Summary:

The authors utilize measurements from a 26-day glider deployment, complemented with satellite products, to investigate how internal tides modulate mixing, nutrient availability, and primary production in the vicinity of the shelf break offshore of the Amazon River mouth. The results suggest that internal wave-driven vertical mixing drives variability in the ocean state and vertical distribution of chlorophyll over the deployment.

Merit:

This paper utilizes glider data to explore how physical processes modulate the vertical distribution of chlorophyll. I think that this work on the interdisciplinary applications of the physics would be of interest to many readers. The approach is generally sound, although additional detail and discussion is needed in places as commented below. The presentation quality and structure is mostly clear, and any points of confusion are noted.

General comments:

1. The results focus on a small area where it is known that internal tides have a significant influence on dynamics/mixing, termed a “hotspot” by the authors. I think something more needs to be said regarding the spatial distribution of such features; that is, whether the observations represent an extreme case or are typical. That might help clarify some of the implications of the work, e.g., whether internal tides are a key driver of variability as mentioned on line 39-41 in the abstract.
2. I think there needs to some more discussion regarding the separation of spatial and temporal variations in the glider data. That is, inherently a glider that moves in space will capture variations in both space and time but without additional context it will be unclear which is more important. There are related elements already in the text; e.g. the discussion of eddy evolution and the location of the segments relative to the position of the eddy. But, I don’t see any explicit mention of it. I think that is needed, even if the aliasing turns out to be minimal. Some discussion of how diurnal-weekly-monthly temporal variations, and the impacts on the observed spatial variability, would improve the manuscript.
3. I think some of the information provided in the methods section is not sufficient for the results to be reproducible. I have mentioned a few places where I think specific details are needed in the comments below.
4. No direct turbulence or mixing estimates are used in this paper. While I do not think this is a problem, I think it should be clear earlier in the manuscript. Much of the language in the abstract/intro/early sections attributes changes to vertical mixing, which may be (likely is) the case but is not shown directly in the paper. I would recommend a careful edit of these sections so this is clear to the reader. Related to this (see my comment for L518), it is implied that vertical mixing is entirely a result of internal tides. While possible alternate contributing factors are clearly mentioned in the discussion, I think it would be helpful if it were mentioned earlier before presenting the results.

Line-by-line comments and suggestions:

L26-27 – I think this sentence is unnecessary. It is already stated later that they do modulate nutrient availability/productivity.

L33 – “remarkable” compared to what? Please clarify

L36 – clarify what contributes to the other 62%

L55 – This sentence feels a bit disconnected; discuss how it influences climate variability, i.e. through air-sea interaction.

L96-97 – I think it would be helpful to add a sentence/references regarding the seasonality of internal tides and mesoscale features.

L111 – clarify that this is in optimal conditions with no currents

L116 – change “thanks to” to “from” or “using”

L117 – strange wording. Reword “enabling to estimate”

L139 – change “imagery” to “images”?

L153 – extra space after 05

L157 – “merges”

L177 – the URL could be moved to a data statement at the end

L194 – What specific hydrographic properties were used to classify the data into these periods? Was this done objectively?

Fig 1 – On a related note, there seem to be breaks between periods A&B and B&C. Are these transitional periods? Why were they not classified into any of the primary subregions?

L204 – How was the aggregating done? Is it assuming that every measurement within that depth range is treated the same? Or, was there some type of vertical averaging?

L210 – I’m curious how large of a contribution is expected from the SMS term? Is this a source of uncertainty?

L226 – How are high and low tidal forcing defined?

L233 – “integrated in DCM at the DCM” – I don’t understand what this wording means. I think you mean integrated in depth within the layer.

Fig 2 – Nice schematic that shows how Chl changes vertically due to internal tides. I think the colors are somewhat ambiguous. It is unclear whether green refers to a) the sum of CHL and SMS or b) just Chl-a from SMS.

L254 – Would a Spearman correlation analysis potentially be more appropriate, considering that I think we would not expect a linear relationship?

L261 – missing space after the period

L268 – I disagree with this… it looks to me like euphotic depth Zeu decreases in the eddy core and increases on the eddy periphery, in a similar pattern to chlorophyll as described in the later text.

L277/279 – 11th / 12th

L277-280 – I’m not convinced there was “expansion” of the eddy. That seems, from the figure, to be an artifact of the cutoff ADT used to define the edge. Please reword to say that (or clarify if I am mistaken).

L288-300 – Following my previous comment, it looks like Zeu and chlorophyll are correlated within the eddy, but that this correlation seems to break down when outside the eddy. I think an explanation of this would be helpful.

L336 – Fig 6 appears to show that salinity was always above 35.5

L333-352 – Nice summary. Much of the discussion on stratification is descriptive, however, and some of the trends mentioned in the text are not clearly apparent on the figure. For example, I do not clearly see more salinity stratification in region A than B, as is mentioned at L342. I think including quantitative information in a few places (i.e., dT/dz and dS/dz) would strengthen this section.

