Review of “Firn data compilation reveals the evolution of the firn air content on the Greenland ice sheet” by Vandecrux et al.
This manuscript is the second version of this paper and the previous revision round definitely benefitted the quality of the text. However, there are still too many points that need attention before the manuscript is publish-ready. Given the severity of the comments posted in the first round of reviews by both reviewers, I was surprised by the relatively short response time (<1 month) of the authors. As in the previous version of manuscript, I have again a long list of minor comments. In my view, these typo’s, bad phrasings, and oversights should be spotted during a full correction round of the co-authors, rather than in a review round.
Besides these irritating minor comments, I have one general comment that needs to be addressed before the manuscript can be published. This manuscript describes the spatial pattern of firn air content (FAC) across the Greenland ice sheet based on observed firn cores and is the first manuscript to do so. Previously, only modelled estimates using regional climate models or firn models have been made. In my opinion, the current manuscript tries too much to suggest that the observation-based method used here are superior to previously presented data, for example the following phrases are used: “urge caution when using models to quantify […] evolution of the FAC” (P1, L34), “confirms our choice of an empirical approach as op¬posed to relying on RCMs and firn models” (P10, L8), “none of the RCMs can simultaneously […] FAC accurately, which justifies our empirical approach” (P18, L1), “the mismatch between RCMs and our dataset reminds that RCMs should be used with caution” (P20, L20). I completely disagree with this type of reporting.
First of all, I think science is not a competition of who has the best methods or results, but should be more about increasing understanding of processes involved. For me, the balance in the current manuscript is completely wrong. Second, the method used here uses (relatively simple) empirical relations to calculate a spatial pattern in FAC and subsequent area-integrated numbers. So although the method is based on observations, the eventual resulting numbers cannot be treated as such. A comparison with other data can therefore never “justify” that one method is better than the other. My suggestion would be to treat the observation-based method used here and the modelling method as complementary rather than as competing. Both schools have their definite pro’s and con’s and only by combining them the best result possible can be realized. Neither this manuscript nor any other currently available has the evident proof that for Greenland FAC one method is better than the other.
In my view, large parts of the results interpretation and discussion sections needs to be rewritten to do more justice to the results of both methods. To do so, it is also needed that the authors look critical at their own results. They should definitely highlight the regions or regimes were the observation-based method appears to perform better, but also be fair to report that in some regions/regimes it does not. For example, the lack of observations in the HAWSA is a serious problem or that models appear more capable of simulating temporal trends then sparse (in time) observations.
Minor comments:
P1, L26: Please be consistent with the hyphens throughout the manuscript. Technically, sea-level rise should be hyphenated (so that is correct), however, the phrase without hyphen (sea level rise) is used much more often. In the same line, however, ice-sheet contribution should be hyphenated!
Any time there is a compound adjective (two words (ice & sheet) that act together to describe a noun (contribution)), you should hyphenate: ice-sheet contribution. Only when there is an adverb ending in –ly you should not hyphenate: remotely sensed data and not remotely-sensed data.
P1, L29: The 6500 ± 450 km3 is very different from the 5200 ± 452 km3 reported in the previous version. The numbers are not even close to being “within the error margins”, which makes you wonder how certain the used method, numbers and/or uncertainties are. Reported uncertainty estimates should theoretically indicate the possible range of outcomes based on uncertainties in the input. Such large difference between the two versions indicates that the reported uncertainty number is far too small.
P2, L9: should be “in the sea level change equation”.
P2, L14: This paragraph needs 1-2 sentences more.
P2, L18-19: Due to the density difference between water in liquid and refrozen form this statement is not completely true.
P2, L19-22: Sentence is too long.
P2, L28: By comparing RCM output with density profiles, the model is indirectly compared to FAC. FAC is nothing more than an integrated density profile.
P3, L1-5: Why is the firn aquifer not mentioned here? A firn aquifer region is the prime example of deep percolation (> 15 m).
P3, L22: Here, it is reported that 324+20 cores are used, while the abstract states 360 cores are used
P3, L6-7: “does not play a negligible role” is somewhat double. Change into “does not play a role” or “has a negligible role”.
P4, L15: Why not use accumulation (b) and surface melt? There is clear relation between air temperature (Ta) and surface melt, but it is not linear due to feedback mechanisms such as albedo. Meltwater refreezing is a much more effective densification process than firn compaction, so to me it makes more sense to use surface melt instead of Ta.
In the previous manuscript version, the atmospheric data from Box et al., 2013 was used, making the choice for b and Ta more logic (as surface melt is unavailable, I think). However, in the revised version MAR is used, making surface melt also easily available.
P4, L21: There are not two patterns visible.
P4, L22: “more scatter” is not really a pattern…
P4, L30: Here, -19C is used, while the previous version reports -16C. Is this difference only due to the difference in climatic forcing between Box et al., 2013 and MAR?
P5, L5: Again, I think it would be good to introduce surface melt as a proxy. Did the authors make a FAC vs. melt-accumulation ratio figure? Or investigate if there are clear patterns found in the accumulation-surface melt space?
Table 2: Why are 11 HAWSA cores also used for the DSA fitting?
