Dear Authors
Thank-you again for your revised version; you may now have seen the referee's comments on this revised version; for reference I have copied these comments below (sections A to I). The referee still wants to see your manuscript after further "major" revision (their term). Separately to me they have emphasised their concerns expressed in sections C, D, H below, and in respect of H also the question of the analysis for figure 8 also. I think the main message in all this is that your response to the referee's concerns should be embodied in your further-revised manuscript. The referee has emphasised that he does like the scientific significance of what you are writing about here, so please take all this as encouragement to clarify your manuscript as asked for.
Yours sincerely
John Huthnance

A) This manuscript presents a method of analysis aimed to quantify diapycnal diffusivity in the upper layers of the Alboran Sea using spectral methods. There are two major conclusions: first, it is possible to map the patchy nature of mixing in this data set. Second, there is a relationship between shear instabilities and mixing hotspots in the data but no correspondence between mixing and the location/amplitude of internal waves. The reported diffusivity levels generally match those found via using other methods: XCTD, ADCP, reference models.

B) I think there is value in the results the authors attain. Products such as turbulence maps can teach us a lot about the oceanic interior and developing tools to do so using smaller seismic “high-res” hardware that can image the thermocline and shallow waters is a great step toward increasing the utility of seismic methods for oceanography. However, it is imperative to report findings as clearly and robustly as possible. I recognize that spectral methods are not the new innovation of this manuscript and am familiar with Sheen et al. 2009; Holbrook et al., 2013; and Sallares et al., 2016; and the sliding analysis window for tracked seismic reflections is not a fundamentally new methodology either, as in Fortin et al., 2016. That said, I do consider this a new method due to the application to higher resolution data; it is not obvious that findings with large systems as in Sheen (2009) and Holbrook (2013) will equally apply to smaller systems. Additionally, using only tracked reflectors and a sliding window analysis has not been done, to my knowledge. Further, Sallares et al., 2016 is a short-format paper that shows only 1 spectra of the average of 117 tracks. Averages or sums of much data is required to get good spectra (Klymak & Moum 2007, a&b) so here when the authors start using smaller subsets of reflector tracks, it is necessary to show spectra sufficient to provide evidence their method is valid. The result of these adaptations is that the method used in this manuscript should be fully justified and show much supporting data.

C) Many of the author’s responses do not address the problems from the first review and the line numbers often point to incorrect sections of text. Specifically, here I am referring to the many times the line numbers refer to sections of text that are headers, blank lines, equations, or unchanged text [e.g. lines 100-102 (blank line in both manuscript versions and unchanged opening sentence); 162-165 (addition of sentence that doesn’t add or address any concerns); 260-264 (only changed one word “anomalies” to “patches” which does not address the issues in the manuscript regarding k-rho values or distributions)]. The result is many changes that were difficult to track and, more importantly, often did not add to the clarity of the text or resolve the concerns posted in the prior review.

Major Concerns:
D) Turbulence levels in Figure 6 do not match how H1, H2, and H3 are described in the manuscript or how they fit into the turbulence map of figures 3 and 5. In the text and due to its location in figures 2 and 5, horizon H1 is described at the high turbulence reflector, while H2 and H3 are low and moderate. However, figure 6 shows the energy in the turbulent subrange of H1 to be significantly lower than either H2 or H3. The authors need to explain what is happening here or else how can we be sure their map of turbulence is accurate when the “high turbulence” example shows less energy in the turbulent subrange.

E) There are issues with the representation of resolution of the method. As stated in the abstract (line 25), the authors claim to resolve mixing with a lateral resolution on the order of 10 meters. The method applied, a rolling 1200 m x15 m analysis window, is attributing changes in spectral energy at the periphery of the window over half a kilometer away to the “high resolution” cell. It is unsurprising that, as stated in the conclusion (lines 397-398) the mixing hotspots appear to be 10-15 m vertically and 1-2 km laterally, a scale much closer to the real resolution of this treatment of the data. In their response the authors claim the method makes the turbulence maps appear more ‘ “realistic” ‘ and I agree that it does. The rolling window approach is not quite a smoothing function, but the authors should make certain the manuscript reflects the true resolution of the method.

