Melting Layer Detection and Characterization based on Range Height Indicator–Quasi Vertical Profiles

Round 1

Reviewer 1 Report

This paper describes the melting layer detection using a multi-parameter radar. The objective is sound. However, the contents are poor. Only results of cases are presented. Interpretation of results and discussion are very poor, and new findings are unclear. I would like to encourage authors to work with more detailed discussions with generality of the results and new findings.

Author Response

Thank you for your time and effort in reviewing this paper.

Please see the attached documents for a detailed response.

Author Response File: Author Response.pdf

Reviewer 2 Report

This manuscript presented a ML detection algorithm using Dualpol moments from X-band radars. The authors presented and analyzed performance of the presented algorithm via multiple cases. This manuscript achieved a highly publishable quality. This method was simple, yet very useful. The case studies included multiple kinds of weather scenarios and showed decent performance on all of them. Thus I didn't have any major comments, only a few suggestions.

 

Line 144-146. Please reformat equations and put them in line center. It would be better to explain rationale of each parameter and describe how and why there are designed so. Line 208. Please add a section around/after Line 211 to discuss/justify why these five cases were selected, how they were representing each kind of weather scenario.  Please double check if figures should be referred as "Fig. X" in texts, rather than "Figure X".

 

 

Author Response

Thank you for your time and effort in reviewing this paper.

Please see the attached documents for a detailed response.

Author Response File: Author Response.pdf

Reviewer 3 Report

General Comments:

While overall the paper is fairly well written, there are a number of grammatical errors that exist, primarily related to the usage of articles and awkward phrasings that could be improved. One of my major concerns with the manuscript is the lack of a clearly-stated motivation. The background section does not seem fully synthesized and comes across as just a list of prior studies’ results without linkages. But to this point: all of these references to other polarimetric ML studies are provided, but it is never clearly stated why yet another approach is needed. What are the deficiencies and concerns with other existing schemes? How do the results from the new proposed scheme compare? In section 2.2 describing the algorithm, some of the same studies are again mentioned but the manuscript then jumps to the fact that the authors “refined” the algorithm. In addition, even the description of the value of the polarimetric variables for ML detection given in section 2.2 is confusing and somewhat haphazard (see Specific Comments 12-17), with the same sentiments often repeated multiple times throughout the manuscript. The motivation for why this work is needed and important would be much clearer if the reasons for wanting a new method of ML detection were laid out explicitly and if the results were compared against those of other methods (maximum value approaches, vertical gradient approaches, etc) that demonstrate why this approach is superior. I also have concerns about the methodology of the work. How was a vertical grid spacing of 250 m decided, and is a higher resolution not attainable? This coarse a resolution is likely insufficient for true ML depth determination with any precision. For example, Fabry and Zawadzki (1995) show that the large majority of true ML depths (from a vertically-pointing radar) are 500 m or less, with many on the order of 250 m. I am also confused about a number of specifics regarding the methodology pertaining to the calculation of gradients and the multiplication of rhohv to the other variables (see specific comments #19, 20, 21). In terms of clarity, I think the methodology section would greatly benefit from a flowchart of the algorithm. There are a number of issues pertaining to the presentation of results and conclusions. The problems lie in both the rigor of the verification and the findings. The verification of the results using MERRA seems indirect and somewhat superficial. How accurate is MERRA, particularly for things like QL and QI? There are reasons to seem suspicious of it: for example, Fig. 6c shows significant QL up to 7 km at temperatures < -10C in what is clearly a weak stratiform case. In addition, rather than the temperature it is the wetbulb temperature that should represent the ML top, as melting can be delayed for 100s of m in dry environments. Can this be computed and used instead? The inclusion of surface data (e.g., T and RH) and much of the discussion involving the vertical profiles (e.g., wind speed) seemed somewhat irrelevant for evaluating ML detection. Many of the comparisons also feature vague statements about approximate heights and rough ranges (e.g., Specific Comment #32, 39) given without any further quantitative analysis. For example, with a larger case set could scatterplots be presented of reanalysis wetbulb-zero height and detected ML top height? Something more quantitative would more readily elucidate any biases in the algorithm results. Finally, the use of only 5 cases, while good to demonstrate examples of the algorithm’s performance, really prevent the calculation of significant statistics such as those shown in Table 1 (see Specific Comment #43). More broadly, the conclusions presented do not seem completely novel, as it is already widely understood that melting layer heights oscillate with the seasons and are higher in the summer than winter. In that sense, the novelty of the paper lies in the proposed algorithm methodology, highlighting the importance of a more clearly formulated motivation and context for the work (see General Comment #3).

