This manuscript presents a robust and methodologically significant paleolimnological study that refines diatom-based transfer functions for reconstructing Southern Hemisphere westerly wind (SHW) variability on sub-Antarctic Macquarie Island. By integrating contemporary diatom data with multi-year hydrogeochemical and isotopic datasets, the work effectively updates earlier conductivity-inference models and capitalizes on a unique post-eradication ecological context to establish a more representative diatom-environment baseline. The rigorous assessment of hadrochemical stability and evaporation solidifies electrical conductivity (EC) as a reliable proxy for wind-driven sea-spray aerosol deposition. The resulting model provides an ecologically grounded and statistically robust tool for reconstructing long-term SHW dynamics, advancing paleoclimatic methodology in the data-sparse sub-Antarctic region. However, few aspects require clarification and expansion to fully support the conclusions and maximize the manuscript's impact. I consider this paper to be highly important and valuable, and I strongly recommend it for publication with major revisions.

Detailed assessment and suggestions for improvement

Major issue:

Comment 1: Clarification on the concept of a "recovered baseline" and its validation (lines 61–75).

The manuscript highlights that earlier diatom-environment models were developed during a period of significant ecosystem disturbance from invasive rabbits and argues that the post-eradication dataset provides a better representation of a "natural" or "pre-invasion baseline." This is a critical premise for claiming an improved and more ecologically relevant transfer function. However, the current argument is largely inferential. To substantiate this central claim, more direct evidence or a more rigorous conceptual framework is required. Specifically, the text should address the following questions:

What defines the "recovered" state? Is it the mere absence of rabbits, or are there specific, measurable limnological parameters (e.g., nutrient levels, sediment composition, vegetation cover) that have demonstrably returned to a defined range? Please reference specific post-eradication recovery studies to define the criteria for "recovery" as applied to lacustrine systems.

How do we know this state approximates a "pre-invasion baseline"? The strongest evidence would be a direct comparison. If available, please discuss whether diatom assemblages from your 2022 surface sediments show greater similarity to subfossil diatom assemblages from sediment core intervals dated to pre-1900 (i.e., pre-rabbit introduction) than to assemblages from core intervals representing the peak disturbance period. If such core data is not available, this limitation should be explicitly acknowledged, and the argument should be reframed more cautiously. Instead of claiming to represent a "pre-invasion baseline," it may be more accurate to state that the model reflects "post-distribution recovery conditions" which are assumed to be moving toward a pre-disturbance state, thereby reducing the confounding noise of extreme eutrophication and erosion in the calibration dataset.

Comment 2: Lines 88-89 & throughout Discussion: Clarifying the mechanistic link between diatom-inferred EC and SHW strength.

The manuscript's core hypothesis is that diatom-inferred Electrical Conductivity (EC) serves as a proxy for Southern Hemisphere Westerly Wind (SHW) strength via wind-driven Sea Spray Aerosol (SSA) deposition. While the study excellently establishes the diatom-EC relationship and demonstrates that EC in western lakes reflects SSA inputs, it presents a circular argument when applying this to paleoclimate. The logic is: 1) SHW drives SSA, 2) SSA increases lake EC, 3) Diatoms record EC. Therefore, fossil diatoms can reconstruct past EC, which implies past SSA, which implies past SHW.

However, a critical intermediate step is missing: a quantitative or semi-quantitative demonstration that the observed spatial and interannual EC gradient is directly forced by measurable wind parameters. The discussion relies on citations (e.g., Saunders et al., 2009, 2018) for this link but does not independently validate it with the new, richer 2018-2022 dataset. To resolve this, the following major addition is required:

Perform and present a correlation analysis between measured EC values (or marine ion concentrations like Na+, Cl-) from your key SSA-influenced lakes and instrumental wind data (e.g., mean seasonal wind speed, frequency of high-wind events) from the Macquarie Island station (BOM, 2025) for the corresponding periods (2018, 2022-23). This analysis would test the fundamental assumption that higher EC in a given year or at a given site correlates with stronger westerly wind metrics.

