Based on a series of idealized baroclinic life cycle experiments with the ICOsahedral Nonhydrostatic (ICON) model, this manuscript investigates the role of gravity waves in vertical wind shear and potential turbulence occurrence over the extratropical lowermost stratosphere. It is suggested in this manuscript that the inclusion of moist processes helps in amplifying gravity wave activity and turbulence potential. This subject is of interest, especially for better understanding gravity waves, moist convection, and turbulence in midlatitudes. However, in my view, there is still room for improvement. For example, it is not convincing to me that the small-scale perturbations extracted by the current study are all gravity waves, since the scale separation assumption between gravity waves and Rossby waves may not be valid over the upper troposphere and lower stratosphere (UTLS) region in midlatitudes, especially with such a small cutoff wavenumber used in this manuscript. Furthermore, I have concerns on the simulation design, which is based on a relatively coarse horizontal grid spacing for explicit convection (no convective parameterization is employed). In addition, many interpretations on the existing results should be clarified. Finally, there are many minor mistakes in terms of the scientific writing. For the above-mentioned reasons, although such theoretical work based on the idealized numerical simulations should be encouraged, I would have to advise MAJOR REVISION in this round of my review. The below paragraphs show my comments in detail, and I hope that they could help the authors improve the manuscript, in order to take the next step in the future.

Major comments

1. Extraction of gravity wave signals

I have concerns on the current investigation method for retrieving gravity wave perturbations, in which 8 is chosen as the cutoff wavenumber (either along each latitudinal band by the 1D FFT filter, or over the entire globe by the spherical harmonic filter. For example, as pointed out and exemplified recently by Wei et al. (2022), only using the statistical approach is sometimes not enough when calculating momentum fluxes induced by gravity waves, and it would be better in this case to also include a dynamical approach (e.g., extracting the divergent components of the winds by the Helmholtz decomposition technique). The main reason here is that the scale separation assumption between gravity wave and other signals (e.g., Rossby waves) may not be valid. In particular for this paper, the cutoff wavenumber (if it is referred to as zonal wavenumber 8) is quite small compared with many other studies (e.g., cutoff zonal wavenumber 20 is used in Gupta et al. 2021), and it is possible that Rossby waves are not fully filtered out. One solution here is to apply an additional dynamical constraint (such as the one used in Wei et al. 2022), also with studying the sensitivity of fluxes/Ri to different choices of the cutoff wavenumber by changing it from 8 to 20. I hope that this concern could be addressed or at least discussed in the revision, and the related literature should be mentioned.

2. The robustness of the results caused by the model setup

As also mentioned in section 6 of the manuscript, ‘key processes such as convection were neglected and the representation of GW spectrum may be insufficient to fully capture the complexity of small-scale GW dynamics.’ For this reason, I have concerns on the robustness of the results caused by the model setup, especially with a relatively coarse horizontal grid spacing for explicit convection (no convective parameterization is employed). According to Table 1, ~20 km is the finest resolution available in this work, which is coarse for explicit convection. Given the important role of latent heating in GW generation, GW amplification and background baroclinic wave life cycles in these simulations, it is important that the authors make a stronger effort to show that their results are robust, and not due to excessive grid-scale latent heating. This could be achieved by (1) performing one simulation with a convective parameterization, and/or (2) performing a convergence test with double horizontal resolution.

3. Additional clarification

Many interpretations on the existing results should be clarified. A list of them is provided as below.

3a. Shear versus small-scale shear versus large-scale shear

In the current manuscript, the word ‘shear’ is often used for both small-scale shear and large-scale shear in the text, although their corresponding mathematical expressions are separated from each other. I think that it should be clarified in the text, otherwise it is quite confusing to the readers.

