This manuscript introduces a new climate index, the "Middle-latitude Indian Ocean Dipole" (MIOD), and investigates its influence on the Southern Hemisphere's middle and upper atmosphere. The study uses a multi-faceted approach combining reanalysis, satellite data, and model simulations to build a compelling narrative. The proposed physical mechanism links positive MIOD events to enhanced planetary wave activity, which in turn drives significant stratospheric and mesospheric changes. This mechanism is logical, well-articulated, and represents a potentially significant contribution to our understanding of ocean-atmosphere coupling. The finding of a strong asymmetry in the atmospheric response between positive and negative MIOD events is particularly noteworthy.

However, the manuscript in its current form is undermined by several methodological flaws and a lack of careful preparation that question the validity and reproducibility of its core findings. Most central is the pre-removal of EESC from SST prior to the EOF, which is unusual and risks biasing the MIOD pattern. Second is event selection that is vulnerable to ENSO aliasing (e.g., 2016). Furthermore, the statistical robustness is limited by a small sample size, and errors in figure labels and captions detract from the paper's credibility. With stronger methodological circumspection, a set of focused robustness checks, and cleaner presentation, the paper can reach the level the idea deserves.

All my concerns are detailed below. I do not necessarily expect the authors to address every point, but I do expect the critical issues to be dealt with convincingly for the work to be credible.

Major comments

1) SST preprocessing with EESC before the EOF

The manuscript removes EESC from JJA SST prior to the EOF but largely treats this as routine. It is not. EESC is a stratospheric halogen proxy : a direct, widely accepted causal pathway to basin-scale SST variability is not established. Regressing out a non-linear, parabolic-like trajectory from SST can reshape low-frequency variance and therefore the EOF structures themselves. In other words, the MIOD pattern may be sensitive to this step. If the intention is to isolate an SST pattern “untainted” by ozone-related radiative trends, that needs a clear physical rationale. Otherwise, a standard approach is to detrend SST (and, if desired, apply ENSO/SIOD partialing in atmospheric fields, not in SST itself). At minimum the preprocessing must be made prominent in the figure caption and methods, and the results shown to be robust to its omission.

2) Event selection and ENSO aliasing

The paper aims to separate MIOD impacts from ENSO, but the threshold-based exclusion (JJA Niño-3.4 ±1σ) is a blunt tool. A case in point is 2016: the trailing influence of the 2015–16 El Niño plausibly persists into mid-2016, yet 2016 enters the “positive MIOD” set. Given the small sample, one influential year can strongly color the composites in Fig. 3. Threshold exclusion is weaker than regression-based control. The latter is standard and makes better use of the record. At a minimum the reader needs to see a 2016-excluded positive composite and a regression-controlled view to judge robustness.

3) Positive–negative asymmetry: mechanism and power

The descriptive evidence for asymmetry is good (Fig. 5), but the paper stops short of explaining why the SST patterns in Fig. 4 project so differently onto the large-scale wave field. There is room, and need, for a more mechanistic line: stationary-wave sources/diabatic heating anomalies, Charney–Drazin refractive index/waveguide diagnostics, or MIOD→WN-1 amplitude regressions would move the argument beyond “constructive vs destructive interference”. The negative-event null should also be tempered by an explicit acknowledgement of limited power (7 cases) and supported by leave-one-out and threshold-sensitivity checks. A brief discussion of MIOD’s relationship to the SAM would give useful context for vertical propagation and annular-mode fingerprints.

4) SD-WACCM6 framing

The SD configuration is nudged to reanalysis : it provides diagnostic consistency (e.g., gravity-wave drag, MLT structure) rather than an independent forced response. The manuscript sometimes reads as if the model “confirms” the mechanism. It would be more accurate to present SD-WACCM6 as a way to diagnose fields not available in reanalysis, with language calibrated accordingly. If any free-running sensitivities or prior literature exist that align with the sign/structure of the MLT anomalies, pointing to them would help.

5) Temporal evolution and breadth of robustness

The proposed pathway invites questions about onset/persistence and seasonality. Lead–lag views (MAM→JJA→SON) would clarify timing and any spring imprint, and a second reanalysis (JRA-55, MERRA-2) for key figures would demonstrate that results are not a one-dataset artifact. Claims about vortex “morphology” would benefit from simple, objective metrics (PV or geopotential on an isentrope; centroid, ellipticity, equivalent area).

6) Ozone transport vs chemistry and gravity-wave filtering evidence

The TCO/ozone anomalies are interpreted primarily as transport. Where available in SD-WACCM6-SD, an ozone tendency decomposition (transport vs chemistry) or at least correlations with residual vertical velocity would strengthen that interpretation. For the MLT, the gravity-wave filtering story is plausible. If SABER gravity-wave potential energy proxies or related diagnostics can be composited, they would provide a welcome observational cross-check.