Discussion of the Wind-EC Transfer Function: If a correlation exists, discuss its strength and the potential variance explained by wind speed alone. If the correlation is weak or non-existent for the short instrumental record, discuss other modulating factors (e.g., rainfall dilution history, wave state affecting SSA generation) and what this means for the certainty of reconstructing wind speed(a dynamic variable) from SSA deposition (an integrated flux variable). This moves the discussion from a simple cause-and-effect to a more nuanced, process-based understanding of the proxy.

Comment 3: Interannual variability and its implications for the calibration dataset

The manuscript correctly observes that the primary clustering in the PCA (Fig. 4) is by lake type (SSA, catchment, rainfall), which indicates the dominant spatial hydrogeochemical processes are consistent between 2018 and 2022. This is a crucial point supporting site selection. However, the same figure also reveals a secondary pattern: for a given lake type, samples often separate by year along PC1 (e.g., SSA lakes from 2018 have more positive scores than those from 2022). Table 2 quantifies this, showing significantly higher mean concentrations of marine-derived ions (Cl, SO₄, Br, Mg) in 2018. This interannual variability in the intensity of the sea-spray signal is an important finding, but its implications for the transfer function need further exploration to fully support the conclusion of robust "hydrogeochemical stability." Please address the following

Impact on model calibration: he diatom-EC transfer function is calibrated on a composite dataset spanning years with demonstrably different SSA intensities (2006, 2018, 2022). This is standard practice, but the observed variability raises a critical methodological question: Does this interannual variation in the modern calibration gradient introduce uncertainty or bias into the species' inferred environmental optima, particularly at the high-EC end critical for reconstructing strong wind periods?

To conclusively demonstrate the model's robustness and the validity of the "stable conditions", a quantitative sensitivity analysis must be added. This analysis should test how the model's core parameters change when calibrated on subsets representing different SSA conditions. Specifically, we request you perform subset calibration: Recalculate the WA transfer function using two distinct modern calibration sets

Set A (Higher SSA):Combine the 2006 coastal data with the 2018 plateau data.

Set B (Lower SSA):Use the 2022 plateau data only.

For key high-EC indicator taxa (e.g., Planothidium lanceolatum, Fragilaria capucina), compare their inferred conductivity optima and tolerances between Set A and Set B. Present this in a supplementary table.

Compare the overall model performance metrics (, RMSEP) and the observed vs. predicted scatter for the two subset models. If species optima and model performance are consistent between subsets, it provides quantitative proof that the model is robust to interannual SSA variability, strongly reinforcing the conclusion of a stable, transferable relationship. If significant shifts in optima occur, it quantifies a potential source of error. This would necessitate a discussion on the implications for reconstructing absolute wind strength and would strengthen the manuscript by rigorously defining the model's calibration uncertainty.

Comment 4: Disentangling EC and nutrient signals (Line 567-574 & Figure 8). 

While the manuscript appropriately attributes low plateau-lake nutrient variability to recovered conditions, the combined calibration dataset explicitly includes a high-nutrient gradient via the 2006 coastal lakes. The variance partitioning (Fig. 8) shows major shared variance between EC and nutrients (TON, Phosphate), yet the partial CCA (Table 5) indicates negligible unique nutrient effects. This raises a critical, unresolved question: does the dominant EC signal ecologically overwhelm nutrient influences in this system, or does it statistically mask a co-varying nutrient effect, particularly in coastal lakes where both marine ions and organic nutrients are elevated? Please expand this discussion to explicitly interpret Fig. 8, clarifying whether the weak unique nutrient signal is an ecological reality of the recovered state or a statistical artefact of collinearity, thereby justifying the exclusive focus on EC for paleoclimatic inference.

Comment 5: From suggestion to synthesis for multiproxy research (Line 625–632)

The conclusion on multi-proxy applications is currently vague. Please expand this into a concise synthesis paragraph proposing a specific framework. For example, explain how δ²H/δ¹⁸O could constrain evaporative effects on EC, or how mercury isotopes could independently validate wind-driven aerosol deposition. Outline one or two testable hypotheses that future multi-proxy studies on Macquarie Island could address to resolve the interplay between SHW strength, precipitation, and evaporation.