Also, the authors should also discuss the differences between the generation of the small-scale shear and the generation of the large-scale shear. For example, as far as I am concerned, the large-scale shear can be caused by the baroclinic instability, which is stronger in the moist environment. Also, the breaking gravity waves could also result in the large-scale background wind deceleration/acceleration. Finally, the large-amplitude gravity waves could directly lead to small-scale wind shear, which is generally the case in the current study (if not entirely the case, to the best of my understanding). It is amazing to find low Ri values over the extratropical lowermost stratosphere in such idealized simulations, mainly due to the above small-scale wind shear directly induced by large-amplitude small-scale waves (presumably gravity waves in authors’ opinions). However, the below two major questions should be discussed/answered.

Question 1: Which mechanism is responsible for those large-amplitude gravity waves? Are they convectively generated gravity waves? Or, are they similar to jet-front gravity waves in dry environment but largely amplified by the moist processes?

Question 2: Why is the small-scale wind shear so strong over the lowermost stratosphere?

Assuming that the small-scale perturbations are gravity waves, one naive explanation (if not the only) could be provided based on the wavenumber vector refraction equations in the gravity wave linear theory, which include the background wind term (associated with gradients of background wind) and the thermodynamics term (associated with gradients of buoyancy frequency and density scale height). When crossing the tropopause, the thermodynamics term (especially vertical gradients of buoyance frequency) could be so large that it becomes dominant and tends to shorten gravity wave vertical wavelength, as the case shown in Wei and Zhang (2015; section 5). Therefore, according to the definition in line 356 of the manuscript, the local vertical wind shear could be enhanced due to the dramatic decrease in vertical wavelength associated with the perturbations induced by gravity waves. 

3b. Low Ri caused mainly by the small-scale shear versus low Ri caused by both the small-scale shear and large-scale shear versus low Ri caused by local shear and weak N both induced by gravity waves

Following the above-mentioned point, low Ri could be caused by either the large-scale vertical wind shear or the small-scale vertical wind shear. However, according to the definition of Ri in line 380, full shear is used for the computation of Ri. It should be clarified which scale of the vertical wind shear contributes more to the formation low Ri.

In addition to local vertical wind shear, it is also possible that local N (or local potential temperature field) can be influenced by gravity waves. Please verify whether the formation of low Ri depends on the computation of N at different scales.

3c. Small-scale processes versus gravity wave processes

As mentioned earlier, the scale separation assumption between gravity waves and Rossby waves may not be valid over the upper troposphere and lower stratosphere (UTLS) region in midlatitudes. In order to verify this assumption, a commonly used method can be realized based on a decomposition of kinetic energy into divergent and rotational components. Please compare the energy spectra across different scales between divergent flow and rotational flow, especially over the small scale defined in the current study. I have concerns that only using the statistical approach is not enough over the interested region, and that it is necessary to also include a dynamical approach (e.g., extracting the divergent components of the winds by the Helmholtz decomposition technique).

3d. Gravity waves versus Rossby waves

In order to improve the readability of the paper, please search the word ‘wave’ over the entire manuscript, and clarify the type of each ‘wave’ mentioned in the text (e.g., replace it by ‘gravity wave’ or ‘baroclinic/Rossby wave’).

3e. The realism of the moist processes

In order to understand whether the moist processes are realistic in the idealized simulations, please provide more information on the associated meteorological quantities, such as the 1-h precipitation accumulation, the convective available potential energy, and the latent heating rate.

3f. The threshold/critical values for Ri, S, and any other quantity shown in the entire manuscript

The threshold value for the identification of low Ri with potential turbulence is much larger than the theoretical value (e.g., 5 versus 0.25). It is argued by the authors that a larger value is required for the resolution used in the current study. Please clarify exactly how the threshold value of low Ri is related to the resolution, as well as whether the results are sensitive to different threshold values. Otherwise, it will appear to readers that this value is randomly selected or tuned for the optimal results.

Threshold values for S are also different between dry experiments and other experiments incorporating physical processes, as mentioned in the manuscript. Additional clarification is necessary. Also, the above selected values are much lower than other studies based on ERA5. It is hard to understand why it is the case, as ERA5 is likely coarser than the ~20-km simulations in the current study.

In sum, all the threshold/critical values, including Ri, S, and any other quantity if not covered here, should be justified in the manuscript.  

