Statistical Characterization of the Observed Cold Wake Induced by North Atlantic Hurricanes
Round 1
Reviewer 1 Report
This is a very interesting and well-written article which investigates the characteristics (magnitude, spatial structure and temporal evolution) of the cold wake left by North Atlantic hurricanes, in relation to the intensity and the translation speed of the hurricanes, as well as to the characteristics of the upper ocean stratification (barrier layer thickness and potential energy). Infrared and merged infrared and microwave remote sensed sea surface temperatures were utilized together with hurricane observations from the IBTrACS dataset. The use of English is very good, the methodology is described very clearly and the figures are of very good quality. The conclusions are supported by the results and the abstract is concise.
It is suggested to accept this article for publication in Remote Sensing journal after minor revision.
Minor corrections:
1) The authors investigate the characteristics of the cold wake left by North Atlantic hurricanes and not simply by tropical cyclones (which is a more generic term). The definition of a hurricane used by the NHC is of a storm with an 1-minute maximum sustained wind speed of at least 64 knots (e.g. https://www.nhc.noaa.gov/aboutgloss.shtml#h), i.e. 32.9 m/s. In line with [35], an 1-minute sustained wind speed of 32.9 m/s corresponds to a 10-minute sustained wind speed of 28.95 m/s (=0.88 x 32.9 m/s), i.e. 104.2 km/hr. Moreover, the Saffir-Simpson scale which is employed in the article (e.g. lines 156-157, Figure 2 etc.) categorizes the tropical cyclones that reach at least hurricane strength. Therefore: A) I strongly propose to substitute the term “tropical cyclone” with the term “hurricane” throughout the paper, including its title. B) In line 155 the threshold wind speed of 28.5 m/s must be corrected to 28.95 m/s. Does it affect the statistics of this article (e.g. see the 3rd minor comment below)?
2) line 71: it is suggested to include what AXBT stands for.
3) line 164: a quick analysis of the tropical cyclone reports of the National Hurricane Center for the North Atlantic basin (https://www.nhc.noaa.gov/data/tcr/) results to a total of 123 hurricanes (including the major hurricanes) from 2002 to 2018 (included). Could you identify and explain the small discrepancy with your total of 126 hurricanes?
4) Line 219: Why was a radius of 100 km chosen? what is the sensitivity of the probability density functions of the minimum SSTA to the choice of the averaging radius?
5) line 249: “… using 2nd order centered differences …”. Is it correct?
6) caption of Table 1, 3rd line: please justify the choice of a radius of 200 km.
7) line 371: the information that the merged SSTs are used in the Figures 7-10 and Tables 2-4 must be included in their captions, in order to be self-explanatory.
8) line 385: 5.7 instead of 6.7 m/s
9) line 411: “… (Figure 7 C2-D2) …”
10) line 419: “… translation speed increases …”
11) Table 2: why is N equal to 1620 observations at each parameter (Wmax, St, BLT and BLPE), and not 1870 as it is mentioned in line 163?
12) line 429: “… combinations of two properties with the …”
13) line 433: “… Figure 8b, 9 top row and Table 3) …”
14) lines 436-440: it is not clear how these results were derived, since there are no results that present the ΔSSTA for different combinations of BLT (cases C) and BLPE (cases D).
15) line 480: According to Figure 10 (upper-right panel) this line must become “… day (B3 and B2, respectively). …”
16) line 548: “higher air temperature”: do you mean higher boundary layer temperature or θe, which will increase the instability? Please clarify it in the manuscript.
Author Response
Dear Referee, please see our response to your comments/concerns/suggestions in pages 3-7 of the attached PDF. Note that a tracked version of the manuscript is available after page 21. Also note that the main changes are summarized in pages 1-2.
Author Response File: 
Author Response.pdf
Reviewer 2 Report
The draft is very well written, with a good structure and nice figures. The authors lead the reader very well to the subject, outlines well the background and the merit of the paper and finally give very interesting results.
I don't miss any information and I haven't found anything to ameliorate. In my opinion the draft can be published as it is. Congratulations.
