The authors have responded to all three reviewers’ concerns about a lack of substantial evidence to support the conclusions of the work by walking back some of the discussion and making their conclusions weaker and their language overall less certain. The fact that the evidence does not fit with the (weak) conclusions drawn is still an issue. The edits render the work as not strong enough to draw conclusions in a way that is progressing this field forward. Instead, the work is highly speculative and continues to discuss the data in terms that are not justified by the data presented. Further, more than 50% of the data that was collected is discarded and the impact of this makes the study not representative of the study site (adding further weakness to the comparison of datasets across different years and season to month comparisons, etc.). There are also at least two data comparisons that do not correctly represent data in the literature. The most important arguments in my previous review have not been adequately addressed. This study is not representative and not appropriate for publication. It would serve the literature better as a measurement report since the new data is interesting, but the context presented is not justified.
1. Nitrate in the boundary layer at Summit can represent a small portion of the total budget of nitrate that is deposited as primary nitrate. I previously argued that the nitrate in the snow represents nitrate that is in the cloud and in the air from the cloud to the ground. Cloud base heights at summit are typically between 500 m to 1700 m - well above the suggested 25 m boundary layer height that the authors use to argue that the aerosol collection at the surface is “representative” of a well-mixed boundary layer. The argument by the authors that the boundary layer is representative of the entire column of air plus the cloud that could be scavenged by snowfall is false. The snow itself is representative of more than what the atmospheric samples are collecting - the snow is averaging the d15N-HNO3 from the cloud to the ground; the aerosol+HNO3 collection is only representing the near surface boundary layer air even if it is well-mixed. Thus, the snow values can change different from what is in the air if what is scavenged by the snow contains much more nitrate than that that which is scavenged form the boundary layer alone.
2. Is the collection of HNO3+NO3- representative? The crux of this argument lay in whether HNO3(g) + NO3-(p) are quantitatively collected. The authors argue that a high NaCl blank should lead to complete collections of HNO3(g) and NO3-(p).
-The blank should be reported in the methods and/or results section.
-Where is this blank sourced from? The authors state that the filters were pre-cleaned and stored under clean conditions.
-The authors should also address whether this blank can impact the pre-treatment resin concentration method. In the pre-treatment concentration method, NaCl is used as the eluent to remove the nitrate, so it seems possible that a high NaCl blank could disrupt the concentration of nitrate on the column.
The authors add a comparison to Silvente and Legrand from a previous study and acknowledge that this is a comparison to a different filter (Nylon in the case of the Silvente and Legrand study). They say in the text that they compare well with Silvente and Legrand value of 19.9 +/- 19.1 ng/m3 and this plus the “large NaCl blank” therefore suggest their measurements are representative of total nitrate in the bourndary later. But in the table they report the denuder concentrations of 38 +/- 53 from Silvente and Legrand versus the Nylon filter results suggested related to proof of the methods. What is the difference here and why are not both the denuders and the filters compared here? Further, even without the way too high values of Jarvis et al that are left out, the average for this current study is significantly lower than the other compiled studies in the table. To choose a single study to compare with seems strange amongst the compilation of a range of datasets.
In response to the reviewers the authors stated information about a nitrate blank and that the isotopic composition of the blank was corrected for. This must be included in the main text - the nitrate blank concentration and the isotopic composition and how it is used to correct the data should be stated explicitly in the methods.
The authors explain in their response how the uncertainty associated with the isotopic measurements was calculated. This should be included in the manuscript as well.
3. The authors use words like “systematic”, “out of range” and “significant” without any statistical justification. The authors argue that they cannot complete statistical comparisons in response to my comments. They do however add T-test comparisons based on the other reviewers’ comments. These T-test comparisons for comparing means are not appropriate for this work – the data is not normally distributed. The authors should be able to provide a framework in which to interpret their data and what is significant change and what is not. They did not do this well, according to all three reviewers, and none of the changes improve upon this. The use of words like “systematic” and “significant” and “trends” need a statistical justification.
The authors argue that the difference in the December data - rendering Dec. not part of the clear “systematic” pattern that the authors say exists – may be the result of a dating error. This is not addressed in the manuscript and should be. In the responses, the authors argue again that
“Here we used the word “systematic” to represent the overall patterns of the seasonal atmospheric and snow δ15N(NO3–), as they appear to follow the amounts of accumulated UV-B dose (but oppositely). As in fact only the Dec. value in snowpack appeared to be out of the system. Feb. snow is also expected to be influenced by sunlight as polar sun rises in March when Feb. snow is still in the photic zone.”
The definition of systematic is that it is a methodical change – this is not evidenced in this work, as raised by all three reviewers. There simply is not enough evidence to call this systematic when in fact there are months when those changes are not the same, there are months with no data at all, and there are months with less than 50% data available. Not too that the authors did not respond to how much data is removed from which months in the dataset, which would help readers to understand how representative the dataset actually is. I think it may warrant rejection itself that more than 50% of the data had to be discarded period.
