This is a solid paper. It proposed a multi-tracer method to estimate dust fluxes. It then estimated the dust flux at a strategic location in the Southern Ocean. The methodology is robust. The results are well presented and the conclusion is well justified.

I only have a few minor comments for consideration.

1. Title – be more concise. Words like “investigating” are a waste of space
2. Line 12-12: I suspected that you mean the flux estimated is between a peak dust deposition event and a low event. If so, the writing as it is does not represent this. Please clarify this and revise accordingly.
3. Line 16-19: This is a bit wordy. The first part of sentence appears to repeat the previous sentence. The main point appears to be something like: the data provided here will help to constrain model estimates of ….
4. Line 136: explain why 125 samples only for 6 years? E.g., give information on the sample duration and frequency.
5. Line 196-197: how an aliquot be DRY sieved?
6. I am sorry if I have missed but how the total mass of aerosols was estimated? This is important to mention as it determines the accuracy of the Fe/total aerosol mass ratio. It should be noted that there may well be sea salt and other natural/anthropogenic aerosols. This could reduce the total Fe content in the total aerosol. Similar applies to Al. This may partially explain the low mean Al/Fe contents in aerosols. It would be great if a mass closure (e.g., sulfate, nitrate, sea salt, OC, EC, dust etc.) is given if such data are available. This comment is also relevant for points raised in the paragraph starting line 286.
7. Table S2 – total Fe content in soil appears to be very low. Yes, there may be spatial variabilities. But could there also be a possibility of the size dependence? The size cut here is about 63 um. And in reality, you are unlikely going to see many particles of that size at the sampling location due to long range transport (not to say that it is impossible). I suggest that the authors look at literature and see how other studies have estimated the total Fe content, both in terms of the size cut of the particles, and methodology. Secondly, can you show all other elements you measure for all soil samples. They are very useful reference data for future research. 
8. Line 266: this is an interesting point. Later sentences supported this argument. Are there representative back trajectories that you can show to support this point? It would be good to have the back trajectories from high and low dust flux seasons. 
9. Line 316 – spelling error
10. Figure 3 – please mention briefly what ratios are being used? UCC or Australian soil results?
11. In Figure 1, would it be appropriate to consider add the locations by Strzelec et al. (and any other studies) where the dust flux was estimated?
12. There are mentions of fire and related dust. This is an interesting point but I do wonder whether you can provide any supporting evidence, such as higher K+ concentrations. I presume you haven’t analysed levoglocosan?
13. Paragraph starting 397: I wonder whether you can compare the estimated fluxes with more modelling studies. I think there are several global modelling studies of dust deposition fluxes. For example, Mahowald et al. 2005. https://agupubs.onlinelibrary.wiley.com/doi/10.1029/2004GB002402
14. Uncertainties: I agree that the multi-tracer method is more reasonable and better than a single tracer estimate. However there are still uncertainties and I suggest that you add a paragraph or section to discuss specifically about all the possible uncertainties, e.g., ratios, deposition velocities. It does not affect the conclusion of this paper but it will help readers to understand the manuscript better, and to use it more appropriately. If you can give an estimate of the uncertainty range, e.g., 2 times, that would be helpful. But I suspect it is not going to be an easy job. It may worth mentioning that models still have large uncertainties so the uncertainties from observation-based flux estimates are still relatively small.
15. Conclusions – this is rather long. Most of the points in the conclusions have already been mentioned in abstract. I wonder whether the final section as “Atmospheric implications” might be more useful to readers. Can you tell us a bit more about the implications of the results reported here? You mentioned nutrient inputs – are the inputs, in different seasons, likely to be important for ocean plankton and biological pump?
16. Can you also have a short paragraph, perhaps at the end of the “atmospheric implications” if you decide to have one, about what future research should be done? You did mention somewhere in the text about the research needs – but they could be at one place of the manuscript.

In this article, Hird et al. investigate the potential of using the concentration of four trace metals (Al, Fe, Th, and Ti), either independently or simultaneously, to estimate dust fluxes at the kunanyi/Mount Wellington time-series station, a site located in the wind corridor that transports Australian dust to the Southern Ocean. The authors present and analyze a data series collected over a period of 5 years, identifying an apparent seasonal behavior, and concluding that the variability in the calculated dust fluxes is reduced using one multi-elemental approach. Although it is a highly valuable dataset, the authors need to address key issues in their manuscript before it can be considered for publication.

General Comments

(1) From my personal perspective, the title of the work needs to be adjusted according to what is presented. According to the title, dust deposition at the entrance to the Southern Ocean will be quantified, exploring the use of lithogenic tracers in aerosols collected in Tasmania, Australia. However, since the Southern Ocean has many entry points, the title is a bit too broad for the scope of the manuscript. Furthermore, compared to what is stated in the title, instead of justifying and demonstrating that tracers work for calculating dust fluxes, the manuscript focuses more on the calculation of enrichment factors of metals in particles, their comparison with continental soils, and the seasonality of the calculated deposition fluxes (see the first sentence of the conclusions). This first comment is very important, as I believe the authors need to better focus their work.

(2) As they mention in the manuscript, they considered the proposal by Traill et al. (2022), who used these four tracers to calculate atmospheric flux in material collected in sediment traps at 1000 m depth. In the cited work, it is understood that the material consists of particles of various origins collected in a very complex environment, where the exposure time of the collectors and the collection area are clearly known. However, in the current work, why is it important to use this tracer approach if there is a way to accurately quantify the collected mass and it is certain that the collected material is aerosols? As I understand it, the greatest uncertainty in calculating a deposition flux arises when considering a constant deposition velocity, like the one you used (2 cm/s). However, by using the chemical composition of lithogenic metals as a tracer, you are not avoiding considering a constant deposition. So, what is the rationale for exploring the use of metal concentration in aerosols to estimate their mass and deposition? Isn't it simpler to quantify the mass of aerosols by weight difference rather than performing acid digestion and measuring metals by ICP-MS? I would like you to mention in your introduction the advantages this method has over others and, in your discussion, compare the flux estimation using other methods, including gravimetric analysis.