Author Response
Dear Referee, please see our response to your comments/concerns/suggestions in page 8 of the attached PDF. Note that a tracked version of the manuscript is available after page 21. Also note that the main changes are summarized in pages 1-2.
Author Response File: Author Response.pdf
Reviewer 3 Report
The manuscript by Haakman et al. presents an analysis of the characteristics of hurricane cold wakes based primarily on a long record of a blended multi-sensor (microwave and infrared) satellite-derived SST product along with other ancillary data. While many of the observations were at least hypothesized previously and much of the work largely reproduces or builds upon previous studies, the length of the study and systematic break down of the results makes the paper a potentially valuable contribution to the literature. The paper is generally well presented and referenced. I just have several comments and points that I feel need to be at least acknowledged and addressed before the manuscript is fully suitable for publication. My recommendation is for publication following minor revision.
The primary, more significant, themes I’ll address first include: better demonstrated understanding of the underlying SST products, further discussion of the assumptions regarding the ocean stratification products, potential interrelationship of the dependencies, and the role of heat content.
First, the manuscript, as presently written, does not fully convey an understanding of the underlying satellite-derived SST products and their uncertainties and alternatives. With respect to section 2.2.1, it is important to clarify that there are, in fact, many “GHRSST” Level 4 datasets combining multiple different products using different methods. The product selected is just one of those conforming to the GHRSST specifications. The name may be consistent with the product name at the PODAAC, but it is not informative by community standards. The product is based on earlier versions of the widely used Reynolds daily SST analysis and improved means for citing are included at the PODAAC link included on line 202. Additionally, improved full peer-reviewed publications are available for citing on line 97 in place of the current [31] reference to a conference paper.
Additionally, it should be acknowledged that there are multiple current blended infrared-microwave SST analyses (also available through GHRSST) – the presentation could potentially lead one to assume greater uniqueness than is actually true. A key potential advantage of the selected dataset is its long time extent – some of the more recent improved products might not go back that far in time. Each of the blended products have their own inherent uncertainties that could impact the results and stated uncertainties presented in the paper. While the uncertainties of the multiple products have, admittedly, not been compared as systematically and extensively as one might like, it is important to note that these exist. A disadvantage of the “merged” product selected is that it has recently been observed to be one of the “noisier” products in terms of its blending of different products and OI methodology. Other infrared-microwave products provide a smoother, likely more realistic, spatial structure on smaller scales. This may or may not have an impact on the results, but when speaking of localized patterns in the cooling, differences in product reliability should at least be acknowledged. As another specific comment, the use of “without missing data” on line 200 is misleading. The OI output has no missing data but neither does the Reynolds OI product either, typically. The microwave data, while providing observations through non-precipitating clouds, does not return retrievals in the presence of more significant precipitation.
Elaborating further on uncertainties, I personally could benefit from a more enhanced discussion on how the presented uncertainties were calculated. The discussion starting on line 257 appears to just refer to the compositing. How do initial underlying product uncertainties also factor in? In talking about spatial uncertainties, is there any consideration of the relative difference in resolution of underlying microwave retrievals (> 25 km) and the grid resolution of the analysis (9 km). The OI process also introduces uncertainties.
Turning to the ocean stratification data, could the authors say a bit more about the expected validity of the assumption that monthly values are sufficiently representative? I appreciate the potential need to make the assumption, but is there further evidence to support it? Is the product equally reliable over the entire extent of the study? I would assume that the product might be better in recent times with the increased availability of Argo data. How does the input data density vary? Could there be any potential impact of precipitation? While there is strong coincident mixing, could precipitation out in front of hurricane passage have an impact on density values? Would the results have changed if the 2018 period was just excluded instead of drawing median values from previous times?
Is there any potential relationship between the time of minimum DSSTA and the various other parameters considered. Given that this time could vary relative to the passage of the storm over -1 to +4 days, did the time extracted show any correlation to the other parameters? In particular, does this factor at all into the temporal evolution in Section 5? When first considering Table 2, I immediately questioned to what extent the parameters might have co-dependencies. This is largely accounted for later in Table 3 and subsequent discussion, but the time is not really discussed.