4. The title change is now too general. The title should be more specific to the conclusions drawn in this work and/or what new work is being presented here specifically. The paper does not do a good job of reviewing previous work at Summit, Greenland (and the reviewers respond to my comment on this that it is not necessary to do so). The title suggests that it will include a complete overview of the topic and this is not actually addressed in the work.
5. The conclusions run counter to the authors’ points in the response. In the conclusions (line 822) the authors restate: “This suggests that the degree of preservation for Δ17O and δ18O(NO3–) are likely different from each other at Summit, mainly due to the fact that photo-driven post-depositional processing causes mass-dependent fractionation of isotopes which directly affects δ18O(NO3–) but not Δ17O(NO3–).”
Why does this affect the degree of preservation? This does not make sense. The D17O represents the difference between d18O and d17O – so it necessarily represents something different than d18O alone.
Following the above line, the conclusions then state: “Overall, our analyses suggest that the photo-driven post-depositional processing impacts both δ15N and δ18O(NO3–) at Summit. As a result, the signals of primary nitrate δ15N(NO3–) is unlikely preserved at this site, and Δ17O and δ18O(NO3–) of primary nitrate are also disturbed but to different degrees.”
This is counter to the authors response document. I point out several times where the authors are stating with heavy certainty how much can be explained by post-depositional processing and I argue that they have not proven this with the evidence provided. Even with their model results, they state in their response that:
“Primary nitrate dominates the Summit nitrate budget, but the seasonal loss of nitrate is driven by the seasonal shift of actinic flux which drives snow nitrate photochemistry. As a result, even though the annual net loss of nitrate is small, the seasonal difference, especially the δ15N(NO3–) could be large. The large N-isotope fractionation associated with snow nitrate photolysis can result in large δ15N(NO3–) changes despite small amount of nitrate loss.”
The fact that primary nitrate dominates the budget and varies from season to season in both its concentration and isotopic composition is not the framing that is presented in the manuscript. The manuscript over and over makes post-depositional processing stand out as the major process controlling the isotopic composition, and that the isotopic compositon can only be explained as NOT representative of primary nitrate. The authors cannot state definitively in their response that “Primary nitrate dominates the Summit nitrate budget” and provide a different context within the manuscript.
There are a number of errors in the author’s responses:
6. The authors responses:
“Note here we compare atmospheric nitrate with surface snow nitrate. Owing to the seasonal resolution of the Jarvis et al. (2009) dataset, we only compared the seasonal mean here instead of any specified month. In addition, the surface snow δ15N(NO3–) data is significantly higher in Fibiger et al. (2016) than in Jarvis et al. (2009) which call for more data to resolve this issue….
Here we compare atmospheric nitrate with surface snow nitrate. Similar to the response above, only seasonal average values were compared here. The winter average atmospheric δ15N(NO3–) is (-12.9 ± 4.6) ‰, while that of surface snow is (-11.7 ± 2.3) ‰.”
The authors compare to a value a Jarvis et al (2009) that is not represented correctly or should be clarified. For 2007, Jarvis et al (2009) report a value for surface snow in March ONLY so it is not a seasonal average. For 2006, they report a spring value of -6.7 ± 0.4 (n = 82) for d15N (and for 2007 it is -11.7 on average); the winter average surface snow value is -13.0 ± 3.2 – these are all different than what is stated above. The average value in the manuscript does not match with these nor does it appear to be an average of the two years of Jarvis data? Please clarify – this is critical to the main point of the manuscript as this comparison is used to justify the main conclusions of the work.
7. The authors response:
“Eq(3) is the mathematical representation of the integral effect of photolysis on δ15N(NO3–) in TRANSIST model. The difference is that the J value used here is in a simplified form, i.e., J decreases exponentially with depth.”
The J value does not decrease exponentially with depth. This is pointed out and explained by another reviewer.
8. The authors response:
“The atmospheric δ18O(HNO3) data in Fibiger et al. (2016) is out of range ((54.2 ± 8.5) ‰ in 2010, (90.5 ± 12.5) ‰ in 2010) and thus is not shown here.”
This is not a sound scientific argument. Another reviewer brought this same issue up. There has to be a justified reason to dismiss this data.
9. I don’t understand this response:
Original reviewer comment: Line 471-483: “Compared to surface snow, atmospheric nitrate is more influenced by snow-sourced nitrate…” Yes. This is because the snow represent more than the surface atmosphere at Summit. And while this is stated as “snow is a much larger reservoir of nitrate compared to the atmosphere” on Line 481, the context here is not clear (see general comments above on this).
Original Response: We think we have different meaning regarding this sentence. We meant to explain that owing to fact that atmospheric nitrate is such a small nitrate reservoir that it could be easily impacted by the snow sourced nitrate, while for the surface snow, once deposited, it would not be rapidly altered as the dry deposition of snow sourced nitrate was too low to significantly impact it.
My point in the original comment was tied into the fact that the snow contains more nitrate than that represented in the boundary layer alone, for which they have observations. The authors argument regarding dry deposition here makes no sense?
