I have read this manuscript with great interest, particularly the geochemical analysis using elemental data from sp-ICP-TOFMS, which complements the authors' previous research. I fully agree that ice core samples should be analysed using multiple techniques to extract climatic signals from polar ice from different perspectives. Since no single method can capture the complete climatic record stored in ice, this study serves as an excellent example of utilizing multiple analytical approaches for dust analysis in the same Greenland ice cubes. This comprehensive investigation can provide valuable multi-dimensional insights into Earth's climate variability.

However, upon closely examining the sp-ICP-TOFMS measurement results, I was highly concerned about the data quality. This raises substantial concerns regarding potential contamination of the ice cube samples used in this study. Below, I outline the reasons for my concerns regarding data quality related to sample contamination. Until the authors address these contamination issues clearly, I am unable to provide a complete review of this manuscript.

Potential contamination issues

The methodology employed in this study is novel and has not been previously established. Given that trace metal analysis of polar ice cores requires extraordinary precautions to prevent contamination, additional examination is necessary. The authors used the “physical property” sections of the EGRIP ice core—these outermost sections are typically used for physical property measurements, where contamination from external materials (e.g., drilling fluid) is less critical. However, for trace metal analysis, contamination risk must be minimized.

The manuscript describes a decontamination process, but given the dimensions of the ice cube samples (1 cm × 1 cm × 1 cm, 1 mL of ice), I am concerned that this procedure is insufficient to effectively eliminate contamination. Established decontamination protocols for ice cores retrieved from fluid-filled boreholes require an initial acetone rinse to remove drilling fluid, followed by ultrapure water rinsing until 20–60% of the original ice volume has melted (Boutron and Batifol, 1985; Delmonte et al., 2002; Gaspari et al., 2006). The authors should provide a more detailed description of their decontamination procedure and critically assess its suitability for trace element analysis in polar ice cores.

Concerns about sample cleanliness become even more pronounced when comparing the ionic Fe background thresholds in Table A1 with total Fe levels reported in two well-aligned Greenland ice core studies: North Greenland Eemian Ice Drilling (NEEM) and EGRIP (Burger et al., 2021; Erhardt et al., 2019).

Typically, total Fe concentrations (including both particulate and dissolved Fe) should be significantly higher than ionic Fe background thresholds. However, the reported values in this study appear unexpectedly high.

First, the unit for ionic Fe background thresholds is missing from Table A1. Assuming it is in ppb (ng/g), which is a common convention, the lowest and highest Fe ionic backgrounds in this study are 9.803 ppb and 424.5 ppb for the cold climate samples G9 and YD3, respectively. These values are alarmingly high compared to the total dissolvable Fe concentrations of 2.9–146.4 ppb reported by Burger et al. (2021) after a month-long acidification process. Despite differences in sampling locations within Greenland, such high background thresholds may suggest contamination.

Furthermore, dissolved Fe background levels in a 3-m EGRIP ice core from the Holocene typically range from sub-ppb to 6 ppb, with non-dusty sections near 0 ppb and dusty sections around 2–3 ppb (Erhardt et al. 2019). The authors attribute the discrepancy between these two studies to methodological differences and different climate periods (line 303), but given that both Holocene EGRIP ice core samples exhibit similar dust particle concentrations (~1000 particles/mL, as measured by a laser particle counter (Abakus)), the observed Fe background levels in this study remain questionable.

In addition to the high Fe background levels, the inconsistency in particle counts and sizes for the five major elements in Figure 5 further suggests a high probability of contamination. Since Mg, Al, Si, Ti, and Fe primarily originate from mineral dust, their dissolved and insoluble concentrations should be positively correlated unless there is a specific event providing an element only without the others. For instance, if a sample exhibits a high dissolved Fe background, a correspondingly high Fe particle concentration would be expected. Similarly, increased dust content should be reflected in Al and Mg concentrations due to their co-occurrence in mineral dust, and vice versa. However, the observed discrepancies in detection trends—for example, high Al but low Fe detections in sample H1 compared to samples G5 and G7—suggest inconsistencies in the data that are difficult to be produced with natural sources alone.

The use of physical property sections—directly exposed to drilling fluid, uncleaned processing and packaging materials—introduces a high risk of contamination, making these samples unsuitable for trace-level analyses without strict decontamination procedure. Additionally, given that these samples have been handled in different environments over the years for multiple analyses, the risk of contamination is further increased. Due to their small size, effectively decontaminating 1 cm³ ice samples for trace metal analysis is particularly challenging.

Conclusion

The study presents a good case for multi-technique ice core analysis. However, the potential contamination issues outlined above need to be thoroughly addressed. The authors should provide clearer details on their decontamination process, re-evaluate its effectiveness, and discuss how contamination might have influenced their results. Without these clarifications, the reliability of the data remains uncertain, preventing further evaluation of the manuscript.



I provide the reference papers that I mentioned in the text as a supplement zip.