Comment 6: Some important environmental variables are missing, for example, the effect of water depth on diatom assemblages (Farqan Muhammad et al., 2025, Quaternary International).

Comment 7: Lines 340-341: How many diatom taxa are classified as ‘unknown’?

Comment 8: In the Discussion section, figure numbers should be inserted where appropriate.

Comment 9: In the Introduction and Discussion sections, more studies on diatom–EC transfer functions and the indicative significance of diatoms for salinity should be discussed, for example, Farqan Muhammad et al. (2025, Ecological Indicators).

Minor issue:

Line 21: “Sea-spray inputs” – Specify whether this refers to dry deposition, wet deposition, or both, as this affects the wind-salinity relationship.

Line 63: “from the late 1900s to early 2000's” change to “late 1900s to early 2000s” (no apostrophe).

Line 70: “were conducted during a period of disturbance related to introduced invasive vertebrates rather than when the island was in a natural state” → awkward; rephrase to “were conducted during a period of vertebrate-induced disturbance rather than under near-natural conditions”.

Lines 79–82: Mention whether lake type (SSA, catchment, rainfall) was validated with independent data or is based solely on the Meredith et al. (2022) classification.

Line 121: “drier windier summers” add comma “drier, windier summers”.

Line 126: Figure 1 caption “modern core SHW belt (50–55S°)” correct to 50–55°S.

Lines 203–207: Justify the use of both parametric and non-parametric statistical tests in the same dataset. Consider providing a table of test results for clarity.

Lines 347–355: Mention whether any taxa (Species distributions) are exclusive to coastal vs. plateau lakes, and the implications for salinity inferences.

Lines 437–440: Figure 11 – Label panels (a–d) clearly in the caption and refer to them in the text when discussing model performance.

General – units and formatting: EC is sometimes µS cm⁻¹, sometimes not specified. Standardize to µS cm⁻¹ everywhere. Also check consistency of δ¹⁸O / δ²H notation (superscript vs plain text).

Line 345: In the taxon name Psammothidium confusum var. atomoides, ‘var.’ should be in regular font rather than italics.

This study builds upon previous work on developing diatom inference models for electrical conductivity (EC) as a proxy for Southern Hemisphere westerly winds (SHW) from a spatial network of lakes on the sub-Antarctic Macquarie Island. While models were developed previously by Saunders et al. (various publications), the study seeks to improve model performance through expanding the water chemistry datasets across several seasons. Improvements to model development are also linked to data being collected after the successful removal of the invasive rabbit population. 

Overall the collection and analyses of the data are robust. Two major things for the authors to consider however are: 

(i) I felt that the analyses of the data itself could have been stricter in terms of discussion on what was found to be “significant” or not. 

(ii) the study ends by presenting an incremental improvement on diatom-inferred EC models for Macquarie, but with no application. As core material already exists for the island, and reconstructions have previously been published, I would have liked a more critical evaluation of model application over and above model development 

Specific comments:

Pages 3-4, Lines 63-75: Although the authors suggest that the post-eradication period is equivalent to pre-invasion baseline communities, I think more caution is needed with this assumption. Moreover, this would only be relevant if EC reconstructions were being carried out on sediments prior to the early 1900s; reconstructions post then based on a spatial dataset that has been impacted by rabbits is appropriate still. So the authors probably need to be a bit more nuanced here. 

Lines 66-68: approximately when were all rabbits eradicated? How does this timescale fit with the dates of the datasets used in this study?

Lines 93-95, is it really the case that seasonal and multiyear lake water hydrogeochemical datasets is “rare worldwide”? While long term monitoring datasets should be more common, they are not rare (although in many places there will be geographical scarcity). The authors could be more critical here and outline where long-term / seasonal datasets have been used for quantitative reconstruction studies similar to their own. 

Likewise in lines 103-105: the authors claim that this study “…provides a first step towards long-term monitoring of sub-Antarctic lake systems.” But it’s not clear to me how the study will facilitate future long-term monitoring. 

