Molepo et al. examined long-term measurements of atmospheric Hg(0) at four coastal or oceanic island sites, focusing on steady-state air Hg(0) concentrations in the MBL over global oceans. Based on these findings and a previous air-sea thin film exchange model, the authors sought to calculate mean dissolved Hg(0) concentrations in surface seawater and extrapolate worldwide ocean Hg(0) emissions. First and foremost, I like the authors' insightful analysis of the observational data and creative approach to estimating oceanic Hg(0) emissions. These contributions are extremely hard and will undoubtedly inspire future research aimed at better understanding the global oceanic Hg cycle using observational data.

While reading the manuscript, I have concerns regarding the accuracy of the authors' methodology for estimating oceanic Hg(0) emissions, or rather, the authors did not adequately explain their method.

• The estimate of dissolved Hg(0) concentrations in surface seawater using steady state air Hg(0) concentrations has significant uncertainty. In this analysis, the authors postulate that steady-state air Hg(0) concentrations result from a balance between gross oceanic Hg(0) evasion and gross air Hg(0) invasion into saltwater. However, considering a box model for Hg(0) cycling, the steady state air Hg(0) concentrations should be also related to atmospheric Hg redox reactions and vertical exchanges between the MBL and free troposphere. The authors did mention atmospheric Hg redox in their discussion and suggested a minimal significance. I recommend that they calculate the net Hg(0) oxidation fluxes over oceans using model simulations and incorporate these into their equations. Additionally, For the vertical exchange between the MBL and free troposphere, a rough estimate from global models should be beneficial. Hence, I suggest a combination of a global model should be very important for a more accurate estimate.
• The calculation of dissolved Hg(0) concentrations in surface seawater based on the steady-state air Hg(0) concentrations indicates a near-zero net ocean Hg(0) emission; that is the gross oceanic Hg(0) emission is balanced by gross air Hg(0) invasion to seawater. Therefore, any further calculations based on the authors’ predicted dissolved Hg(0) concentrations in surface seawater will generate zero net ocean Hg(0) emissions. I read from Figure B1 (c, f, I, and l) that positive ocean-air Hg(0) exchange fluxes can be detected in their model, but these net emissions only occurred within a short distance from the site and most of the rest open oceans may not release Hg(0) (net emission) to the air, and this might be inconsistent with traditional knowledge.

Other minor specific comments:

Line 182-187: better to show the reactive gaseous Hg(II) concentrations and calculate their fractions in total gaseous mercury concentration.

Figure 1 c and e, the span of Y axis is to large, making it difficult to read the data.

Line 307-311: what we can learn from these temporal patterns? Are they indicating ocean Hg(0) emission paly a minor in atmospheric Hg(0)?

Line 364-365: did the authors calculate the mean air Hg(0) concentrations for the LFT categories? What is the difference between them and those in the MBL? Are they similar to those expected here?

Line 394-395: given the air mass travelling time and atmospheric Hg(0) residence time, about 3% loss of air Hg(0) can be expected during 6 days due to oxidation. While from Figure 4, the mean air Hg(0) concentrations during the initial several days are generally less than 10% lower than the steady state concentrations.

Line 433-435: with these dissolved Hg(0) concentrations in surface seawater, we will expect zero net ocean Hg(0) emissions according the equation (1).

Line 455-457: Previous studies may have reported numerous dissolved Hg(0) concentrations in surface seawater, which should encompass DGM concentrations during both enriched and un-enriched DGM episodes. Therefore, short-term measurements of DGM might be not the reason causing the elevated DGM concentrations by previous studies as compared with this study.   

In conclusion, the manuscript is well-organized and well-written. The concept of using observational data to constrain oceanic Hg(0) emissions is innovative. However, it remains unclear whether the proposed method for estimating ocean Hg(0) emissions is feasible. This warrants further evaluation by the authors.   

This manuscript by Molepo et al. aims to constrain Hg(0) air-sea exchange using long-term land-based observations from coastal regions and islands. While the long-term observations provide valuable insights into Hg(0) trends in both hemispheres over past decades, significant issues in the methodology and conclusions limit the reliability of the study. I recommend major revisions of the manuscript as detailed below.

1) The HYSPLIT model has significant uncertainty, particularly when using the coarse resolution employed in this study. The approximation methods used to solve Lagrangian and Eulerian approaches for transport and dispersion introduce larger errors as grid resolution becomes coarser. I recommend that the authors re-run the HYSPLIT model with finer grid resolutions, such as 1°, 0.5°, and 0.25°, for recent years at the observational sites. This would allow the authors to observe the substantial differences in back-trajectory tracks across different resolutions for a given location and time. Moreover, the 2.5° grid resolution used in this study is larger than the spatial scales of Amsterdam Island and São Vicente Island, making it difficult to determine whether an air mass originates from the continent based on the back-trajectory alone. This raises doubt about how the authors assigned trajectories as marine or terrestrial for these two observational sites – Cabo Verde Observatory and Amsterdam Island, which is not clearly described in the methods section.

2) Atmospheric Rn data used in this study provides a robust method to challenge the authors’ classification approach using the HYSPLIT model to determine whether an air mass originates from marine or terrestrial sources. As the authors noted in Line 321, “222Rn emission by the ocean is negligible (at a rate 2 to 3 orders of magnitude lower than the terrestrial flux),” which explains why atmospheric Rn measurements in the open ocean are rare – concentrations are typically too low, often below 20 mBq/m³, which is less than the detection limit of the instrument used at Cape Point. Therefore, whenever atmospheric Rn concentrations are detectable at Cape Point, it indicates that the air mass cannot originate solely from marine sources. Referring to the Rn data in Figure S4, the MBL_i label should not be assigned to a purely marine source, as the Rn concentrations are too high and clearly result from terrestrial emissions. Consequently, all the Rn data in Figure S4 suggest that the air masses are terrestrial sources (or maybe a mixture of marine and terrestrial sources, while the extent of this mixing cannot be quantified based on the Rn data itself).

3) The authors have applied the air-sea exchange equation under inappropriate conditions to estimate surface ocean dissolved Hg(0). The assumption stated in Line 419, “At steady-state F ≈ 0 ng m^-2 h^-1” is rarely valid in the open ocean. As shown in the previous measurements referenced in Table 2, surface seawater is generally supersaturated with Hg(0), leading to active emission of Hg(0) to the atmosphere. While exceptions may occur in specific seas during certain seasons, they are not representative of the open ocean as a whole. Consequently, given that “F > 0 ng m^-2 h^-1” in most open ocean settings, the subsequent estimations of surface seawater dissolved Hg(0) and the air-sea exchange flux of Hg(0) presented by the authors are not reliable.

I would suggest that the authors use the HYSPLIT model for qualitative rather than quantitative analysis, given its significant uncertainty in back-trajectory calculations, particularly when using the coarsest resolution (2.5°). Additionally, I suggest discarding the air mass categorization for the two observation sites, Amsterdam Island and São Vicente Island, since the HYSPLIT model resolution exceeds the size of these islands, making the classification unreliable. Furthermore, I encourage the authors to reconsider their method for estimating surface seawater dissolved Hg(0) concentrations and oceanic Hg(0) evasion, and ensure all co-authors are convinced of the robustness of these calculations.

Lastly, while using AI-tool for writing and editing manuscripts is not prohibited by EGU journals, I strongly recommend careful proofreading and revision to address too “AI-style” for some paragraphs.