3g. The definition of lowermost stratosphere

It appears to me that the lowermost stratosphere corresponds to the layer above the extratropical tropopause and below the tropical tropopause. Please provide addition clarification/justification on this.

Minor comments

There are some minor mistakes in the manuscript. I have collected a list of such mistakes, which can be found in the following message. However, I don’t think I could find every single one of them. If possible, please double check the entire manuscript. Also, I believe that some articles are misrepresented in the discussion, and I would also like to recommend some additional articles, which are very relevant to the current manuscript. Details are also listed in the following points.

1. Line 17 in the Supplement: ‘upto’ -> ‘up to’
2. In this manuscript (including the Supplement), both ‘Moist’ and ‘MOIST’ are used interchangeably. Also, the first name sometimes is misleading in the sentence. Due to this reason, I would suggest that ‘MOIST’ should be used in the entire manuscript (including the Supplement and the text shown in the figures).
3. Line 28 in the Supplement: What do you mean by “total moisture” here?
4. The second line in the caption of Figure S1 (as well as all the other parts in the entire manuscript): “northern hemisphere” -> “Northern Hemisphere”
5. The second line in the caption of Figure S1 (as well as all the other parts in the entire manuscript): “Logarithmic occurrence frequency color scale.” -> “Logarithmic occurrence frequency color scale is applied.”
6. The Supplement: Figures in the Supplement are not introduced in the manuscript. I think that it is better to include only the figures (as well as their captions) in the Supplement, and the corresponding discussion/introduction should be shown in the manuscript.
7. Line 20 in the manuscript: ‘jets’ -> ‘jet imbalances’ (Note: the differences between jets and strong wind shear should be briefly clarified here.)
8. Line 29 in the manuscript: ‘GWs’ -> ‘GWs,’
9. Line 31 in the manuscript: ‘temperature gradients’ -> ‘horizontal temperature gradients’ (Notes: the differences between temperature gradients and atmospheric stability should be briefly clarified here.)
10. Line 33 in the manuscript: This first sentence in this line should be improved. In this particular paragraph, it reads awkwardly and repetitively. I think that this information should be moved ahead as the first/second sentence of this paragraph.
11. Line 41 in the manuscript: Please quantify the criteria for the TSL based on S^2.
12. Line 64 in the manuscript: This definition is confusing to me. Why is tropical tropopause relevant over midlatitudes?
13. Line 87 in the manuscript: ‘are’ -> ‘which are’
14. Line 149 in the manuscript: I believe that ‘TKE’ is shown for the first time here in this draft, and the full name should be given, if this is the case. Also, a full name of ‘TKE’ is somehow provided in line 408 in the manuscript. Please consider providing this information (as well as all the other short names) as early as possible, in order to improve the readability.
15. Line 186 in the manuscript: What do you mean by ‘a third initial state’? Please clarify.
16. Figure 1: Bad contour design. It is hard to tell one field from another. Also, the dynamical tropopause and extratropical tropopause should be the same thing in this manuscript. Please clarify this point (or simply use either one of them throughout the entire manuscript).
17. Line 199 in the manuscript: ‘13’ -> ‘20’ (Note: inconsistency between this line and the table)
18. Lines 228-230 in the manuscript: I am not sure whether these two statements hold true. First, how to quantify whether the GW emission is less or more? Second, how to verify whether the results are more conservative or less conservative? Third, exactly how does fast growth rate of the baroclinic wave result in the so-called numerical, spurious features?
19. Line 233 in the manuscript: ‘wave breaking’ -> ‘baroclinic wave breaking’ (Note: the authors should check the entire manuscript and briefly clarify which type of wave is mentioned.)
20. Line 250 in the manuscript: ‘Plougonven and Zhang, 2013’ -> ‘Plougonven and Zhang, 2014’ (Note: Please double check the entire manuscript.)
21. Lines 254-255 in the manuscript: I am sure whether the work of Wang and Zhang (2007) is cited correctly. In Wang and Zhang (2007), several dry baroclinic wave idealized simulations are performed with varying baroclinic instability, in order to understand the sensitivity of mesoscale gravity waves to the baroclinicity of jet-front systems. Note that this comparison is done at the exact same phase of different baroclinic wave life cycles. However, in this manuscript, it is about the same baroclinic wave life cycle but at different phases.
22. Figure 4: It is hard to understand the discussion on this figure, since the wind/pressure field is not shown and it is hard to identify the location of ridge/trough.
23. Line 258 in the manuscript: Delete ‘sort of’.
24. Line 274 in the manuscript: ‘wave’ -> ‘waves’
25. Line 274 in the manuscript: ‘in the’ -> ‘in’
26. Line 275 in the manuscript: ‘occurrence’ -> ‘occurrences’
27. Line 276 in the manuscript: ‘11-km’ -> ‘11-km altitude’
28. Line 296-299 in the manuscript: Please add ‘(1) …, (2) …, (3)…’ after ‘including’.
29. Line 311 in the manuscript: How to make sure that those synoptic-scale waves are gravity waves (instead of baroclinic waves)?