10. The authors suggest in the response below that stratospheric transport is rather weak in the Arctic region. However, the ozone concentration at Summit, Greenland are consistently high because of the mixing in of upper tropospheric/lower stratospheric air. My purpose here was really to suggest that the authors should better explain the dismissal of high summertime d18O via a statistical measure (e.g., an outlier test across the datasets used for comparison) rather than just assuming that the observation of a higher value that is published in the peer reviewed literature is incorrect.
Original comment - Line 217-220: I agree that it is odd to have a higher summertime d18O. But the validity of the data should be questioned based on evidence that somehow the higher values are biased in some way. For instance, an outlier test could be used. Is it not at all possible that a higher d18O could represent something anomalous that summer at Summit? could there have not been any different chemistry that could contribute to higher values (for instance, stratospheric intrusions)?
Original Response: We agree that statistical methods would provide a more firm comparison here. Unfortunately, we didn’t have the original surface snow data reported by Jarvis et al. (2009). Stratospheric intrusions are unlikely to be reasonable here as it’s known that stratospheric transport is rather weak in Arctic region, such as suggested by Stohl. (2006).
11. From the author’s response document:
“In summary, the Fibiger et al. (2016) cannot provide any evidence that nitrate in the air (or even the surface air) is disconnected with surface snow nitrate. In fact, the Fibiger et al. (2016) stated in their paper “BrO chemistry does not have a significant influence on the formation of local HNO3 at Summit” (because they cannot explain the observed lower atmospheric δ18O(HNO3) with higher BrO concentration). This is exactly what we think their observations can demonstrate. If BrO chemistry is not important for atmospheric nitrate at Summit, it’s not surprise to expect no correlation between BrO concentration and atmospheric Δ17O(NO3-), let along in surface snow.”
I don’t understand the authors rebuttal here. The point of the Fibiger et al study was the conclusions were drawn back on a lack of evidence for influence of BrO. The conclusion was a surprise at the time because Kunasek’s work had specifically suggested that the influence of BrO may explain the higher than predicted D17O values observed at Summit. This difference between expected and observed still exists – even in the Jiang et al model they cannot explain the D17O values at Summit given our current understanding.
12. The authors response:
“As the seasonal patterns should be the same under a same background climate, we would expect that compiled seasonal patterns in snowpack should also represent that in the year of the aerosol sample collected.”
This is not true for the isotopic composition.
13. Other reviewers also noted confusion with this statement, which the authors edited: “This likely suggests the oxygen isotopes are also affected before preservation in the snow at Summit, but the degree of change for δ18O(NO3–) should be larger than that of Δ17O(NO3–) given that photolysis is a mass-dependent process that directly affects δ18O(NO3–) in snow but not Δ17O(NO3–).”.
This is still not an accurate statement as the isotopes are affected by photolysis, but this cancels out because of how D17O is calculated. This should be modified to be explicitly clear.
13. The authors argue that the Shi et al study need not be included in response to my comment because they consider it a laboratory study that was conducted in the field, rather than evidenced in the field. This study should still be cited and the evidence it provides for a small to minimal change in the isotopes should be used to back up the authors claim that this process is not important under the conditions in this study at Summit -- at higher temperatures the fractionation could become important.
Dust concentrations can seasonally be significant too, so the addition of the Rothlisberger citation in response to my comment and mention of glacial periods should be made more general.
14. The authors agree that statistical tests could be included “We think that when the data is overlapped within each other’s uncertainty range, using statistical method such as a T-test could help to discern whether the difference between two groups of data are statistically different. But when the range of data is not overlapped, it’s unnecessary to rely on statistical method to judge whether it is out of range, as in the scenario described in the text”, but do not make any attempt to consider actual statistical measures. I feel that this weakens any statement in the paper where differences are suggested. The error bars on all of the means are pretty large rendering it difficult to ascertain when something is an outlier and when it is not.
15. The authors counter that their model is useful to describe the change due to post-depositional processing, not the values directly themselves. But their model does not describe the change in D17O well and therefore I argue that conclusions drawn based on the modeling of D17O is not appropriate since the model cannot explain the D17O observations. It should be explicit here that the model suggests that the cage effect is negligible and explain why that is that case in the model. I do not feel the model can be used as evidence for a conclusion about the data when it does not explain the data (its absolute values nor its change seasonlly).
16. Original comment from another reviewer: Line 380, are there physical mechanisms that could explain the spring-summer differences such as recrystallization?
Author original Response: We think recrystallization is irrelevant to the discussions here as we are seeking the explanation for why the atmospheric δ15N(NO3–) is most depleted in spring instead of in summer, as the photolytic NOx flux from snow maximizes in summer with very depleted δ15N values. Our hypothesis is that owing to the more unstable boundary layer in summer that favors the export of NOx instead of locally reforming nitrate, or an increase in δ15N of primary nitrate which also contributes to local atmospheric nitrate. So far no known physical mechanisms can explain this detail of the observed seasonality.
The authors do not invoke previous hypotheses in the literature that suggest that primary nitrate changes seasonally to account for some of the values. If anything, this once again shows that the authors want the data to fit a particular conclusion – that the flux of snow-sourced NOx can explain everything, but here it does not explain the data. |
