Prasad Lahiri et al.  employs the use of a coupled ocean-atmosphere regional model (ROMS + WRF) to examine processes contributing to the mini warm pool in the Arabian Sea. They examine three events of the warm pool in their model and attempt to determine the relative contributions between ocean and atmospheric processes driving the strength and dissipation of these events.

While I find the concept of the study particularly interesting and potentially a good contribution to literature in the future. Nevertheless, significant revisions must be made before this manuscript can be reconsidered for publication.

As detailed throughout the comments below, there is a need to restructure the manuscript text in general to make it clear and concise. There is an extreme overuse of conjunctive adverbs such as “moreover”, “however”, “nonetheless” and many others that is in several cases is erroneous. There are missing references in several parts. The model description and validation are lacking. There are also several statements throughout the results section that do not appear to be supported by the figures. For example, the provided plots qualitatively comparing with a buoy do not support statements that the model compares well with the buoy data. Second, the statement on line 296: Figure 8f shows that the net surface heat flux is the dominant term driving the heat tendency with contributions from vertical processes remaining largely the same throughout the time series. It is my impression that several of the comments below can be addressed with a thorough revision of the text.

1. Section 2.2: I find the description of the model components lacking and insufficient. For example: no information is given on the time-step of each component, no information is provided on how the open boundary conditions are specified except for the datasets, the horizontal advection scheme used in ROMS, and other important configuration details.  Furthermore, the authors jump back and forth describing the model components which is quite confusing. I’m also curious about the selection of nested domains that are not fully overlapping each other between the components (WRF domain 2 does not fully overlap with the ROMS domain). See the references below for examples on complete model descriptions:
   1. Olabarrieta, M., Warner, J. C., Armstrong, B., Zambon, J. B., & He, R. (2012). Ocean–atmosphere dynamics during Hurricane Ida and Nor’Ida: An application of the coupled ocean–atmosphere–wave–sediment transport (COAWST) modeling system. Ocean Modelling, 43, 112-137.
   2. Castruccio, F. S., Curchitser, E. N., & Kleypas, J. A. (2013). A model for quantifying oceanic transport and mesoscale variability in the Coral Triangle of the Indonesian/Philippines Archipelago. Journal of Geophysical Research: Oceans, 118(11), 6123-6144.
   3. Ross, A. C., Stock, C. A., Adcroft, A., Curchitser, E., Hallberg, R., Harrison, M. J., ... & Simkins, J. (2023). A high-resolution physical-biogeochemical model for marine resource applications in the Northwest Atlantic (MOM6-COBALT-NWA12 v1. 0). Geoscientific Model Development Discussions, 2023, 1-65.
   4. Seijo-Ellis, G. G., Giglio, D., Marques, G. M., & Bryan, F. O. (2024). CARIB12: A Regional Community Earth System Model/Modular Ocean Model 6 Configuration of the Caribbean Sea. EGUsphere, 2024, 1-48.
2.  Table 1 and sensitivity experiements. Are the open boundary conditions for the first time step also replaced along with the initial conditions? If not, wouldn’t this generate noticeable discrepancies and noise near the boundaries?
3. The authors omit important citations in several places, for example no reference is given to the ERA5 and SODA reanalysis datasets or the ROMS and WRF models.  These should be cited in the text, not just the Data availability statement.
   1. ERA5: Hersbach, H., and Coauthors, 2020: The ERA5 global reanalysis. Q.J.R. Meteorol. Soc., 146, 1999–2049, https://doi.org/10.1002/qj.3803.
   2. SODA: Carton, J.A., G.A. Chepurin, and L. Chen (2018), SODA3: a new ocean climate reanalysis, J. Climate, 31, 6967-6983, https://doi.org/10.1175/JCLI-D-18-0149.1
4. 136-137: It would be much clearer and more concise to say: "The first month of each simulation is used for spin-up and not included in the analysis.” On that note, is a 1-month spin-up realistically enough for this case? Are the ocean boundaries nudged or sponge layers used to help with initial noise at the ocean boundaries?
5.  Line 139: “We named this set of runs the control experiment (CNTRL).” What set of runs? The ones in Prakash & Pant (2017)? If so, the simulations must be described to some extent here, I have no idea what they did there.
6. All datasets used should be described under Section 2. Data and Methodology not in the Results section. That includes the validation datasets and description of any processing done to them for the purposes of the validation comparison.
7. Lines 190-202: Figure 4 results are described before Figure 2 and 3.
