations at depth.
Line 694-695: remove “be” after “are not” (same typo occurs in conclusion L794-795).
Lines 781-786: The double use of “however “here is confusing. Please rephrase both sentences.
Line 800-801: This does not match with figure 7.
The number of times nitrate is recycled (Fig 7) and the quantification of the fraction of nitrate lost and gained across the continent when including photochemistry and transport are, to me, important aspects of this work. Figure 9b would be much more useful if it were broken into two figures so the colorbars could better display differences across the continent – otherwise the figure could simply be described in words. I would still argue that a number of figures could be described in the text and included in a supplemental (like Figure 6 - the important point here would be a range of change when the fluxes are set to 0 in EAIS vs WAIS, but the figures are not that compelling). |
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