30. Line 314 in the manuscript: I would suggest that the cited two references should be replaced by Wei and Zhang (2014) and Wei et al. (2016), since I think that the current references are cited incorrectly here. Neither of them is based on the study of simulated idealized moist baroclinic wave life cycles. The first paper cited in this line (i.e., Zhang 2004) is based on the dry simulations, instead of moist simulations. The second paper cited in this line (Zhang et al. 2015b) is mainly based on observations, instead of simulations.
31. The second line in the caption of Figure 6: What are the contour levels for absolute GW momentum flux?
32. Line 334 in the manuscript: What do you mean by ‘a vertical gradient barrier’? What is the specific definition here?
33. Line 351 in the manuscript (as well as all the other parts in the entire manuscript): ‘divergence’ -> ‘horizontal divergence’
34. Line 351 in the manuscript: ‘both are’ -> ‘they are’
35. Line 352 in the manuscript: ‘w’ as all other prime quantities here represent filter quantities.’ -> ‘As all the other prime quantities, w’ here represents filtered quantities.’
36. Lines 353-354 in the manuscript: What filter is used here? Spherical harmonic filter over the entire globe? Or the 1D FFT filter over each zonal direction with the cutoff zonal wavenumber at 8? Please clarify. Also, regardless of the filter method, the cutoff wavenumber appears to be rather low, compared with many published articles.
37. The equation in line 354 in the manuscript (as well as all the other parts in the entire manuscript): This equation, listed in a single line, should be numbered.
38. The equation in line 354 in the manuscript: It is not clear to me how the overline is computed. This information, as well as all the other procedures in the computation, is important, otherwise it will be hard for others to reproduce the results in the future. As a potential example, please check section 2d in Wei et al. (2022).
39. Line 359 in the manuscript: I am not sure about the expression of ‘divergence-convergence of vertical velocity’. It appears that they are treated as the same. Horizontal divergence and vertical velocity may be related, but they have different mathematical expressions with different units.
40. Line 385 in the manuscript: ‘We also regard’ -> ‘Following this idea, we regard’
41. Lines 389-390 in the manuscript: This is confusing to the readers. Do both the 3.5-PVU level and the 380-K isentropic level correspond to the feature mentioned here? Also, what do you mean by ‘the maximum potential temperature of the tropical lapse rate tropopause’?
42. Line 401 in the manuscript: Please double check whether the ‘S^2-S^2’’ is correct here.
43. Figure 9: I don’t understand why lines of ‘Ri=1’ are not shown in Figure 9a (upper and lower subplots).
44. The lower subplots in Figure 9 (as well as all the other parts in the manuscript): Please clarify whether S^2 or S^2’ is used in the computation of Ri. It appears to me that S^2’ is used here, which is different from the original definition of Ri.
45. Line 423 in the manuscript: ‘the the’ -> ‘the’
46. Line 424 in the manuscript: ‘between’ -> ‘among’
47. The second line in the caption of Figure 11: What do you mean by ‘pairs’?
48. Line 462 in the manuscript (as well as all the other parts in the entire manuscript): Are the ‘the sub-synoptic waves’ mentioned in this line gravity waves or Rossby waves?
49. 49: Line 462 in the manuscript: I think that there is an error in the printed text for the ‘N^2’’, with a redundant prime notation.
50. Figure 13a: For each vertical cross section plot, the corresponding line in the horizontal view (as well as the wave signals in the horizontal view) should be given.
51. The last two lines in the caption of Figure 13: ‘The zonal mean dynamical tropopause altitude is indicated by the dashed black line and tropical tropopause (380 K isentrope) by grey dashed line.’ -> ‘The zonal mean value of 3.5 PVU in the potential vorticity field is indicated by the dashed black line, and the zonal mean value of 380 K in the potential temperature field is indicated by the grey dashed line.’
52. Line 478 in the manuscript: ‘we will now explore in more detail’ -> ‘we will explore in the next section with more detail’
53. Line 481 in the manuscript: ‘and the potential’ -> ‘, as well as the potential’ (Note: there are two ‘and’s in the sentence.)
54. Line 485 in the manuscript: ‘tropopause following coordinate’ -> ‘the tropopause-following coordinate’
55. Line 487 in the manuscript: ‘occur’ -> ‘are’
56. Lines 491-492 in the manuscript: It is hard to follow this sentence.
57. Line 493 in the manuscript: I am not sure why threshold values are different between dry runs and other runs incorporating more complex physical processes. I think that it is better to keep them consistent.
58. Line 519 in the manuscript: ‘due’ -> ‘by’
59. Line 525 in the manuscript: ‘vertical wind shear and potential turbulence and their contribution’ -> ‘vertical wind shear, potential turbulence, and their contribution’
60. Line 542 in the manuscript: This is not a new paragraph. Please remove the redundant blank space in the previous line.
61. Line 552 in the manuscript: ‘the breaking of synoptic scale wave’ -> ‘the breaking of synoptic scale baroclinic wave’
62. Please consider citing the work of Zhang et al. (2015a), which has investigated the UTLS GWs associated with the jet streak observed by the aircraft measurement.
63. Please consider citing the work of Plougonven and Snyder (2007), which has compared GW characteristics between different baroclinic life cycles.
64. Over the entire manuscript (including the figures): ‘pvu’ -> ‘PVU’