8. Figure 4 should have a differences panel like Figures 2 and 3. This is important because there seems to be biases in the magnitude and spatial extent of some features. Current vectors could also be included in the difference panels similar to Figure 4 in Liu et al. (2015).
   1. Liu, Y., Lee, S. K., Enfield, D. B., Muhling, B. A., Lamkin, J. T., Muller-Karger, F. E., & Roffer, M. A. (2015). Potential impact of climate change on the Intra-Americas Sea: Part-1. A dynamic downscaling of the CMIP5 model projections. Journal of Marine Systems, 148, 56-69.
9. Lines 94-: “The simulated SST effectively captured the cold SST along the Somalia coast across all the examined years, firmly aligning with AVHRR SST data (Fig 2). The SST bias remained within 1oC in all three experiments except in the northern Arabian Sea, where a cold bias patch appeared in the model simulated SST.”  While the cold-tongue is present in the model, the statement as it is currently written is not supported by Figure 2 which shows some of the largest SST biases occur along the Somalian coast (particularly in 2016). Similarly, there are biases above 1degC (positive and negative) in other parts of the domain, not just in the Arabian Sea. While these biases are likely acceptable (the authors must convince the reader they are), it is still important to recognize them properly.
10. Lines 196-198: “This cold bias is attributed to the dry anomalous wind originating from the northwestern region of the South Asian landmass, a pattern also detected in the CMIP models (S. Sandeep & Ajayamohan, 2014).” This doesn’t make sense to me. Have you tested this is true in your model? CMIP models are free-running global climate models while you are running a reanalysis forced model. Unless you tested this is true, there is no reason at all to believe the same bias would exist in your forced simulation. Sandeep and Ajayamohan (2014) show that this SST bias results from biases in the representation of large-scale circulation on CMIP models. Those biases would likely not be present in your model and very constrained in the reanalysis forcing.
11. Lines 203-206: The figures in the supplemental materials must have a panel with the differences. The current qualitative comparison does not support the statement that the model results aligned well with the Buoy data. This part of the validation is important as the model must represent the temporal and vertical evolution of properties which are important to the processes the authors aim  to understand better.
    1. Figure S3 SST: shows noticeable difference in the time extent and magnitude of the warm temperatures and the shallowing of colder waters towards the end of the simulation.
    2. Figure S3 SSS: shows even more noticeable discrepancies between the model and buoy data. The buoy misses a notable high salinity water mass around June 2018. The near-surface distribution of salinity is also quite different.
    3. Similar comments generally apply to Figures S4 and S5.
12. The authors do not provide a reference to the buoy data.
13. Lines 206-208: Some additional information would be useful. Is this taking from a single grid point in the model closest to the buoy location? Or is this a horizontal average? If it is a horizontal average, over what region?
14. Line 138: Be consistent with the terminology, is it dissipation day or phase. One implies several days the other one a specific day. These terms seem to be used interchangeably throughout the manuscript which is confusing.
15. The definition for the mature phase in Lines137-138 say  “..is characterized by the day when the sea surface temperature (SST) within the MWP core (shown by the white box in Fig. 1) reaches its highest magnitude in May.”  Why only in May? What if it reaches the highest SST within the MWP on June?
16. Line 241: the use of “Furthermore” is not correct here.
17. Line 242: “…the wind stress over the SEAS remained less.” Less than what? Sentence is incomplete.
18.  A table detailing the mature day and dissipation day for each event would help the reader. The table can include the threshold used to define each.
19. The authors often omits the year when writing dates which makes the reading more confusing that it already is with the back and forth between the different years.
20. The domain of interest should be included in ALL figures and panels showing maps like shown in panels c, f and g of Figure 2.
21. Figure 6. Since the description of this figure in the text largely relies on the difference in the conditions between the mature and dissipation phases the authors could consider showing a similar figure with the difference between the time periods (i.e. dissipation – mature). This would be much more informative and relatable to the text in most of Section 3.2.
22. Line 255-257: “The signal of the southeastward propagation…”  Without the surface currents I can’t tell the low salinity signal is propagating southwestward, could as well be that the source of that low salinity is weaker and thus its extent is less.