L365-378 – The answers to some of my earlier comments are here. I think, perhaps, this should be moved earlier. I.e., discuss the four periods, then discuss their differences?

L368 – I think better to use 3 significant figures to be consistent here and in other places for the isopycnals

L371 – “a distance was recorded” – odd wording; please rephrase

Fig 8 – Add units on the y-axis (& for Fig 13). Also, it seems strange to me that the spectra are so smooth (or, perhaps I am mistaken). Was any smoothing done to the lines on this plot? If so, I would suggest to just plot the raw spectra.

L398-408 – It seems from the earlier plots that there is strong variability in surface chlorophyll. But this is not clear from Fig 9. Please explain this apparent discrepancy.

L419 – Odd wording. Maybe say “the peak is more pronounced”?

L422 – Was there significant temporal variability in the chl-a profiles? If so, perhaps a proportional criterion for thickness might work better?

L425 - While the relationship between thickness and high/low internal tide activity is very clear, I’m less convinced about the relationships between thickness and chlorophyll within the two IT regimes. It seems from Fig 11 that the high R values are because of peak thickness varies by much more than delta CHL, rather than a large change in chlorophyll. As suggested earlier, I think calculating a Spearman ranked correlation coefficient might be more appropriate, and would tell whether high values of Chla are associated with low values of thickness.

L428-430 – I think this is probably a stronger conclusion than the correlation coefficients (and is more clear in Fig 11). Maybe move earlier in the paragraph?

L447 – I’m a bit confused on how “chlorophyll-a loss” is calculated. From Fig 12, it does not look like the decrease in Chl at the peak is as high as 64%. Please clarify.

L458 – Is there any SMS contribution to the DCM layer? I assume not based on the calculations in this paragraph.

L470-481 – nice summary of the differences between A and B.

L493 – extra space between “ability”

L518-524 –I think it would be useful to try to contextualize this more with existing literature – i.e. are there papers quantifying the impact of NIWs and fronts on chlorophyll. If not, are there any that have quantified physical turbulence parameters relating to these issues? I think having some additional background is important here, considering that the paper is based off of an implied assumption that the entirety of vertical mixing results from internal tides (which may be mostly true, but it would be helpful it this was put in context).

L575 – I’m not sure about the specific journal policy for this special issue regarding whether having data available upon request is acceptable.

Thank you for this opportunity to review this paper. This study investigates the impact of internal waves on a subsurface chlorophyll structure observed during a 26-day log glider deployment, complemented by satellite data. The manuscript presents a very interesting dataset and a compelling effort to explore the relationship between Chl-a concentrations and internal tides. However, several key elements in the methodology and interpretation of the results required further investigation and clarification. In particular:

1. Definition and identification of ISWs: I believe the introductions need more context and explanation of what internal solitary waves (ISWs) are and how they differ from internal tides. Mostly because ISW is a big part of the results and I believe there is some lack of clarity on how they are identified in the glider data. Do they have a different mixing diffusivity value compared to the tides? How do they relate to the separation of high tide vs Low tide analysis?  In the results, the identification of ISWs—particularly in glider and satellite data—is unclear and inconsistent.
2. Assumptions about mixing and chlorophyll: A central conclusion of the paper is that differences in chlorophyll concentrations between high tide and low tide are due to physical mixing, but this assumption is not entirely justified in the methods and excludes potential biological processes within the DMC. I think the paper still has good results, but without turbulence or mixing data, the inferred mechanisms require stronger connection to prior work or clearer acknowledgment of uncertainty. 
3. Glider data processing and resolution: The methods section lacks detail on how glider data were interpolated, gridded, or treated before spectral analysis. Details about dive depth, vertical resolution, and time-series construction are critical to evaluating the strength of the results. This is particularly important for the spectral analysis
4. Justification of assumptions and definitions: Further justification and clarification of how key periods, depths, structures, and thresholds are defined throughout the study is needed to strengthen the interpretation of the results. 

Overall, I think this work has great potential to contribute to the literature of the region, but it needs major revisions to improve its readability and impact of its results. Below I describe in detail major comments and minor comments:

Major Comments:

Lines 47-52: The introduction of the ISW theory might need some work. The acronym is used before explaining what it is, and these sentences appear out of order. SWs are mentioned frequently throughout the paper, so it would be helpful to include more background here—how they are generated and how they differ from internal tide

Lines 115-124: Throughout the study, there were different ways of using the glider data (surface comparison with the satellite, spectral analysis etc), which I think is excellent, but it's not clear from the methods how the data were interpolated (if it was) or gridded.  Also, what was the maximum dive depth? Later, it’s mentioned the glider does 12 profiles per day, with 2 hours per profile (Line 203), suggesting it’s not reaching 1000 m. More detail on glider operations would help readers understand the interpretation of the data analysis 

Line 233: The assumption that differences in chlorophyll a between high and low tide are due solely to mixing needs more support. What are the limitations of this assumption? Does this imply ΔSMS_dcm = 0? Since turbulent mixing was not measured, it would strengthen the argument to connect with prior work from the region that documented internal wave-driven mixing or estimated diffusivities consistent with your interpretation. Including possible mechanism (shear-driven turbulence? ) 

Figure 2:  The diagram is hard to interpret. There is no context for why CHL_LT shows a larger peak than CHL_HT. After reading the results, this becomes clearer, but at this point is hard to follow the logic. Why are there two green lines?