Reference

Gupta, A., T. Birner, A. Dörnbrack, and I. Polichtchouk, 2021: Importance of gravity wave forcing for springtime southern polar vortex breakdown as revealed by ERA5. Geophysical Research Letters, 48, e2021GL092762. doi: https://doi.org/10.1029/2021GL092762

Plougonven, R., and C. Snyder, 2007: Inertia–Gravity Waves Spontaneously Generated by Jets and Fronts. Part I: Different Baroclinic Life Cycles. Journal of the Atmospheric Sciences, 64, 2502–2520, doi: https://doi.org/10.1175/JAS3953.1

Plougonven, R., and F. Zhang, 2014: Internal gravity waves from atmospheric jets and fronts. Reviews of Geophysics, 52, 33-76, doi: https://doi.org/10.1002/2012RG000419

Wei, J., and F. Zhang, 2014: Mesoscale Gravity Waves in Moist Baroclinic Jet–Front Systems. Journal of the Atmospheric Sciences, 71, 929–952, doi: https://doi.org/10.1175/JAS-D-13-0171.1

Wei, J., and F. Zhang, 2015: Tracking gravity waves in moist baroclinic jet-front systems. J. Adv. Model. Earth Syst., 7, 67-91. doi: https://doi.org/10.1002/2014MS000395.