23. Line 271: “However, these components of the net heat flux could not justify the progress of the MWP in the SEAS.” How do the authors reach this conclusion? it seems obvious to me that the latent heat flux is an important contributor to the progression of the MWP: the pattern of the net surface heat flux during the dissipation phase is very similar to the combined patterns of latent and surface heat fluxes. This is not surprising, as wind stress increases it drives evaporation at the surface which acts to cool the ocean surface via release of latent heat. In fact, Figure 8f shows that the heat tendency is largely explained by the net surface heat fluxes.
24.  Line 292-294: “ In 2018, the net heat flux supplied…” This needs re-writing as it implies this is true for the full time series in Figure 8d which is not.
25. Lines 296-300: While vertical mixing has a negative contribution to the heat tendency (i.e. cooling effect) that is true for the full time series. The vertical mixing curve remains largely flat with no noticeable trend driving the large variations shown for the heat tendency. The statement the authors make is only somewhat true for 2018. In 2013 its clear that contributions from horizontal advection and net surface fluxes drive most of the heat tendency during the dissipation phase. In 2016, the net surface heat fluxes also drive the heat tendency during the dissipation phase with the contribution from vertical mixing largely uniform throughout the time series.
26. The panels in Figures 9 and 10 need numbering.
27. Line 307: “…the intial pre-April ocean temperature…” Is the author referring to the initial condition mean SST? Please clarify this in the text.
28.  Lines 304-315: The description along these lines is extremely confusing and difficult to follow within the context of what the authors aim to describe. I would encourage rewriting. Start by reminding the reader what the first sensitivity experiment was, describe the results of the experiment, then connect with the results of the control simulation and what the results from the sensitivity experiment mean. Then do the same for the second sensitivity experiment.
29. Line 314-315 seem to contradict the statements made before about net heat fluxes and vertical mixing in the control experiment, which I already commented about in #24 above.
30. Figure 11: each panel should identify to which experiment is corresponds to. I shouldn’t need to read the caption to find this information.
31. It would be more useful and informative if Figure 11 and 8 were combined.
32. Line 333-334: “Moreover, the atmosphere was the primary driver of the vertical processes within the mixed layer that lead to the dissipation of the MWP.”  I’m not sure what the author means by this. How is the atmosphere the primary driver of vertical mixing processes in the ocean? Furthermore, the net surface heat fluxes are the main contributor to the tendency 11d, with combined contributions from all terms in Figure 11b. Furthermore, as detailed before, the contribution by vertical processes remains mostly the same throughout the time series, so its hard to understand in Fig.11 b and d how vertical processes are the drive the dissipation phase.
33. Lines 336-338 seem to me repetitions of Lines 330=331?
34. Figure 12-15. Experiment must be identified in the figure in addition to the caption.
35. Lines 373-374: shadow seem like an odd way to describe an area of high Ptke. Keep it simple and call it what it is.
36. Figures 13-15 are all discussed in a single paragraph. I would recommend combining (by eliminating unnecessary panels). The authors do not describe and/or comment on the panels associated with the thermal buoyancy flux or haline buyoyancy flux driven turbulent energy.
37. Line 409: “…revealed that net heat flux is the primary driver of the MWP development..” this statement (which I agree with) is not consistent with statements made in the results section (see comment 24 and others). Specifically line 271.
38. Lines 411-413: “However, net heat flux alone did not fully account…” You mixed layer budget (Figure 8) does not support the statement that after the mature phase, vertical mixing in the ocean leads to a rapid dissipation of the MWP, except for 2018 to some extent.
39. “Net heat flux” should always be “net surface heat flux”.
40. Line 414: “…significantly impacted…” what defines a significant impact in this case? There is no statistical analysis done to determine significance. Furthermore, one resulted in an increase and the other in a decrease. This is rather inconclusive.
41. Lines 423-424: “This contradicts previous studies, such as Kurian and Vinayachandran (2007), which suggested that MWP development in May was independent of the pre-April ocean conditions.” This needs further elaboration and comments by the authors. What are the differences between this study and the Kurian 2007 study that may lead to these different results?
42.  Figure 16 is potentially a nice way to wrap-up the manuscript. But the author make no effort to summarize and describe the formation and dissipation mechanisms of the MWP as shown in the figure. Describe in 1-2 simple sentences the processes as shown in Figure 16.