(3) In the methodology section, you should expand the information on dust collection and the calculation of fluxes using a hivol device: 1) sampling time, explaining why that time was used and, in case of high variability between samples, discussing why and how it affects the results. Currently, something unclear is mentioned (L115: “with each sample representing a period ranging from a few days to 2 weeks”); 2) Was the collected mass determined by gravimetry using the hivol device?; 3) Were the filters cut for digestion?; 4) How is the "total metal concentration (ng m-3)" calculated, as it is unclear?; 5) In the equations, the dimensional analysis is incorrect, making it difficult to understand how the fluxes were obtained. For example, in equation 1, considering the variables stated and the concentrations, you would not obtain a flux in mg/m2/s. The same issue occurs in equation 2, where the denominator is a concentration in wt%; 6) For clarity, the multi-elemental equation should be written; 7)I know it is mentioned later, but in the methodology section, it would be important to explain why the cold period is under-sampled, with only 2 out of the 6 sampled years represented. This last point is important for discussing whether seasonality truly exists or if it may be a result of under-sampling.

(4) Another question that arises is, if the intention is to consider the concentration of lithogenic metals as proxies for the deposited dust mass, why weren’t perchloric acid and higher temperatures (150 and 220°C) used during acid digestions? This could fully extract the metals from the particles and reveal their concentration. The absence of a total digestion protocol, like the one used by Traill et al. (2022), is concerning, as atmospheric fluxes could be underestimated. There is some evidence in the results that might point to this: 1) In Table S1, the recoveries presented for each metal are far from 100%; 2) if Table S2 is analyzed, the concentrations of Fe and Al in sieved top soils are low compared to the UCC, possibly indicating incomplete acid extraction; 3) something striking is what is presented in Table 2, as it would be expected that the best correlation would be between the elements with the highest abundance in the Earth's crust (Fe and Al).

(5) I would like to point out that the discussion of the seasonality of the calculated dust fluxes is not well supported. In fact, if you carefully observe Figures 2 and 3, half of the months in the time series were not sampled for the reasons mentioned by the authors. This creates a problem if the goal is to analyze any seasonal or interannual variation. What becomes evident is that the authors do not try to present meteorological evidence that helps compensate for the lack of data during the cold period. For example, it would be expected that a statement about seasonal variation in the calculated dust deposition fluxes would be accompanied by a detailed analysis of wind direction seasonality, relative humidity, atmospheric pressure, particle back trajectories, AOD, etc. The authors limit themselves to presenting a single graph of air-mass back-trajectory frequency that only considers 10 days before a single collection date, which of course is not representative of their entire study.

Other Comments

Abstract

It is not clear what the actual contribution to the knowledge of aerosol fluxes to the Southern Ocean is. As I mentioned in the first general comment, the focus of the work needs to be improved.

Introduction

L34-35, L45-47: These lines present similar information.

L100: See the first general comment.

Methodology

L140: When are the interannual trends discussed?

L143-144: The details of the chemical analysis should be provided in the manuscript. This includes a summary of the method detection limits, recovery percentages, measurement accuracy, and concentrations in the blanks.

L146-149: Could the low recovery percentages be related to the leaching method? See general comments.

L151: On what basis is a recovery considered satisfactory when it is greater than 80%?

L154-157: Considering the low recovery percentages, why did you continue to consider Th as a tracer for calculating atmospheric fluxes?

L161-164: Here, your Vd described in L169 should be mentioned. The same goes for lines L169-172, as they disconnect from L161.

L167: The equation lacks data to fulfill dimensional analysis. Another question that arises is whether you also calculated particle flux using weight difference.

L177: If F(x) has units of mg/m2/d and [X]UCC is in %wt, what would the units of Flith(x) be? Could you clarify?

L179: Could you clearly express exactly what you mean in an equation?

L206-212: The use of the enrichment factor to identify sources is debatable. It is more suitable for understanding whether an element is enriched or depleted with respect to the upper continental crust.

Results and Conclusion

See general comments.

L309-310, L315, L320: This does not indicate whether the correlation is significant. Statistical information is missing, and the coefficient needs to be properly named.

Conclusions

L149: When are the interannual trends discussed?

Figures

Significant improvements are needed in the figures. Among other things, the scales, shading, line thickness, font sizes, etc., in Figures 3 and 4 should be consistent. The same applies to the box and whisker plots.

Figure 1 needs improvement—according to the results of the work, would seasonal changes in wind patterns be expected? According to the figure, are they dominant in a certain period of the year? The text is unclear, as it indicates several things and does not clarify what is being referred to. It is like a figure that the author must interpret. The acronyms in Figure 1 should be described in the figure caption. Avoid directing the reader to a table that is not presented in the main manuscript.

Figure 2: If elemental ratios are mentioned with exponents in Table S3, they should also be presented this way in the figure.

Delete Figure S1 due to its lack of contribution to the work, and consider including a real trajectory analysis in the main manuscript.

Tables

In Table 1, it would be better to represent concentrations in ppm and %, just as in McLennan (2001). This should also apply to Table S1.

In Table 2, are you sure that R2 is the correlation coefficient? Isn’t it the coefficient of determination? I recommend using “R” . This also applies to the written text.

Table S1 should be moved to the main manuscript.