In abstract: These findings refine our understanding of mantle dynamics and lithosphere-asthenosphere interactions in the Zagros collision zone.

This is rather generic statement. Authors must emphasize their findings on what new tectonic-geodynamic concluding remarks this study brings in the fragment of the research.  

Moreover the abstract and introduction sections lack a scientific rationale, which is essential for the study. The authors must provide this rationale as the main motivation, explaining why they initiated the study in this region. That is to say, the significance of studying seismic anisotropy and its role in elucidating the remaining portion of the puzzle must be examined explicitly.

“In addition to asthenospheric flow, we also consider the possibility of “frozen” anisotropy, inherited from the study region’s tectonic history as part of the northern Gondwana landmass.”

This is a qualitative argument but is required to be proven by some advanced sophisticated modelling techniques that can enable to resolve actual orientation and type of symmetry (hexagonal, orthorhombic, etc) of the “frozen fabric” if exists.

So a total of 3256 records were initially selected and following data quality criteria, the final data set was including those with 155 non-null and 630 null. Can you also please enlighten us how many earthquakes you have selected at the beginning and how many out of the total event number you obtained in the end.

Line#97: “ … (5) at least a 50% reduction in energy on the transverse component after anisotropy correction … ”

I suppose this minuimum threshold for tangential energy is still high. What is your argument? Do you loose too many events if you increase the reduction threshold to for instance 70-80 and more over? How do you justify the estimated anisotropy if you can only correct the half of the energy related to anisotropy?

Lines# i.e. 102 or 104: change Sh to “SH”

The authors employ a conventional approach to splitting detection and measurement, utilizing the cross-correlation technique. According to my recollection, some early works (e.g., Vecsey et al., 2008) identified three known methods for solving the aforementioned problem. These three methods are eigen value, cross-correlation, and minimum tangential energy. The latter method has been shown to provide more robust and stable solutions than the other two methods based on several noise-free or -added numerical tests. Indeed, the sensitivity of distinct methodologies varies in response to specific conditions, including data noise and the presence of unknown sedimentary effects. Therefore, a single method may not always guarantee this simple diagnosis of seismic anisotropy. It is recommended that two different approaches be used in conjunction with minimum energy, as well as the cross-correlation or eigen method. The optimal splitting parameters from the source-receiver cases, where there is observed to be overall consistency between at least two different methods, should then be determined.

How do you estimate uncertainty for each single measurements? Describe the approach in the a separate paragraph of method section?

Lines# 119-120: “These spatial variations suggest that the observed bimodal pattern of fast-axis orientations primarily results from lateral rather than vertical heterogeneities in the anisotropic structure.”

This appears pretty much interpretative within a section where you share your Results quantitatively. If so this has to be covered in its fine-details with supporting arguments from other previous/recent seismic tomography, receiver functions, or any geochemical, mineralogical-petrological constraints.  

Lines# 162: “This consistency suggests a relatively simple and coherent anisotropic structure beneath the study region.”

I think this is one another interpretative statement of the Results. In general Results section must be the place where you can only presents your anlysis results in a quantitative and objective way. Please revisit your Results section to account for this fact.

The present work reports a large amount of null measurements compared to non-null ones. But at the same time we see that authors are not using the information from such large null measurements, even such that, larger than the number of good splitting cases for supporting their geodynamic interpretation too. It is unfortunate, even, we are not provided any information or discussion, specifically on from what type of special cases these null-splitting cases were observed, i.e., whether they are classified as null due, i.e., i) to very small delay time or ii) to the fact that pattern of cross-correlation coefficient obtained after a systematic grid search of the pairs of splitting parameters was implying a null solution most likely stemming from the azimuth of the analyzed event aligning with possible fast or normal to slow axis orientation of anisotropic structure beneath the station of interests. In case when the former observation is more valid for the null cases then this must have various reasons including i.e., isotropic nature of lithosphere, or more complicated anisotropy (e.g. possible double-layer of anisotropy in the simplest manner) characterized with orthogonal fast wave azimuths in each layer that can cancel out the effect of overall anisotropy. In overall I would like to see an in-depth discussion that are enriched specific visual data examples of null-measurements (thus this requires additional figures) and its implications on past/present geodynamic history of the region within a specific sub-section in the Discussion.

Table 1: Errors fort he splitting parameters are required in this table.

Fig. 5: What type of interpolation technique are you using. In the figure some unrealistic geometrical (rectengular shaped or triangular) relatively large or small delay time zones are noticeable that I am not sure how realistic these zones are.

Fig.7: Concerning my comments on null-splitting measurements above, I wonder if there is any systematic correlation beween LAB shown in Fig. 7d and null-splitting examples.

