|Review of “Parameterization of oceanic whitecap fraction based on satellite observations” by Albert et al.|
I was asked by the editor Michael Schulz to give feedback on this revised version. Below, I give my opinion on how selected comments from the initial two reviewers were addressed. This is followed by a conventional review of the revised manuscript.
1.1) "Poor flow to manuscript" – Manuscript flow in section 3 still needs to be improved.
1.2) "Authors fail to distinguish the proposed formulation from SAL13" – I believe this point is still valid.
1.3) "Discussion regarding 37GHz vs 10GHz intercept is not convincing" – This is now better in the revised manuscript. But, I do not agree that too much physical insight can be inferred about the sign and trend of the y-intercept (for the 37GHz data) without first letting the wind speed exponent be a free parameter (or showing it is not statistically different to 2).
1.4) "Discussion about the “secondary factors” being “imbedded in the exponent of the wind speed dependencies” is misleading." – While I may not have used the term “misleading”, I generally agree with the reviewer on this point. In their rebuttal Albert et al. state that “Anguelova and Webster (2006) …. suggest that the influence of secondary factors is expressed as a change of the wind speed exponent”, yet here the authors have chosen to fix their wind speed exponent to 2. Additionally, I found the discussion of the statistical significance of SST effects confusing. Furthermore, the authors refer to SAL13 and state on page 32 line 3-5 that wave field development is the most important secondary factor accounting for variability in W after wind speed, yet this was not investigated here. Therefore without presented evidence to the contrary, it is possible that any inferences regarding the influence of SST may be inadvertently due to wave field variability.
2.1) "Results and conclusions are rather limited. The paper has potential, but needs additional work." – In my opinion this comment still stands. I am not convinced that the authors have gone above and beyond what was presented in SAL13. I do not see the utility of another parameterization for the same W dataset presented in SAL13. A more fruitful line of enquiry may be to apply the results of SAL13 to SSA emission flux predictions and/or present a more thorough comparison of regional differences in W variability by considering wave and temperature effects.
2.2) "Regardless of the well correlated linear fits of sqrt(W) there is little justification why it should be quadratic" - I agree with the reviewer, and this aspect has not been sufficiently supported or defended in the actual manuscript. The inclusion of an investigation of a cubic wind speed dependence in the paper serves little purpose.
2.3) "Progress over the extensively referenced Salisbury et al. paper is poorly documented or highlighted" – I still believe this is a valid comment.
2.4) "The main advantage of the paper might be exploration of regional differences" – I agree with the reviewer, and believe this should be the focus of a revised paper, with more thorough evaluation of combined wave field effects and SST effects.
2.5) "I disagree with the concept of avoiding intrinsic correlation of W and U10 substituting QSCAT wind speed by ECMWF wind. In fairness, W should have been fitted directly to ECMWF data of whatever resolution because a large scatter (regardless of good overall correlation) between two wind speed datasets could have produced discernible differences in W." – From what I understand of the satellite retrieval algorithm, some intrinsic correlation is to be expected when W is parameterized with U10QSCAT. This is evident in the reduced scatter when W is plotted against U10QSCAT in comparison to U10ECMWF in the revised paper (figures 6 and 7). The authors have tried to evaluate this. However, in addition, I suggest that the difference in W data scatter when using U10QSCAT in comparison to U10ECMWF be quantified by evaluating W data spread at specific values of U10 for each wind speed source. Ideally, for robustness, any statistical inferences between W variability and SST (or other forcing factors) could also be evaluated using both sources of wind speed data. However, it should not be forgotten that the retrieval of W using satellites represents a very important progression in remote sensing capabilities and will no doubt continue to improve. As long as the magnitude of intrinsic correlation is known, progress can still be made.
The authors have clearly invested significant effort into this manuscript, and into the revisions. This effort is recognized by this reviewer. However, I find that that many of the initial concerns of the 2 reviewers to be still valid. For this reason, I suggest the paper needs further work or a change of focus. For example, the focus could be shifted to provide more detail on regional differences in W (perhaps using a more limited number of regions) to really derive more physical insight into W variability in relation to a wider range of factors other than SST, which can then be applied to SSA flux. Also, detailed spectral model wave data (e.g. from ECMWF wave model or similar) could be incorporated into a revised study to complement the existing data sources. Alternatively, the authors could follow on from the Salisbury et al. papers and apply the results already derived from that work to SSA flux, and potentially, to gas flux.
i) The authors have not presented a convincing case that fixing the wind speed exponent to 2 in their parameterisations is justified. I believe that it should be a free parameter, as this will have implications for how they physically interpret the resulting fit coefficients. If, however, they show that the wind speed exponent is not significantly different to 2, (I.e. is within 95% confidence intervals of 2), then they would be more justified in their analysis, and this would be acceptable.
ii) The authors state that wave field development is the second biggest factor influencing W, after U10, yet this was not considered at all in the study. Therefore, any conclusions related to SST are limited and may be due to potential correlations between SST and wave field development.
iii) An additional quantification of potential self-correlation between W and U10QSCAT could be provided. For example, a measure of the data scatter around the W-U10ECMWF and W-U10QSCAT parameterizations, as a function of wind speed, could be presented. This could be done as an rms error as a function of wind speed for each wind speed product, and/or by showing W residuals as a function of wind speed. I suggest this because of the quite large difference in the spread of W(U10) values in figure 7 when compared with figure 6b (i.e. using two estimates of U10). (Is it the same for 10GHz data?) Performing subsequent statistical tests on W data variability in relation to secondary factors using U10QSCAT and U10ECMWF are likely to be different, and potentially significantly so.
iv) Regarding the flow of the manuscript, I found the text to be improved but still confusing in several locations (especially in several parts of section 3) suggesting that significant points could be better articulated.