Review of “An evaluation of the Arabian Sea Warm Pool’s advancement during its mature phased using a coupled atmosphere-ocean numerical model” by S. P. Lahiri, K. R. Prakash, and V. Pant, submitted to EGUsphere.

This paper aims to investigate the temporal progression of the Warm Pool using observations and a regional coupled model (COAWST but without waves). The simulations are quite short

(~ 3 months) and are targeted at just one season. WRF component is run at 20km (inner nest) and ROMS is 1/6deg. The experimental and analysis approaches include control and sensitivity experiments for different years, mixed layer temperature budgets, and potential TKE analysis.

The paper has many interesting points and addresses an important climate topic. The experiments are useful, including the various helpful sensitivity experiments.  However there are some major limitations for which I give a Major Revision.

Major points

1. The simulations are rather short (April 1 to June 20). My interpretation of lines 72-74 and 131-133 is that the coupled model develops biases when simulations are longer than a season (please clarify this).

It is possible than by April 1^st, the mature phase has already started to develop, as a response to surface fluxes.  In this case, the ocean initial conditions on April 1 are a function of the prior surface fluxes of the warming period. Your finding that ocean initial conditions on April 1 are important may not be inconsistent with Kurian and Vinayachandran (2007). If you had initialized on Feb 1^st or March 1^st, your statement on lines 423-424 (“contradicts… Kurian and Vinayachandran (2007)”) would be reasonable, but for your current set up of April 1 initialization I think this line referring to Kurian and Vinayachandran (2007) should be removed.

Further, you analyze the heat budget from early May to June, but the warm pool has already considerably developed by early May. E.g. in your Fig. 8d,e,f there are only very brief periods in May where the temperature tendency is positive, it is mostly negative, a weakening. I realize you want to avoid the spin-up period, but perhaps you could do a heat budget anyway for April 1 to June and see if you capture any development of the warm pool (i.e. longer period of positive temperature tendency).

1. I found the section 3.3.2 on potential TKE production weak, mainly because the figures were too difficult to interpret. A probable improvement would be to provide timeseries for box averages of the terms in Fig. 13-15, for the region boxed in Figs 2c,f,i).

1. Map figures, e.g. Fig. 2, 3,4, 6, 7, 9, 10. The figures show a vast area of the Indian Ocean and it can be hard to see the region of interest. I understand that you sometimes want to display large-scale features, but for some figures you can show a smaller area, e.g. north of 5°N and east of 60° For example, in Fig. 4 it is hard to see coastal currents, and a smaller display region focused on the coasts would be better. For Figs 13-15, replace with timeseries plots as in Major Comment 2.

Line-by-line points

Line 13-14. See Major Comment 1.

Line 151. An earlier reference is Stevenson and Niiler 1983 - https://doi.org/10.1175/1520-0485(1983)013%3C1894:UOHBDT%3E2.0.CO;2

Lines 169-170. The expression in Han et al. 2001 does not include the von Karman constant, and I could not find this expression in Rao et al. 2002. Please check, I may have missed it.

Lines 208-214. A bit more detail on the analysis – were you looking at daily or monthly variability? How long were the data records? Do you remove any seasonal cycle or trend?

Line 189-190. Please put the time period also in the caption of Fig. 2.

Lines 253-257. This process is hard to see in Fig. 6. Please explain more, or delete.

Line 281 “enhance”->“allow”

Lines 291-300. See Major Comment 1.

Line 303. At this point, remind readers that the focus (control) year is 2018, and sensitivity experiments impose non-2018 conditions.

Figs 9-10. Please show 2018 control as an additional row for comparison.

Section 3.3.2 See Major Comment 2.

Lines 423-424. See Major Comment 1.