General comments

This manuscript presents new azimuthal anisotropy measurements in Iraq and the Persian Gulf, from splitting of core phases. These data are integrated with a very large set of measurements of the same type on a broad regional scale, on the Arabian plate, in Iran and eastern Anatolia, to confirm or refute the hypothesis that this anisotropy, supposedly linked to asthenospheric flow, documents a deviation of the general SW-NE flow by the asthenospheric keel under the Zagros.

At least, that's what I think is the main aim of this work. Unfortunately, the scientific objectives are not clearly stated in the introduction. It is therefore difficult to understand what these few new data contribute to our understanding of the general dynamics of the Arabian-Eurasian collision. The final discussion is confusing and convoluted. It could be better structured around a few key objectives, if they were mentioned in the introduction. The size of the maps varies from one figure to another, from perfectly focused on the region studied (ex. Fig. 4a, Fig. 7), to intermediate (Fig. 4b), to broad regional scale (Fig. 6). These changes in scale don't make the discussion any easier to understand. These are my main concerns about this manuscript, which in my opinion requires major revisions before it can be accepted for publication.

Specific comments (including detailed comments related to the concern described above on the aims and discussion of results)

I did not list all the comments and questions I have on the discussion part. The best would be to completely re-structure and re-write it to make it clear and easy to follow. It could also be shortened and better focussed. Please avoid obvious statements such as "the lithospheric root causes substantial variations in lithospheric thicknesses" (l. 223).

- Abstract: why is it important to have more measurements in the foreland of the Zagros? This should be explained already in the abstract. The last sentence is also very vague.

- Introduction: rather than starting the introduction with explaining the use of seismic anistotropy, you should explain what your study aims at. The aim cannot be only to provide the first measurements of mantle anisotropy in this region. You should consider adding in Fig. 1 a map of available  shear-wave splitting measurements at the regional scale of Arabia-Eurasia collision.

- l. 63: you mention "the thick lithospheric root" but references are missing; is this a widely accepted observation?

- Fig. 1: I cannot see the red dashed line. Scale of APM arrows missing.

- Fig. 3: what are the grey sectors? Could you add the numbers of non-null and null measurements at each station on this figure?

- Results section: in l. 113, you start commenting the non-null measurements at a number of stations based on Fig. 3, but you don't comment the null measurements: are they compatible with the non-null? Do you use them as quality assessment of the non-null? What about the stations which only have null measurements (ex. SAM1, NSR3, KAR2 which is discussed in l. 130 but too late..)?

- l. 134-137: is the difference in average splitting time between 0.82s and >1s statistically significant? The map of Fig. 5 documents this difference, but explanations on how it is computed are missing.

- l. 162: I understand that you conclude that the anisotropic structure is simple because the projections of the fast-velocity vectors to different depths are consistent (Fig. 6). What do you mean by simple? A single anisotropic layer? The consistency of the projections to different depths is not surprising because the projection only spreads the measurements. I don't understand the reasoning.

- l. 167: you only show Eastern Anatolia and not the whole of it.

- Fig. 7 should show the entire regional area and not only the Zagros foreland.

- l. 169: by "correlation" do you mean "coherence with APM"?

- l. 171: what is your definition of the Northern Middle East? Your study region would be more precisely described as the Arabia-Eurasia collision zone along the Zagros.

- l. 175: which correlation?

- l. 184: the aligment with APM suggests a coupling between the surface (where the APM is measured) - not the lithosphere - and the asthenosphere.

- comparison with Pn anistropy: Fig. 7c does not reveal different anisotropic patterns but coherences and inconsistencies between Pn velocity anisotropy and SKS anisotropy. No scale of Pn anisotrpy is shown in Fig. 7c. Is it significant?

- l. 192: when you know that the lithosphere is thin, you don't need to compare to Pn to state that the lithophere has a negligible influence on the total anisotropy. The asthenospheric origin of SKS anisotropy is now widely accepted, isn't it?

- l. 196: what do you mean by "complexity of this tectonic region"? The APM vectors rather document a simple pattern.

- l. 198: "unaffected" by what?

- l. 198: what do you mean by "post-collisional tectonics"? The Zagros collision is still ongoing.

- l. 204: what do you mean by "behind a lithospheric root"? According to Fig. 7d, these measurements are located in the thick lithosphere region.

- l. 205-208: the circular mantle flow is not visible in Fig. 7d, which is too zoomed. If the mantle flow turns around the keel, there should be no asthenospheric flow beneath the keel. Can you plot the extent of the keel in the Fig.? Fig. 7d shows abrupt changes in fast-velocity directions between the Mesopotamian Foredeep and the region of the Zagros suture. How do you explain them?

- l. 286: "..the first evidence of such rifting effects...": rather a hypothesis than an evidence.