 

Specific Comments:

Line 35: When discussing snowstorm events, why mention the descent into warmer temperatures if no phase transition occurs? Line 44: “The high-resolution, X-band dual polarization radar” makes it sound as though the authors are talking about a specific radar instead of the value of dual-polarization radar in general. Also, the subsequent sentence seems to just reiterate this one about the microphysical information available from dual-polarization radars. Lines 60-61: What is meant by these variables having “similar distributions”? Similar distribution shapes, similar distributions among cases, etc. Line 61: What is meant by “strong” melting layers? Lines 62-65: This abrupt change to discussing refreezing seems out of place and unrelated to everything else in this section and paper. Line 67: The Brandes and Ikeda study was focused on the freezing level, not the melting layer, and hence was characterized by low ZDR. It is inaccurate to say that they characterized the melting layer by low ZDR. Line 76: Isn’t 6 km higher than typical melting layer heights? If it is within an updraft, is it still correct to refer to this region as a melting layer? What are the benefits of using R-QVPs over regular QVPs? Is the motivation to develop a QVP method for RHIs because the radar in question already scans in an RHI configuration as opposed to PPIs? Line 101: I see no mention of refreezing rain in this manuscript. Also, I would describe the verification as “indirect”, or simply compared with temperature, RH, etc. Line 109, 209-211: These sentences are not needed and can be removed. Line 113: The process of R-QVP construction should be explained in more detail. My impression is that the data at a given range gate from each elevation angle in the RHI is converted to a physical height, and then data from multiple elevation angles within a given 250-m vertical grid spacing are averaged together. However, the use of the phrase “elevation-wise averaging” initially implied to me that data was averaged on a given elevation angle plane (i.e., on a sloped surface). In addition, is only one azimuthal angle used to construct the R-QVP, or are data from all RHI azimuths used? If the former is the case, then which azimuths were used should be included for each of the case studies. Line 123: “Large-wetted particles” are already considered under the sensitivity to “precipitation type” (i.e., phase). Line 125: What is meant by “complex interactions” being responsible for the increase in Z? The topology of water inclusions in a melting snow aggregate can certainly be complex, but the actual reasons for the increase in Z in the ML are straightforward (and addressed in the subsequent sentence): an increase in the dielectric factor of the particles, and possibly enhanced aggregation rates, before they melt into smaller raindrops and decrease in concentration due to flux divergence. Line 127: This sentence needs to be qualified: ZDR can easily exceed that typical of rain for pristine ice crystals, while snow aggregates tend to have ZDR below that of the equivalent rain distribution. Line 127: The sentence “In the ML, the ice particles tend to precipitate in the form of rain” is confusing and doesn’t make sense. By definition ice particles are already melting in the ML, but are also not yet rain until they are out of the melting layer. Are the authors trying to state that ice particles transition to rain drops within the melting layer, and hence their axis ratio evolves during melting (as stated in the following sentence)? Line 129: The ZDR increases in rain over what – that of snow or melting snow? I assume this sentence is addressing the smaller typical canting angles of raindrops compared to snow, rather than the increase in ZDR due to changes in shape and dielectric factor? Lines 134-137: There are numerous confusing statements in this section. It is stated that [6] suggested ZDR, rhohv, and KDP are more sensitive for wetted particles – more sensitive than what? “ML depends on the habits and size of frozen particles” – what about the ML depends on these things (e.g., depth, amplitude of BB characteristics, etc)? What about Z, ZDR, and rhohv is “robust”? Is the point being made just that all 4 polarimetric variables (Z, ZDR, rhohv, and KDP) have distinct polarimetric signatures in the BB that can be used for detection of the ML? If so, haven’t these points been made in the previous section? Line 138: What is the “combined method” referenced here? Also, on Line 139 I would just clarify that the profiles are being normalized by the maximum value in the profile. Lines 140-143: I am very confused by the proposed methodology described here. What is meant by “these gradients could not detect the true ML thickness”? Other studies have successfully use the change in gradient of Z and rhohv at the top/bottom of the BB to detect the ML. How is the true ML thickness being determined? Why is the (inverted) rhohv multiplied with Z and Zdr and what is the basis for doing so? This isn’t clearly stated. I understand that owing to the decrease of rhohv in the ML that doing this multiplication prior to normalizing will accentuate the brightband signature amplitude, but why is this needed? Lines 151-152: I don’t believe that the maximum value of the gradient represents the bottom of the melting layer. As an example, for a Gaussian profile the gradient will be maximized in the bottom half of the profile, not at its endpoint. To that point, it appears that your gradients have been “forward” calculated – that is, the gradient value