F) Figures that are necessary, and have been produced by the authors, are missing from the manuscript.
- Figure rev2-3 shows the tracks of all the reflectors and detail of spatial coverage. This figure adds emphasis that a rolling window approach is potentially viable for this seismic line and a table or at least an average number of tracks per analysis window would make an excellent addition and help justify the handling of the data as was done in the manuscript.
- Figure rev2-2 shows much needed support for how the data was handled. The gray lines on this figure are hard to compare but show considerable variability. A re-working of this type of figure would give indication to just how certain we can be about analyses of a small number of reflector tracks broken into ~1-2 km segments.
- Figures rev2-5, rev2-6, rev2-7 include the turbulent subrange. This manuscript is fundamentally about turbulence and parts “d” from these figures should be included.

G) The relationship between internal waves and turbulence is still somewhat unclear. Lines 20-21 state “mixing tends to concentrate in areas where internal wave[s] become unstable and shear instabilities develop.” This statement leads readers to think the data have a noted relationship between internal wave and turbulent structures. However, in the conclusion lines 406-407 say, “we found no clear correspondence between the location of the mixing patches and the location and amplitude of IWs” (also lines 255-256) then go on to discuss a relationship between shear instability and mixing. These two statements seem to be at odds with one another. The matter is further confused by introducing the relationship with shear instability. This reads as saying that (1) IWs and shear instability are related, (2) shear instability and turbulence are related, but (3) IWs and turbulence are not related. If both IWs and turbulence are related to shear instability, then it should follow that a relationship between IWs and turbulence would also exist.

H) I am confused about the changes reported about analysis window length for figure 7a. Per previous review suggesting an analysis window of 1.2 km (to match the mapping analysis) the text was updated to say that figure 7a was done at 1.2 km in place of the first version using a 1 km window. However, this is no change in figure 7a from the previous version of the manuscript. I would expect a smoother profile of k-rho, particularly since the addition of 0.2 km is quite significant at the plotted scale and would encompass entire spikes and drops in turbulent signature. Further, figure rev2-2 shows great variability in non-overlapping 1.6 km segments, so there are significant differences at different points in the line and there should be differences when showing sliding 1.2 km segments as compared to 1 km segments.

I) Minor Concerns
Please explain the scale factor “b” (line 182)

Dear Authors
Thank-you again for your revised version. The referee whose comments this addressed did ask to see it again but has not responded to requests. However, the other referee was content and this referee has already seen it twice. It seems to me that with this version you have responded well to their comments, and in any case they were supportive of your work. I am now asking for some “technical corrections” (below). When you have done these the manuscript will go direct to Copernicus for publication. However, there will be copy-editing (for use of English etc.) which I expect will make some changes; you should check that these keep your intended meaning.
Thank-you for publishing in Ocean Science.

Suggested “Technical corrections” mainly for clarity or easy English; line numbers as in revised manuscript.
Lines 73-74. “(Smyth et al., 2011). In turn this makes it difficult . . dynamics. Mixing effects . .”
Lines 78-79. “climate models. Thus improving our knowledge . . mechanisms, and . . models, remain as an outstanding challenge.” [Move “thus”, add “,” twice].
Line 98. “. . allowing coverage of the existing . .”
Lines 108-9. “. . recording the energy reflected at variations of acoustic impedance (density . .”

Lines 205-206. “. . allows proper calculation of the reflector . .”
Line 211. “. . As explained . .”
Line 237. Delete first “the”

Line 297. “10**-2.5”. Looking at the first line of section 3.2, should this be “10**-2.7”?
Line 315. “. . As explained . .”
Line 344. “coincide, within error bounds, with those of the global ocean average.” You then give values in the range 10**-2.9 to 10**-3.5 which are (much) larger than 10**-4. Also in lines 315-352, “. . average kρ≈10**-4.3 m2s-1, which is close to the global ocean average . .”. These statements are inconsistent and I think it is line 344 that needs changing; something is missing?

Line 359. “. . responsible for disruption . .”
Line 368. “. . GM model, for which S10**4/SGM**4 usually ≈3. . .”?
Lines 373-375. “. . The ranges of variation . . comparable, from maximum values . . to minimum values . .”
Line 385. “. . not efficient enough to sustain the overturning . .”
Line 400. “. . regions (e.g the Gulf of Mexico . .” ? [If the Gulf of Mexico is an example and not a complete specification of “other regions”].
Line 409. “. . values along H1 exceed the global average . .”

Line 472 (Table A1) first column. “F” should be “f”? “Y” should be “ν”?
Line 474. “APPENDIX” (spelling)
Lines 487-8. “. . propose RB > 200 as safe for high mixing . .”?

Lines 756-757. “Figure S4. Current velocity profile from ADCP data, SAGAS in May, 2010. (a) The zonal velocity (V) variations, and (b) the meridional velocity (U) variations . .”