Wei, J., F. Zhang, and J. H. Richter, 2016: An Analysis of Gravity Wave Spectral Characteristics in Moist Baroclinic Jet–Front Systems. Journal of the Atmospheric Sciences, 73, 3133–3155, doi: https://doi.org/10.1175/JAS-D-15-0316.1

Wei, J., F. Zhang, J. H. Richter, M. J. Alexander, and Y. Sun, 2022: Global Distributions of Tropospheric and Stratospheric Gravity Wave Momentum Fluxes Resolved by the 9-km ECMWF Experiments, Journal of the Atmospheric Sciences, 79(10), 2621-2644. doi: https://doi.org/10.1175/JAS-D-21-0173.1

Zhang, F., 2004: Generation of Mesoscale Gravity Waves in Upper-Tropospheric Jet–Front Systems. Journal of the Atmospheric Sciences, 61, 440–457, doi: https://doi.org/10.1175/1520-0469(2004)061<0440:GOMGWI>2.0.CO;2

Zhang, F., J. Wei, M. Zhang, K.B. Bowman, L.L. Pan, E. Atlas, and S.C. Wofsy, 2015a: Aircraft measurements of gravity waves in the upper troposphere and lower stratosphere during the START08 field experiment. Atmos. Chem. Phys., 15, 7667-7684, doi: https://doi.org/10.5194/acp-15-7667-2015

Zhang, Y., S. Zhang, C. Huang, K. Huang, Y. Gong, and Q. Gan, 2015b: The interaction between the tropopause inversion layer and the inertial gravity wave activities revealed by radiosonde observations at a midlatitude station, J. Geophys. Res. Atmos., 120, 8099–8111, doi: https://doi.org/10.1002/2015JD023115

This study investigates how gravity waves, emerging during baroclinic life cycles, influence vertical shear and potential turbulence in the lowermost stratosphere, contributing to tracer mixing and the formation of the extratropical transition layer. Using ICON model idealised experiments with varying resolution and physical complexity, the authors show that GW activity is strongly linked to model resolution and is amplified by moist processes, primarily due to latent heat release. These findings underscore the key role of GWs in shaping dynamical and mixing processes in the LMS. 

I find the scientific results highly relevant and of considerable interest.  However, I recommend a major revision of the manuscript to improve clarity, resolve potential conceptual issues, and enhance the robustness of the results. Below, I provide major and minor comments intended to support the authors in refining their study.

Major comments:

1. Idealized Setup – Scope and Limitations
   
   While idealized experiments offer a controlled framework to isolate and study specific processes, the limitations of such an approach should be acknowledged in the introduction. I encourage the authors to elaborate on the potential constraints of transferring these results and conclusions to real-case simulations.
2. Resolution and Model Configuration
   
   The chosen in the study domain with hight of 35 km may be sufficient for UTLS-focused analyses. However, the interactions of GWs with large-scale circulation higher in the stratosphere are likely underrepresented. Additionally, it should be noted that GW and convection parameterizations are not included in the coarse resolution runs (e.g., Δx = 80 km), where such processes are arguably unresolved but highly relevant. Therefore, in my opinion, conclusions drawn from these runs—particularly concerning the absence of GW activity—is to be expected.
   
   
   
   I suggest the authors explicitly discuss these limitations and, if possible, include sensitivity tests with GW and convection parameterizations enabled as well as one test  case with higher model top. Such inclusion could refine the understanding of the processes of relevance such as vertical momentum transport, and resulting shear evolution in coarser resolutions.

3. Figure Clarity and Presentation
   
   

   Several figures would benefit from clearer layout, consistent formatting, and improved labeling:

   • Figure 1: Consider splitting into two panels—one showing θ and the other q fields.
   • Figure 2: Maybe it worth to add marked zones for a particular feature on the figure and refer to them in the description for the better understanding
   • Figures 3–4: Unify altitude labeling and fix overlapping x-axis ticks.
   • Figure 6: The occurrence of shear is not visually clear. Consider using colored lines (e.g., red) for better contrast and increasing font/line size
   • Figure 7: Consider moving 7a to the appendix.
   • Figure 10: Note the change in y-axis scale for different cases (dry vs. moist).
   • Figure 13: a/b panels depict different altitudes. If the discussion centers on the UTLS, consider extending the altitude to 22 km. It seems that figures for model time of 288 and 312 h would exhibit some features above the 18-20 km, which might be of relevance. The figures might also benefit from cropping Ox to 15–75° longitude.
   • Figure 14: Remove the 264h panel from 14e for consistency.