Page 2. Line 12. The mean whitecap coverage estimate from Blanchard is given as 1.2X10^17, which corresponds to about a 3.33% coverage.
Figure 4(a,b) should be presented with logarithmic y-axis.
Page 8, line 13-14. Then why was n fixed to 2 here when investigating different regional variations?
Pag3 14, line 14. When all satellite W data are included, how does the data spread compare to the spread in in-situ W data? Does it cover the same 3 orders of magnitude variability?
Page 16 Line 6. Why is the timescale absorbed into the shape factor?
Figure 5. On lines 1-5, page 11, the authors state that W37 should always be greater than W10. Yet, Figure 5 suggests this is violated sometimes.
Pg19, Lines 1-2. Why is wave field development not addressed here given the statement further into the manuscript? (see page 32, line 3-5)
Page 20, line 5. Wind speed product plays a role in the variability. For example, and as commented upon in SAL13, using the same W dataset but wind speed from QuikSCAT and ECMWF, Goddijn-Murphy et al (2011) found the exponent on a simple wind speed only whitecap coverage parameterization to change by a factor of 2 from 1.86 (±0.14) to 3.76 (±0.20). The only way to investigate if such an effect is seen in this study is to use a parameterization of the form W = a (U10 + b)^n, with both sources of wind, where all fitting coefficients are free parameters, and n is not pre-determined.
Page 20 , lines 13-end, and Page 21, lines 1-5. While it is reasonable to assume that surfactants may stabilize foam so that it is present at wind speeds below 3 m/s, a discussion on the sign of the b coefficient in the formula (W = a (U10 + b)^n) must only be done after a fitting exercise which leaves the wind speed exponent (n) as a free-parameter.
Figure 7. The solid line in Figure 7 should go through the origin as reported in the legend. Figure7 could be presented with part a and b. Part a as is already presented, with part b on a logarithmic y-axis and with W in place of W^1/2.
Figure 8. The information presented in this figure may be better represented in a table where regions, seasons, and fit coefficients (along with 95% confidence intervals) are presented. As it stands, the information in figure 8 is poorly communicated to the reader.
95% confidence intervals are needed on the datapoints presented in figure 9 (and on all fitting coefficients). Also, here and page 23 lines 21-29, stick to either evaluating potential trends in coefficients and or coefficients and . Otherwise it becomes too confusing for the reader.
Page 26, Line 24-26. Here, the authors are extrapolating the MOM function to wind speeds well beyond the range over which the MOM function was determined. This needs to be stated. Also, given the statement later on page 29 lines11-15, is this exercise valid?
Page 27, Lines 8-15. I don’t understand this paragraph. The authors say that SST does not have a statistically significant effect on W values in the previous paragraph. Yet here, they say that a single quadratic parameterization, without additional temperature information, implicitly accounts for “most of the SST (and other) influences”. But, how can they account for SST influences if they are not statistically significant, and how can they deconvolve this signal from other potentially stronger signals such as sea state development which has already been shown to be important in SAL13?
Page 27, Lines 16-24. It is my opinion that the wind speed exponent be a free-parameter.
Page 28, Line6-8. But the parameterization was generated using this dataset. So why is this a noteworthy result? The parameterization would likely follow the data even better if the exponent was a free parameter, and not fixed at 2.
Page 28, Line8-10. I believe this shows that secondary factors do not have a large influence on this satellite derived dataset.
Page28, Lines11-19. Here the authors have lost me. This is especially unfortunate since they state that this paragraph contains the most significant result of the paper. Also, (lines 16-17 specifically), SAL13 comment that satellite retrievals above 20 m/s be handled with caution, where W10 and W37 cross-over, which is not physically reasonable. I suggest that comments relating to differences in W parameterizations at wind speeds > 20 m/s be removed.
Page 28, Lines 25-31. The authors have not convinced me that any inferences on different combinations of U10 and T have systematic influences on W. Also, SAL13 have already derived parameterisations that are different from previous cubic parameterisations such as CAL08 and MOM80.
Page 29, lines 21-23. I am confused. The authors state on page 26, lines 20-24, that “ANOVA and Student tests show no significant difference” between the quadratic parameterization, and MOM80.
Page 32, line 3-5. If wave field development is more important than SST, then how can we evaluate any of the statements on SSA emission and W related to SST, when this has not been addressed in this manuscript?