assigned at height i is calculated from X(i+1) – X(i). Because of that, the actual location of the maximum gradient is being nudged downward by up to 250 m, perhaps giving the algorithm a more correct result for the wrong reason. At the very least, the fact that the gradient is being assigned at i rather than centered-differencing (i.e., at i + 0.5i) needs to be explicitly stated. Lines 153-157: Again, the same concern from the previous comment applies to the ML top. In terms of depth, the errors from the nudging of both downward may offset each other, but the actual heights of the ML top and bottom will be biased. It should also be clarified that the Z and Zdr values discussed here are the normalized values, and that the rhohv values are considerably lower in the top half of the ML, not higher. Line 161: This sentence should be amended to something like, “… the maximum height of either the height of the minimum Z or maximum rhohv gradients should be greater…”. The use of the word “between” led me to believe the authors were referring to the difference in height between the gradient maxima. Line 176: This should say “the minimum and maximum gradients of Zh and rhohv…” Lines 192-193: How does the radar provide 1 PPI per minute but 6 PPIs in 5 min? Line 196: How is the backscatter differential phase δ being treated in the calculation of KDP? The KDP shown in Figure 1 appears to have an oscillatory profile, with large values in the bottom part of the ML and negative values in the top part of the ML, which suggests that δ is not being removed and is biasing the KDP estimates. Line 205: QL and QI need to be defined. Lines 231-233: This has already been covered in both the background section and section 2.2. 2a: Where is V coming from – a vertically-pointing stare of the radar? If it is taken from horizontal data, is it being corrected for elevation dependence? I don’t see much info about where this is coming from. 2b, 2c and elsewhere: Where are these profiles being taken from in MERRA – the radar site, or averaged along the R-QVP path? I see that it says for Goyang Province, but were the MERRA columns averaged over the province? Line 239: Is the increase in wind speed alleged to be from the rain reaching the surface, and not other meteorological factors? 2c: The data for QI shoots straight off the graph. Can the x-axis be expanded to show the maximum data values? Line 243: Can liquid water in the re-analysis at 6 km really be used to justify the detection of a ML that allegedly begins at 5 km? Lines 245-248: What is meant by “a larger ZDR peak than the Z peak”, since these are two different variables – just that the relative normalized amplitude of the ZDR peak is larger? I also think the “maximum eccentricity” needs to be qualified – of which size particles? It seems more likely that the smallest particles have already collapsed into nearly spherical raindrops that are small and contribute less to Z in general, leaving the largest aggregates dominating Z and thus ZDR (rather than solely being related to shape alone). Line 251: A true ML thickness of 1 km (nevermind 1.6 km) is very large and almost unheard of (see Fabry and Zawadzki 1995), unless due to significant riming or dry air/low lapse rates. How confident are the authors in such a result? Line 253-254: It may be more correct to say the BB was absent, since the melting layer (of hypothetical melting) still exists there. Lines 259-260: It appears to me that Z also decreases toward the ground (whether due to evaporation, drop breakup, etc) – unless the authors mean the Z is higher on the bottom side of the BB than the top? Also, besides the BB itself, what is meant by “this is indicative of the phase change of the hydrometeors”? Finally, it appears that in many instances the ZDR is higher above the BB (>0.5 dB) than below it (<0.1 dB)… Line 263-264: Is the rhohv high due to deposition and riming (which I believe can actually slightly depress rhohv) or just the homogenous nature of the hydrometeors? Lines 266-268: This speaks to Comment #28, but are these downward fall speeds defined positively? Or is it actually radar-measured vertical velocity, which includes the wind component? V appears to decrease toward the ML – is this the riming and aggregation referred to? Again, on Lines 294-295, it is stated that the high V implies ice while the low V implies rain – is that because positive w advects ice crystals upward more than rain due to their lower terminal velocity? I am struggling to reconcile the statements regarding V with the implied conclusions. Line 283: The 0C line appears to me to be closer to 3.5-3.8 km than 3.8-4.0 km. Line 287: What is meant by “QL associated with RH”? Do the authors mean “both QL and RH”? Lines 310-311: Do the authors mean “changed over” to snow rather than “converted”? Line 315: It seems more likely that the rain falling into a dry layer near the surface is causing the RH to rise, rather than the other way around. Table 1 presents the mean top and bottom ML heights at greater precision than is available from the data given the 250 m resolution. The table also requires units [km]. Finally, are these statistics only from the 5 cases examined in the paper, with only 1-2 per season? If so, despite these conclusions already being known (see General Comment #5), this is a small sample size with which to make such a claim. Line 363-364: How did these radar variables (and V) indicate the different shapes of the ice particles? Line 374, 377: More useful than what? How does the work shown here provide early warnings to the public?