P7, L4: I do not understand this. How is the temperature dependency in HAWSA and DSA similar? In the HAWSA regime there is surface melt, making the vertical temperature profile inherently different than without melt.
P8, L4-10: This method feels a lot like cherry picking… There are not enough cores, so one from the HAWSA 6 from the firn line are added. How does this influence the results and why are only these 1+6 added and not more or less?
P8, L26: I think Ligtenberg et al., 2018 calculates FAC to the density of ice and not pore-close off depth.
P8, L29: Refer to Figure 4.
P9, P14: Referring to a 2019-paper is somewhat preliminairy.
P9, L23: In Figure 2b, I see a remarkable underestimation in 1995-2000 and a remarkable overestimation in 2000-2005. What explains this?
P9, L24: add e.g.
P9, L25: In light of the major remark (see above), I find it surprising that firn modelling is here used to confirm the found results.
P11, L7: Was it checked how this relationship looks in modeled data: HH, RACMO, MAR? I would suspect it also varies spatially, was this checked?
Also, for FAC10 < 3m the relationship in Figure 4 is lacking confidence. Why is it still fair to be used for lower FAC10 regions?
Figure 6: Can be added to Figure 5 as Figure 5b.
Figure 6: For the cores locations, it is visible that all 98-08 cores, expect one, were situated on the northern transect, while all 10-17 cores, expect one, were located on the southern transect. How robust does that make the reported temporal change (35%) in LAWSA between these periods? Are we not just looking at spatial differences in FAC rather than temporal differences?
P14, L2: That is a very open door, as FAC10 and FACtot are linearly related in the used method…
P14, L7: Here it is stated that the LAWSA FAC10 loss from 98-08 to 10-17 is 24%, while on P12, L14 it is 35%. Please check your numbers carefully!
P14, L8: Please remark that is likely unrealistic (as was also mentioned in P12, L4-9).
P14, L10-16: I do not agree. It is (very) likely that melt is the main contributor, as in %-change in melt has a nth time higher effect on FAC than the same %-change in precipitation. Also, large changes in melt are well documented and observed, while precipitation changes are small or insignificant.
P14, L19: I would replace “Box” by “Box13”
P14, L24: By saying, “Additionally, in these regions no firn observations are available to constrain our FAC10 estimates”, you basically say that this procedure should not be used in these regions. This is something I agree with. When there are sufficient FAC observations, the used method is valuable and definitely adds insight to what we know. However, when at most a handful of observations is available (as in the S and SE, or in the HAWSA as a whole), these regions should be masked from the results.
L15, P5-6: Would help to re-iterate that the infiltration ice density is used to convert km3 in Gt.
P15, L7-10: Sentence is too long.
Table 4: Can be merged into Table 3 as the two are directly linked through the infiltration ice density.
P15, L15-17. The difference between the here reported storage capacity (310 Gt) and the one by Harper et al., 2012 (1289 Gt) is a factor 4. Even with increasing knowledge, more observations, etc. this is a difference that very difficult to fully explain. Could the modeled FAC (HH, RACMO, MAR) indicate which of two might be more likely?
P16, L7: “firn aquifers” or “the firn aquifer”.
P16, L8-10: I do not agree. Firn aquifers contain liquid water that can resides there for ~30 years, which to me is too long to simply neglect it. On the other hand, all refrozen meltwater is included here as it is “retained for centuries” (P16, L10). The latter is definitely not true in the current (fast-)changing climate. This manuscript reports that over the last decade alone the FAC in LAWSA has decreased with 24%. If that rate continues, some of the refrozen meltwater will re-melt and runoff in a summer within the next 30 years. To me, it is therefore not correct to include this refrozen retention while excluding the firn aquifer liquid water.
P17, L7-8: Refer to the correct Table and Figure.
P18, L5: RMSE.
Table 5: Would be interesting to include the bias and RMSE for the empirical method as well, for comparison.
P18, L15: Would be valuable to indicate the uncertainty interval.
P18, L20-23: You refer to biases in the modeled SMB of RACMO and MAR, but biases compared to what? This paragraph is unclear.
P19, L3: By saying “HIRHAM overestimation of FACtot in DSA…”, it is implied as if FACtot is an objective observation that can be used to test other estimates. FACtot is however far from a direct observation.
P19, L12: I would be very hesitant to draw strong conclusions about the performance of RCMs in the HAWSA. The HAWSA FAC numbers reported here are based on only a few observations.
P20, L5: add “by the extreme summers of 2010 and 2012”.
P20, L6: Is this decreasing FAC10 trend in the RCM significant? In Figure 2, it is visible that in the 1990s the highest FAC were reported, so does that not also generate a small decreasing trend in the observational record?
P20, L7-9: Why should it be a flaw in the models? Would be fair to list all possibilities.
P20, L18: This is a very shaky conclusion. Since FACtot and FAC10 are linearly related in this manuscript, these numbers follow logically from one another. However, it is very unlikely that the total FAC has decreased by this much.
P20, L21: As mentioned in my major remark (see above), I do not fully agree with this. Both methods have their pro’s and con’s. The results presented here also show that there are some regions where insufficient FAC observations are available to map all spatial variations in FAC. For these locations, RCMs estimates are very useful. |
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