This revised manuscript has been extended to accommodate some of reviewer’s initial comments. The reviewer acknowledges that this manuscript is formally different from the arXiv Zakharov et al. 2012 paper. Therefore the revised manuscript was reexamined in more detail. As said in the previous review this manuscript is interesting work deserving attention, but it appears to have been put together too hastily as there are still many issues to explain. Despite important improvements there are still issues to be clarified requiring a major and serious revision.
The statement by the authors that the new results (to check the consistency of the new paradigm for duration limited wave growth) are sufficient for publication in NPG, is in my opinion not for the authors to decide but for the editor after consulting the reviewer’s opinion.
The lack of clarity related to the description of the figures is a severe shortcoming of this manuscript. It may suffice in a (PowerPoint) presentation but not in a written exposure. Although the results may support the author’s expectations, this is not sufficiently for a journal article where one should convince the reader in written language. Some issues per figure are summarized below. Another issue is the lack of quantification of errors. Now only subjective statements are made about the agreements. This is too subjective, as in some cases errors up to 10% are encountered and presented without any comment.
The title is still not appropriate. The focus is not on wind only, but on the whole concept of the new set of source terms.
All computations have been performed with only one wind speed U=10 m/s. This may be OK to point out some seemingly interesting findings. But it lacks generality, especially in relation to the choice of a fixed frequency f=1.1 Hz where the Phillips tail is forced on the spectrum to mimic the implicit dissipation. Is the present method also applicable for low wind speeds in the order of a few m/s?
The authors comment on the physical basis of the ZRP wind input by providing 4 arguments. These are valid arguments indeed, but in my opinion they miss my key comment. The ZRP wind input was derived by virtue of the implicit damping forcing the tail to an f-5 shape In Eq. (11) only source terms for Snl4 and Sinp exist, whereas no Sds term is present. So, only the COMBINATION of ZRP and implicit damping enables the self-similar spectra, but no conclusion can be drawn about the validity (or physical basis) of the individual processes of dissipation and wind input. It is interesting that this notion is expressed by the authors on page 2, see line 28 ( .. our explanation is simple but has the same consequences), and line 33 (..and INDIRECTLY confirmed …). These statements cannot be considered as proof that each individual mechanism is based on first principles. i.e. a physical basis. Therefore my original questions remains: what is the physical basis of the individual source terms for wind input and dissipation?
The numerical implementation of the implicit damping in the form of a Phillips f-5 tail has still not properly been explained. Just noting that details are of secondary importance cannot be an excuse. A key requirement of any paper is reproducibility. Further, the choice of applying such a tail always from f=1.1 Hz may be valid in the range of wind speed observed in Resio and Long (2007) and here for U10=10 m/s, but it may fail for lower wind speeds. In the extreme of a wind speed of 1.15 m/s the Pierson-Moskowitz peak frequency coincides with 1.1 Hz. This limitation and the applicability for low wind speed should be discussed.
On page 7, line 13 information is missing on the frequency range and spacing.
In addition, applying the implicit damping and forcing the spectral shape for frequencies close to the peak frequency, degrades the wave model concept from a 3G-model to a 2.5 G model. This issue should also be discussed. It may limit the general applicability of this method in wave forecasting techniques.
Page 8, line 15. Details of the numerical procedure are still missing. That details might be provided in a further paper is no excuse to omit them here. It can’t be that difficult to describe these in a kind of pseudo-code which steps are taken in the numerical procedure. Is a constant time step used or does it depend on dimensionless fetch or duration (as in the EXACT-NL model of Hasselmann and Hasselmann, 1981). Is the time stepping explicitly, or implicitly, etc… Of particular interest is the treatment of the source terms in the action balance equation. It is therefore surprising that Eq. (45) contains a Sds term, whereas this term is missing in Eq. (11). These apparent inconsistency should be removed or at least explained if they are required for this manuscript. Does it hint that implicit damping is formulated in terms of a source term? If true, then the formulation of this source term should be provided.
On page 9, line 2 the universality of the omega-4 for large frequencies is mentioned. This statement needs clarification as it is not clear what is meant with LARGE frequencies. Are these higher than 1.1 Hz? Looking at Figure 7 a typical spectral shape is seen with an f-4 region just above the peak frequency and a Phillips tail for larger frequencies.
Page 9, line 10. Which RMS value is referred too?
Page 8, section 4.2. Which method was used to estimate the parameters p and q?
Page 12, line 10. Please correct. It is the dimensionless total energy!
Page 12, line 10. Please correct. It is the dimensionless fetch!
Page 12, line 12. Please correct. It is the dimensionless mean frequency!