Author Response

Thank you for your time and effort in reviewing this paper.

Please see the attached documents for a detailed response.

Author Response File: Author Response.pdf

Round 2

Reviewer 1 Report

I understand that the paper shows the applicability of R-QVP method. Another good result is the statistics derived from R-QVP method. The discussion, particularly, in terms of cloud physics is still poor. But I would like to agree to accept this paper. 

Author Response

I understand that the paper shows the applicability of R-QVP method. Another good result is the statistics derived from R-QVP method. The discussion, particularly, in terms of cloud physics is still poor. But I would like to agree to accept this paper. 

=> We thank the reviewer for accepting the paper. Now, we added some more discussion related to the cloud physics.

Reviewer 3 Report

I appreciate the detailed efforts the authors have made to respond to the issues raised in my previous review. I now believe the manuscript is much improved and clearer than before. However, there are still a number of concerns I have with the manuscript, some of which are minor, some of which are related to the new content in the paper (outdated captions, etc), and some of which are sources of confusion that remain from the original draft. Once these are resolved, I feel the manuscript will be acceptable for publication.

 

Line 57: This sentence has no further details and seems out of place. Also, the following sentence appears to be missing a few words.

 

Line 73: The use of “melting process rate” is misleading here, since the number of particles doesn’t affect the melting rate, and an “increased melting rate” implies faster melting, which would result in a thinner brightband. Do the authors mean to say that increased numbers of particles results in more cooling due to melting, etc?

 

Line 96: Why could Allabakash et al. not provide the ML characteristics? Could not, or did not?

 

Line 99-100: I appreciate the expanded description of the motivation, although I still do not quite understand why it should matter how the radar data was processed. Put another way: the goal of both QVPs and R-QVPs is to obtain a high-quality time-height series of radar data through averaging. Given that all of these ML-detection approaches just look vertically within a single profile of radar data, why would a method work for QVP data and not R-QVP data if it is only dependent on having an accurate vertical profile of the polarimetric variables in the end?