Materials and Methods 

Lines 113-115: I guess an ultimate goal of model development would be to compare reconstructions of EC with monitoring records of SHW to determine if there is correlation between model and instrumental records. Has this been done by previous authors at all?

P7, Lines 147-148. I’ve not heard of surface sediments being collected before using a long-handled scoop. How were only the top 2cm of sediments controlled for (scooping up sediment suggests to me some mixing will occur). What timescale might 2cm of sediment represent? Could these surface sediments therefore represent several years, or even a decade of accumulation? More information here on sediment / diatom sample collection would be good. Does the collection method match with previous studies etc?

Results

P12, lines 271-272: I'd say that pH 5.7 is an acid lake rather than 'slightly acidic', and pH 9.14 is definitely more than being 'slightly alkaline'. Did diatoms preserve well in these more alkaline lakes? Was there any sign of differential dissolution?

Line 278: Given the relative proximity of the lakes to each other, I think that relying on p values of < 0.05 is a generous cut-off for significance. If this was made more strict, e.g. p < 0.01 or even better 0.005, would you still see differences between plateau lakes measured in 2022 and coastal lakes in 2006? I think that this is a recurring theme throughout the analyses where p values chosen could be more strict and therefore simplifying interpretation of the data better. 

Table 1: is it possible to put n values for e.g. each season (numbers of lakes)

Table 2: I wonder if this might not be better presented as box and whisker plots to see differences (if any) between the two years

P14:, line 298-299:  if we were being more strict (which I'd recommend,) there is no sig dif in Br either. I think the authors need to appreciate more that the close proximity of the lakes to each other will influence p values through spatial auto-correlation and the same will be true for analyses of lakes in seasons relatively close to each other in terms of time as well. I honestly do not think that p=0.023 represents a true significantly different result. There is quite a large literature on the benefits of using smaller p values in interpreting data. 

Lines 310-311:  don't think that these lakes are outliers (from looking at Figure 4). They are just at the far end of the gradient. There are various definitions for values / sites to be considered outliers, so technically an objective term!

P15: The section on stable water isotopes have produced some robust findings. 

P18, Lines 364-368: Were Bonferroni corrections considered in the forward selection – they need to be.  

P19: This section on partial CCAs is robust, ending with good justification for modelling EC

P20, Section 3.3.3: Figures 9 and 10 do not show species optima and tolerances!

F. capucina has an interesting bimodal distribution – why might this be? Did the authors consider using species relationships to selected environmental variables via species response curves fitted with a GAM?

P22: Table 6: I think Temperature is always a difficult variable to model for diatoms, and there is quite a large literature critiquing modelling T from diatoms e.g. see Juggins 2013 (which the authors already cite). I would avoid modelling Temperature in this study

P23 Figure 11: the relationship shown between observed and modelled conductivity is complex and far from linear. ML looks to be more straightforward. It’s good to see (in the Discussion) that the authors taken this complexity when deciding on best final modal to use, and what might be the reasons for this complexity in the EC responses

Discussion

Lines 454-463: the discussion on Br (and indeed all the chemistry) could be more succinct, if as suggested above the threshold for “significance” is more robust (e.g. p = 0.005).

Lines 485-491: this paragraph feels out of place here, and probably belongs elsewhere in the discussion., eg Section 4.4. I doubt that TF would be improved with better seasonal monitoring, although the understanding of lake water chemistry would be improved. Key for any transfer function is that the season for peak diatom growth is sampled. Is this the case here?

I thought that section 4.2 on Evaporation was very good, as it furthers our understanding on a key control on chemical variation in these lakes. 

Developing transfer functions: the discussion section is good and supported well by the data. I would agree with their final choice in ML model selection.

Section 4.5: this is fine, but a bit brief. What TF models have been applied to Macquarie Island lakes before. Could this new model not have been applied to those for a comparison? Especially the model developed by Saunders et al 2015 and then applied model by Saunders et al. 2018. 

Further, the final sentence on using a multiproxy approach is far too vague – more detail should be given that’s relevant for the region, e.g. what other proxies could be used, how would they complement existing interpretations.