One term I do not recall seeing mentioned at all in the manuscript is heat content. To what extent could this be a parameter of interest, or be related to the other parameters considered? Considering the opening paragraph, while I have not closely followed the literature, I am aware of ongoing discussion regarding the relative impacts of SST and heat content on TC evolution. While I am not necessarily advocating for additional analyses, I think at least some mention of heat content and its relationship to the other parameters could be worthwhile.
Additional specific comments:
Line 71: Is it worth noting that normal GPS dropwindsondes do not include a direct measurement of SST? Some recent sondes have added an IR sensor but these measurements still have notable uncertainties.
Line 99, “limited performance”: I think the discussion could be a bit more explicit here. If there are clouds present, an infrared sensor cannot retrieve a valid SST value. Degraded performance might only be applicable in regions of partial cloud cover. For regions of hurricane wakes, IR observations are only available after the clouds have passed.
Line 123: I would argue against the use of “only” here since the products do also blend in situ data.
Line 150: Is the word “relevant” needed here? Relevant here, at least to me, could imply that there are some other (unspecified) criteria for selection of the storms. If just the development location, I would remove. If there are other criteria, I would recommend explicitly describing these.
Lines 150-1: For the sake of added clarity, would it be worth explicitly stating whether storms developing within the Gulf of Mexico and/or Caribbean Sea were also included?
Line 184: Again, I would argue against the use of “only” as presently used – the only remotely sensed data yes, but not the only data.
Line 212-3: “were removed” -> were first removed. I think it is worth establishing right up front that this is just a first step and that the steps in 2.2.4 are really needed to get to the “TC-induced” stage.
Lines 236-8: Since circles of 100 km have been discussed as well as 500 km, please clarify explicitly how “present in the previous 10 days” was determined.
Lines 302-3: I was not entirely clear by what was meant by “validated through an individualized check of every profile.” Are these the input profiles to the product? In the case of surface drifters there would not have been profiles.
Lines 331-2: As above, “poor ability to capture the SST under cloudy environments” may be a bit vague or an understatement. I’d suggest being more explicit about the limitations.
Lines 337-9: While certainly true in concept that inclusion of microwave data is better, one should really also factor in the uncertainty of the input microwave data and the quality of the merging procedures. Another argument to be a bit more explicit about the potential role of uncertainties in the input products. The microwave data could still be subject to uncertainties related to precipitation.
Figure 5 caption: Here and later (line 412) I would argue against the use of “zonal” given that there has been a rotation of the data and zonal to me implies something geographic. Something like parallel or perpendicular to the motion might be more appropriate.
Line 361: I might be cautious with the use of “overestimation” here since there is no absolute truth. The implicit interpretation here would be that the blended product is truth. I agree that the IR product would underestimate the magnitude due to the inability to retrieve in clouds, but the truth on the width is a bit less “cut and dried” given the resolution of the data and uncertainties in the accuracy of the merging techniques on localized scales. In any event, it is worth noting throughout the manuscript that there is no absolute truth available and that over- and underestimation are relative to another product (assumed closer to the truth).
Line 362 and vicinity: I think it is also worth stating “width as estimated”. The results here are for a width based on decay scale, but a width estimated by some absolute decrease from pre-TC values could potentially yield different results. I could see some cases where an alternate absolute measure might be equally or more useful.
Line 476: Is this truly “days after passage” or days after the minimum as discussed before?
Line 494: “what is expected” -> “which is expected”?
Line 507: “exists any connection” -> any connection exists
Line 607: I don’t necessarily follow the “explained by their use of infrared data”. I can see that IR data could underestimate the absolute magnitude of the decrease, but a shorter return to original values might not obviously be expected. The point at which the wake is detected could be delayed, but a recovery time from the actual TC passage could still be similar. Please clarify what is meant here.
Author Response
Dear Referee, please see our response to your comments/concerns/suggestions in pages 9-21 of the attached PDF. Note that a tracked version of the manuscript is available after page 21. Also note that the main changes are summarized in pages 1-2.
Author Response File: Author Response.pdf