 

Table 1: What do the numbers in the CAPPI column represent? What do the symbols in the “Volume” column represent?

 

Line 146: By “significant”, do the authors mean they were more important? Or was something about the actual magnitude of these variables significant?

 

Line 146-148: I’m not sure what is meant by this sentence, especially as Z is the most sensitive to particle size out of all those variables.

 

Lines 154-155: I’m still a bit confused as to why the Wolfensberger algorithm is said to fail so often. From my knowledge of the algorithm, it performed well in their original study, especially with the secondary correction process included (their steps 8-11). Considering point #4, what would it cause to perform so poorly using R-QVP data?

 

Line 171: Should this be “higher (1-rhohv) values”?

 

Line 199 and elsewhere: The text says “wetbulb temperature” but all of the figures for each case still say temperature in both the image and caption. Do the figures and captions need to be updated to reflect it being the wetbulb temperature? Also, all of the temperature profiles in Figs. 4c, 5c, 6c, 7c, and 8c look exactly the same as they did in the original manuscript, even in areas of dry where a substantial difference between temperature and wetbulb temperature should exist. Were these figures actually updated to use wetbulb temperature as stated?

 

Line 243 and elsewhere: Which Zh and rhohv values are being used? Does the dashed line refer to the Wolfensberger methodology? Or does it refer to excluding the ZDR gradient in the current approach? If the former, it appears that it is the melting layer top that is primarily affected—was their second step of steps used? I’m just surprised that this is such an issue with the R-QVP data that wasn’t an issue with their RHI data in the original study.

 

The dashed lines in Fig. 4 and others are very hard to see in some panels, and appears to be a solid line in the rhohv panel. Finally, information about the dashed line needs to be added to all of the captions.

 

At the bottom of page 9, it appears this is an extra figure that needs to be removed.

 

I see in Figs. 4, 5, etc. that the resolution of the radar data is increased to 100 m, but it still appears that the detected melting layer is at a 250 m vertical resolution. My primary concern with the resolution of the radar data was the effect it had on the melting layer top/bottom detection. I know the authors state they compared the results and they did not differ too much between 100 and 250 m, but I think it would be good to have the resolution of both the radar and the ML top/bottom match at 100 m, especially since statistics are being computed on them. More precise estimates would presumably help the robustness of these statistics given the typical thickness of observed brightbands relative to a 250 m resolution.

 

Line 292: I believe this should be “rain and ice” rather than “ice and rain”.

 

Line 295-296: It is probably more correct to say that it is the depositional growth of the pristine ice crystals (e.g., Kennedy and Rutledge 2011) that results in the reduced rhohv rather than the “homogenous nature” of the pristine ice.

 

5c: Given that the QI scale is very small at 1e-10, can the scale be increased so that the data doesn’t shoot out of the figure’s range?

 

Line 331: “(solid lines)” should be “(dashed lines)”.

 

Figure 8b and elsewhere: What causes the oscillation of ZDR and the occasional negative values? Was ZDR calibrated in any way?

 

Line 434: I am terribly confused by point #6. Given that we are talking about snow (not hail), the “solid particles” should have a much lower terminal velocity than rain. In that sense I don’t understand the results here. Also, is Fig. 10e the actual Doppler velocity spectra or a PDF of the observed values as with the other variables? Assuming the latter, what do values as low (high) as -20 m/s (20 m/s) represent? I still do not see much information presented on what V is (vertical velocity? horizontal velocity? radial velocity measured by the radar at each elevation angle averaged together?). Am I correct that since this includes vertical velocity of the air, that the “low” values for rain are because the high terminal velocity of raindrops overcomes the positive vertical velocity moreso than snow, which subsequently has a “high” vertical velocity? If so, how is vertical velocity being calculated – is it from a vertical stare of the radar? The authors state that this is covered in 2.1, but I do not see any information specifically regarding V and what it means.

Author Response

Please refer the attached document.

Author Response File: Author Response.pdf