Page 13. The conclusions are a bit short. There is hardly a serious discussion on the application of this promising method for other cases including applications to lower wind speeds.
The range of applicability for other than academic 1D-cases is not discussed at all. As mentioned in PZ2016 the next step should be to test the applicability in 2D- field cases, but nothing is said about this. Neither about the applicability of implicit damping for low wind speeds when the value of 1.1 Hz may not be appropriate any more.
The introduction and discussion of the results in the many figures presented is still poor. Some comments to a specific figure may also hold for other figures. My comments serve as a guideline for clarifying many detailed issues and the authors should check this carefully!.
Figure 2 contains a systematic deviation between results and the fit. This does not look like a fit as the lines only coincide at the origin. This difference is puzzling. Some lines are not explained in the egend to the figure or in body text.
Figure 3. Add the target value of p=10/7 and comment that the relative error is still 6%, which is clearly subjectively acceptable by the authors. It could also be noted that there is an asymptotic behavior for long duration. Whether this also occurs in nature, where conditions are less ideal, should be a point of discussion.
Figure 4: the different lines in the figure are not explained in the legend and in the body text. It is puzzling why the fitted line has a systematic difference with the computed line. I wonder whether it is a fit at all. In case it is a fit, then the method how the fit was made should be explained.
Fig 5: the magic target value of q is missing in this figure and legend. The occurrence of the wiggles is not noted and discussed. Further, there is a discrepancy between the sign of q in the body text and in the figure
Figure 6: the magic target of p=1 is not plotted. The choice of the range along the vertical axis obscures the relative error of 10%, which is seemingly acceptable by the authors. Nowhere in the manuscript such differences are explained. Only subjective statements about ‘goodness of fit’ are made.
Figure 7: the dashed lines are not explained in the legend. The legend along the x-axis is wrong. Although the frequencies are plotted on a log-scale, the actual frequencies are shown. So the legend should just be f (Hz). Note that the unit should be added. Further no comments are made on the regions in the spectrum where the spectrum adheres to either an f-4 of f-5 tail. Some guidance to actual values enhances the readability.
This typical spectral shape is worth mentioning, especially as this shape has been observed in nature. It is unclear why the authors have not been searching for empirical evidence of this behavior. It could only strengthen their case and is one of the interesting results of this study.
Figure 8 appears after figure 9. This should be reversed. The dashed line is not explained in the legend. The inertial range should be better explained as not all readers immediately see where to look.
Figure 10. The broadening of the spectrum is not visible in this type figure. A direct way, and more convincing, is to plot the directional spreading as a function of frequency. Take care of dimensions along figure axes.
Figure 11: The line types are not defined. The RMS error should be quantified. The range of values to which the dots refer should be mentioned as it is not yet stated which part of the simulation is covered. The convergence to theoretical results should be mentioned. Also, an explanation why the regression line has a systematic deviation to the computational results should be discussed. Usually, a fitted line has a certain minimum error and is close to the data points, but not here. Details about the fit procedure should be provided, at least for reproducibility.
Figure 12:Here is good agreement indeed. Not much to add.
Figure 13: There is still an error of about 5% in the computed value of p. Wiggles appear in the simulation. This should be noted and explained in the context of this study. The choice of the range along the vertical scale subjectively improves the quality of the results. This may be OK, but only in combination with a quantitative assessment of the error.
Figure 14: The various lines in this figure are hardly explained in the body text. Further, fp is not mentioned. To what purpose have both fm and fp been plotted? There is no discussion about the relative position of these lines and whether this is acceptable. There seems to be a systematic bias in the results.
Figure 15, Text is missing about what can be seen in this figure. Also a mismatch in sign of q between body text and figure.
Figure 16. Here is good agreement, but also some wiggles appear in the solution
Figure 17. The legend along the x-axis is wrong, it should be f (Hz) and probably also for the y-axis. The data are plotted on log-scale but the values remain unchanged. The dashed and dash-dot line are not explained in the legend.
Figure 18. The dotted line is not explained in the legend. An explanation is required why the ZRP wind-input term drops to zero for f> 1.1 Hz. This seems related to the numerical procedure, but has not been explained. It also contradicts the equations 41-44 where no mention was made of this behavior. It appears an essential part of the numerical procedure requiring explanation.
Figure 19. The units are missing along the x-axis. Also note the discontinuity of the compensated spectrum at f=1.1 Hz. This is a puzzling issue.
Figure 20. See also comments on Figure 10. Further, the origin of the secondary peaks at angels of +/-85° should be noted. Is this a serious side-effect?
Figure 21: Note the convergence to the theoretical results. Also, what range do the plotted symbols cover. |
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