Minor comments

The caption (Line 502) identifies the plot as showing TCO for negative MIOD events, but the pattern shown is a direct and obvious consequence of the circulation changes described for positive events in Figure 8a. The caption and text must be reconciled with the figure's content.

The x-axis of Figure 6 (both panels) is incorrectly labeled "Longitude (°)." As this is a zonal-mean plot, the axis must be corrected to "Latitude (°)."

The numbering is incorrect and inconsistent in Section 2.2. There are two equations labeled (4), a jump from (5) to (9), and an unnumbered thermal wind equation. Please correct all numbering to be sequential.

Figure 2b Visualization: The overlapping symbols are confusing and inefficient for conveying the event selection process. This figure should be replaced with a clearer visualization, such as a timeline or a table.

Figure 5 Clarity: The climatology contours are difficult to distinguish from the zero contour of the anomaly shading. Please use a different color or line style to improve readability.

Text-Figure Mismatch (Line 347): The text refers to Figure 4b as showing "positive-phase MIOD events," but the figure shows the composite for negative events. Please correct this.

Typographical Errors:

• Line 446: The latitude range "50°S-7°S" appears to be a typo and should likely be "50°S-70°S."
• Line 555: The sentence beginning "The spatial phase of this cold band..." is redundant and should be revised or removed.

Methodological Justification:

• E-P Flux Normalization (Figure 6): The non-standard "two-layer normalization approach" requires justification. Explain why this was chosen over standard methods.
• MIOD Index vs. PC2: Briefly elaborate on why a physically-based box definition is preferable to the mathematically derived PC time series.

Comments on “Impact of the Indian Ocean Sea Surface Temperature on the Southern Hemisphere Middle Atmosphere” by Yang et al.

This study investigates the impacts of the midlatitude Indian Ocean sea surface temperatures (SSTs) on the Southern Hemisphere middle and upper atmosphere based on the proposed midlatitude Indian Ocean Dipole (MIOD) index. The authors show that positive MIOD events enhance planetary-wave propagation from the Indian Ocean sector, leading to variations in temperature, zonal winds, as well as a strengthening of the residual meridional circulation, while negative MIOD events have relatively weak impacts on the Southern Hemisphere middle and upper atmosphere. The issues tackled in this study are worthwhile and well within the scope of this journal. However, some conclusions are lack of sound verification. It needs major revisions before it is accepted for publication. The following are some specific comments and suggestions:

1. Line 38-39: The stratospheric thermal radiation only can not insert significant influences on both tropical and extratropical circulation，it is radiative-chemical-dynamic coupling that is important.
2. Line 104-105: The statement “Yet the atmospheric background conditions during austral winter are more favorable for planetary wave propagation into the stratosphere” needs reference support.
3. Line 164-166: what is the top level of MERRA-2 reanalysis? The WACCM6-SD run at the model top near 140 km. On which model level does the nudging begin to perform?
4. Line 180: “between 40 and 80 kilometers” >>>”between 40 and 80 km”
5. Line 346: “positive-phase MIOD events” >>> “negative -phase MIOD events”
6. Line 362: what is hgt?
7. Line 368: HGT>>hgt
8. Line 440: Figure 6: Longitude>>Latitude
9. Line 510: “ozone deletion” >> “ozone decrease”. The depletion generally means destroyed rather the transported.
10. My major concern is related to Section 4. This section presents the results in the mesosphere. It looks strange to put those results in Discussion Section. Are those results are preliminary?
11. Line 540：Figure 9：above 80 km, there is no consistency between the satellite observations and model results. Is it due to nudging approach?
12. Line 590-594: The authors stated that “Discrepancies between thermal wind estimates and reanalysis winds are largely attributable to planetary wave breaking”. This is not true! various processes may have contributions to those discrepancies.
13. Line 597-598: The authors stated that “The influence of the MIOD extends into the mesosphere and lower thermosphere (MLT) through gravity‐wave filtering modulated by stratospheric wind perturbations”. This statement has no support.
14. Line 625-627: “The findings are consistently supported by satellite observations and WACCM6 simulations, lending robustness to the identified SST atmosphere coupling”. However, there are no any comparisons between the model results and satellite observations in the stratosphere.
15. Line 628-629: “with the Southern Hemisphere atmosphere being more sensitive due to its unique background circulation during winter”. There are no any discussions on this statement.
16. Line 632-633: “The analysis further suggests that long-term trends in Indian Ocean SST may have contributed to the observed variability in Antarctic ozone depletion and recovery”. There are no any discussions on the long term trends of variables. How can you draw this conclusion?