    

   Minor comments and technical suggestions:

• Lines 37–52: The introduction could benefit from a more quantitative framing (e.g., order-of-magnitude estimates of GW-induced shear/turbulence) and acknowledgment of uncertainties or active debates (e.g., resolution sensitivity or parameterization limitations).
• Line 23: "ascend” -> ascent
• The introduction largely describes the importance of GWs and related phenomena without discussing potential challenges or uncertainties in the field. A brief mention of existing debates or challenges in studying GWs (e.g., model resolution limitations or uncertainties in parameterization) could provide a more critical perspective.
• Line 29: Fix spacing in “(UTLS)(e.g., …)”
• Line 90: Add commas around “which are quasi-periodic”
• Line 128: Remove “so-called”; reduce ICON technical details and avoid referencing polar grid issues in idealized simulations
• Table 1: When referring to the resolution R03B07, horizontal grid spacing is Δx = 13 km
• Line 210 and thought the text: Unify case labels (“Moist” vs “MOIST”)
• Line 223: Replace “after the model starts” with after the simulation time
• Line 227: Does that mean that the definition of the dynamical tropopause is taken from the cited literature? It would be better to reformulate the sentence for clarity.
• Line 232: Please consider rephrase it in passive, for instance: Differences are observed in the size of the PV streamer…
• Line 240: Suggested rewording: “Wave activity was not prominent before the indicated simulation time…”
• Figure 3 caption: Clarify as “model integration time”; please remove hyphen from “11 -km”
• Line 270: Use the abbreviation  UTLS
• Line 272–276: Clarify whether observations refer to a specific case or general result; re-order figure reference
• Line 287: Replace viz. with i.e. or namely for clarity
• Line 334: Consider replacing “air parcel” with air masses, since it is a description of a physical process and broader term would be better suited. 
• Line 343–344: Suggested rewording: “We have shown that GWs emerge under various initial states, grid resolutions, and process complexities.”
• Line 352: Avoid starting a sentence with a symbol; rephrase
• Lines 374–375: Combine into one clear sentence (e.g., “We focus our analysis on strong wind shear and static stability (N²), with emphasis on GW-induced shear and potential turbulence in the LMS.”)
• Line 376: Replace parcels with masses
• Line 379: Include the formula for the gradient Richardson number alongside the non-dimensional form for clarity
• Line 384: Phrase “on the resolution used in this study” seems misplaced—restructure for coherence
• From Fig. 6 it seems to me, that the GWMF is not overlaping with the shear occurrence  in “stream” case. Is there an explanation for such behaviour? 
• Line 392: Define S’ (small-scale shear) again, as the earlier mention is far removed
• Figure 8: Consider separating panels into different figures or moving higher-res versions to the appendix
• Line 395: Rephrase/remove “right side of the distribution” for clarity.
• Line 396: Reword for clarity: what is the comparison baseline for “larger S² values”? I am struggling  to understand the discussion, therefore clarifying the paragraph is required.
• Lines 401–410: Add explicit figure references to help the reader follow the analysis
• Line 411: “On smaller scales and in instantaneous considerations” does it refers to the instantaneous outputs? 
• Line 415: Clarify whether turbulence rarity refers to model output or general atmospheric behavior. Cite observational studies.
• Figure 10: Is there any explanation on higher S’2 in the case TURB Moist for N2 close to 0 (Fig.10e lower panel)? Could you please elaborate, wether it is connected to the  gap in high S2 occurrence  with small N2 (Fig.10e upper panel)?
• Line 420: Suggested rewording: “Dynamic instability becomes likely when Ri ≤ 5.”
• Line 440: The values of shear were also shown on Figs. 7,8. Indicating same situation, lower values for dry cases and 10 times larger S2 values for moist cases. Please, refer back to previous figures (7, 8) where similar shear behavior is present but not discussed.
• Lines 483, 485: Replace “exceedance” with “exceeding a defined threshold”
• Line 511: Clarify whether “TSL occurrence across sensitivity experiments” refers to figures or broader results
• Line 550: Use plural: GWs