Stoll and co-authors present results from single particle time-of-flight (SP TOF) ICP-MS analysis on EGRIP (Greenland) ice core samples that have already been analysed by Raman spectroscopy and laser ablation (LA)ICP-MS. Overall, I find the subject very interesting and would like to see publication. Before this, I recommend that the authors consider significant revision to ensure the case they attempt to present for this new method is a compelling one, based on robust interpretation of the data, accounting for assumptions and uncertainties. 

I found the manuscript difficult to read. After reading the abstract, introduction, and conclusions (what many readers initially do) I was no wiser as to the specific focus of the study. The abstract includes several nebulous claims of ‘complimentary perspectives’ and ‘new possibilities’ but it is not clear what these are. From reading the manuscript through, the only advantage of including SP TOF analysis in the chain of particle-related analytical methods presented by manuscript is the chance to estimate particle size distribution from the SP TOF results. It would be better if the abstract, conclusions, and likely also the title, focused on this aspect, rather than claiming any benefits that are not demonstrated in this study.

Why develop a new method for particle sizing at all? Why not stick with CFA-based Abakus, SPES or Coulter counter methods? It would be great to see some justification of the need for the method development proposed here.  L285-288 could be moved from the Discussion for example.

A couple of technical queries:

• Could more information be provided on the conversion from measured ‘intensity’ (Fig. 1) to a ‘detection’ (is this the same unit as intensity, minus the threshold value?), to ‘normalised detection’ (normalised to what?).
• L43 “if suitable standards are analysed concurrently”. What are the standards referred to here? Are these the “calibration standards” mentioned at L107? How do you calibrate for ionic species and insoluble (particulate) elements? Or (related to above point) does a true calibration not actually occur?
• How representative do you expect the Au nanoparticle recovery result to be of particulate matter within these ice core samples?

How well is the efficacy of the proposed SP TOF method for particle sizing demonstrated…?

The authors state “Estimating particle sizes is possible if specific crystal phases are chosen for each element to obtain phase density and element mass fractions.” In section 2.5 they describe how each element measured is assigned a mineral, based on previously published Raman spectroscopy work. This assumes, for example, that all Si is sourced from SiO2, all Al from potassium feldspar, and that the mineralogy present in the nanoscale particles matches that of the microscale particles measured. These both seem like huge assumptions. The authors state the mineralogy assignment is a “simplification”. I don’t see that the implications of these assumptions are tested, i.e., to what extent do they influence the particle size results obtained? Si and Al are, by definition, present in all aluminosilicate minerals, which have different densities and elemental fractions.

In section 3.2.1, Figure 4, each element (or isotope) has been assigned to a mineral, and each mineral is assumed to have a certain density. Are these provided anywhere? – this choice seems absolutely critical to the particle size estimate, if I understand correctly. Overall, the conversion from mass to size and the potential uncertainty is not clear – the reader is referred back to Section 2.5, which provides little help.

Figure 5 displays the calculated particle size distributions for the five chosen elements/mineralogy assumptions for three of the samples only. The axes labels are impossible to read so it is difficult to begin to judge how these distributions might compare to existing particle size data.

Only samples H1, H2 and YD3 have insoluble particle data available (and only H1 is plotted on Fig 5). There doesn’t appear to be any comparison with these existing data within the manuscript. Unless I missed it, there is no attempt to verify the results of the SP TOF particle sizing method using independent means.

Finally, a quick note to say I do not share Reviewer 1’s concerns on contamination potential. Significant contamination from drill fluid or human handling would have shown up in the previous analyses. Drill fluid needs micro-cracks to penetrate into the ice core and these were not visualised. A clearer description of decontamination procedures and maybe a brief justification for their choice would be valuable. The second point highlighted by Reviewer 1, on the threshold setting, needs clarification before publication.

Minor suggestions:

The Introduction needs re-writing to streamline the information and argument presented. Many of the paragraphs reiterate arguments previously made.

L21: Is there not a more up-to-date reference than this 1997 one? The excellent Encyclopaedia of Quaternary Sciences by Koffman springs to mind (although I appreciate it is not OA).

L32: please more be specific on the ‘particular material characteristics of ice’!

L55: please explain what a “competitive trace element analysis” is.

L56-57: Please explain, for the average ‘ice core’ reader, the terms ‘non-target particle screening’ and ‘the internal and external mixing state of particles’ (if these advantages are actually relevant to this study).

Paragraph from L58: Isn’t there some SP TOF work coming out of Ohio State (Stanislav Kutuzov)?

L103: Acid-cleaned vials?

L125, 147: 24Mg etc are isotopes not elements. This occurs throughout the manuscript!

L187: Again, isotopes are listed not elements. 43Ca in G7 is low on Figure 2 but 44Ca is not – surely the relative abundance of isotopes of the same element should be corrected for? Why not describe elements as elements? Why persist in using isotopes? Hopefully Table 3 is not actually listing 56Fe/27Al (ditto for Figure 6)?

Figure 2: Last sentence of caption needs adjusting for clarity.

L249: 23Mg should be 24 Mg.