Line 279-280: Is this growth of the eddy observed here typical this region? The speed in which it grows appear fast, but I am not be familiar with eddy activity here. 

Line 315-317: The identification of ISWs in Figure 5d is unclear. Are these timestamps of whent hey are observed in the glider or satellite data?  If satellite, how is timing assigned? ? There also seem to be solitons near the spring-neap transition, which complicates the assertion that ISWs align with spring tides. This relationship and its time scale need further clarification—maybe add more context in the introduction.

Table 1: Figure 5 seems to show two crests on September 9—was a height threshold used to identify crests?

Line 370: The phrase “well-defined T/S stratification” needs clarification. Do you mean stronger or weaker stratification? Is it more linear? Or does it refer to T and S both increasing or decreasing with depth?

Line 371-373: I think Period C seems to be fresher than B within the 24 –24.8 mass? 

Line 386: There seems to be an assumption that ISWs coincide with tidal peaks—but this is not apparent in Figures 5 or 6. For instance, an ISW is labeled on 13 Sept, but no large oscillation is visible. Also, which peaks are being referenced? (See earlier comment about identifying ISWs.)

Line 386–387: The drop in surface temperature during spring tides (sections A and C) could be due to other causes—e.g., position relative to NECC or eddy edges—rather than tides alone.  This sentence seems to imply that the tides drive this drop in temperature, but is this through mixing? Or another process? 

Line 388: How was the glider data used and prepared to create these FFT? Were they interpolated to a uniform time series? 

The sentence “A Fast Fourier Transform (FFT) analysis of isotherms (145–165 m) confirms the semi-diurnal modulation of these oscillations” is unclear in its current form and would benefit from further clarification.From the results, I'm inferring that the FFT is examining the variability of vertical displacement of an isotherm, not the variability of temperature at a fixed depth. Is this correct? Maybe adding units to the spectrum figure will also help clarify this.  was some form of averaging or stacking performed across this depth interval that makes the plot so smooth?  How was the glider data prepared for the FFT? Was it interpolated to a specific depth? Was it bin averaged? How would this impact your results? A more precise description of the methodology—especially the variable being spectrally analyzed and how it was derived—would greatly improve the reader’s ability to interpret the results and evaluate the evidence for semi-diurnal modulation.

Line 448: Could changes in DCM chlorophyll be due to biological responses, not just physical mixing? This relates to the concern above about the mixing assumption. The equation on line 454 is also unclear and needs more explanation

Line 474 -475:  The phrasing is confusing: “deeper, less dense” or “upper, denser”? Clarify what part of the eddy is being described. Additionally, the reference to McGillicuddy et al. (line 478) requires more context. Greater depth compared to what?

Lines 482-488: I think these results should be added in the section of the results where the authors do the spectrum analysis. Its presence here is unexpected and underdeveloped. Maybe other questions can be answered from these distinctions: why is it important to distinguish between these two types of oscillations (wind forcing, length scales, etc)? Have other papers discussed these differences, and do the results agree with your findings? Also, how was the spectrum in Figure 13 produced? The same as Fig. 8 but longer time series? What is the error bar, How many spectra were averaged, and what are the error estimates?

Is there any filtering applied to the data? Are they the same depth as Fig 8? 

Line 504-416:This ecological context is appreciated and very usefull—perhaps connect it more explicitly to the tidal vs. near-inertial forcing context in terms of timescale? 

Minor comments

Line 97: Add more information about why Sep and Oct 2021 were an optimal period for IT activity

Line 214: A closing parenthesis is missing from the equation.

Line 217-219: If previous studies used a similar derivation for these equations, please cite them.

Line 233: The terminology DCM (ΔDiff_DCM) is not clear to me, i suggest explaining what Diff(DCM) means. 

Line 267: Add reference to figure 3e-h

Line 421: Why was 0.2 mg/m³ used as the threshold for chlorophyll peak thickness?

Suggestions and minor questions

Line 79: Consider referencing Figure 1 to help the reader visualize the study area. 

Line 336: Is there a specific reason why you use 35.5 as the euhaline threshold? As someone unfamiliar with this region, this seems a high threshold. 

Line 338: I suggest referencing the black lines in Figure 3a when describing the cross of AE1