The study presents a statistical model reconstruction for bias-corrected gridded regional model (e.g., HIRHAM and RACMO) and reanalysis model (CARRA) accumulation fields for the Greenland Ice Sheet (GrIS). The authors use an empirical orthogonal function (EOF) approach to reduce the model accumulation fields into primary spatial modes. Thereafter, the means, climatologies, EOFs and corresponding principal components (PCs) are adjusted through a set of coefficients that attempt to minimize the differences between modeled accumulation and SUMup in situ observations across the GrIS. Prior to adjustment, RACMO is shown to have the smallest absolute monthly mean accumulation biases, followed by HIRHAM and CARRA, but all accumulation zone and ice sheet-wide maps’ biases are reduced, especially in RACMO, after the adjustment takes place. It is interesting to note that post-adjustment, the biases of the highest resolution product, CARRA at 2.5 km, are not reduced further. The authors’ posit this may be due to such limited observations within these small gridbox areas.

The paper mainly showcases the statistical techniques and insights the render more accurate annual and seasonal accumulation maps and trends versus those produced with the native, unadjusted regional model/reanalysis outputs. This work may represent a significant advance toward understanding and developing Arctic/Antarctic accumulation maps going forward.  

The paper is nicely written, and results are by and large clearly presented. Several of my comments, however, are along the lines of structural changes where disentangling the tandem pairing of methods with or immediately followed by results is warranted. A more clear outline of the paper’s sections toward the end of the Introduction, followed by distinct separation of methods from results would improve the flow and readability of the manuscript. Further comments are noted by line (L) number below. In summary, these collectively constitute at least minor revision.

Major (Technical suggestions)

General comment: While each regional model is shown for their respective dataset start years to 2022, what about also showing maps for consistent periods (i.e., the CARRA record), 1991-2022 for more direct comparison of seasonal patterns and trends? This could complement Table 3.

Minor (Typographical/Structural suggestions)

L83: leavingàleave

L95-104: This content seems like more methods and initial results than introductory material, particularly in the description of the number of principal components retained and their explained variance.

L138: What is meant by “is merged with” – please clarify.

L156-166: This comparison of RACMO P-E and SMB against SUMup precedes introduction of the SUMup data. These results should be given after SUMup is described in detail in 2.3 or as initial results within the Results section.

L189: some time à sometimes

L193: subject-verb agreement here needs corrected to the “pre-summer/post-summer end dates are”

L328: Why use HadCRUT5 versus another global temperature dataset such as Berkeley Earth or GISTEMP? A brief note justifying use and acknowledging shortcomings of this product is warranted here.

L523: overestimatesàoverestimate

L623-630: Seems like these large-scale climatic dataset descriptions should go in the data section, then a results subsection could be framed around climate relationships to the PCs.

L649-650: “This is particularly relevant near the coast, where sea ice variability is known to strongly affect snowfall.” A citation to previous work is needed here at the conclusion of the sentence.

This study presents a statistical approach for bias-correcting accumulation data provided by regional climate models and atmospheric reanalysis. To do this, the authors first use an Empirical Orthogonal Function (EOF) to identify dominant modes of accumulation variation across the Greenland Ice Sheet. They then use the SUMup dataset to find a set of coefficients for adjusting the principal components (PCs) so that accumulation can be reconstructed without bias. Adjusting the PCs of accumulation grids allows the authors to derive accumulation biases across a much larger spatial extent and temporal resolution than would be possible using just the in-situ observations themselves. The manuscript is therefore able to identify model biases across the entire ice sheet in places that observations do not exist. Overall, I think that this is a very clever approach for adjusting modeled accumulation and the maps may represent our best current estimates of accumulation over the Greenland Ice Sheet.

I have a few general recommendations that I think would improve the manuscript. The first is that the paper is quite long which makes it challenging for the reader to follow at times. There are many repetitive statements that could be removed (or woven into previous text). There are also many cases where the authors provide figure (or table) “commentary” to start a section. These commentaries (e.g. L223-224, L360-362, L371-376, L435-438, L462-466) interrupt the narrative of the results section and, in most cases, could easily be removed. If the figures are clearly labelled and captioned, they don’t need to be described again in the main text. I highlight the relevant lines in my specific comments below.

My second recommendation is for the authors engage a little more with the limitations of their analysis. Currently the limitations section is very short (L6761-682) and only really discusses the uncertainties of the observational data. But there are other limitations that the authors mention earlier in the text which are not fully discussed in this section. I would be interested to see a reflection about the use of P-E vs. SMB in this analysis. The authors nicely show that P-E is perhaps better than SMB on average (Table 1). But there could be places on the ice sheet with substantial snow erosion or deposition where this may not be true.

Likewise, much of the analysis hinges on the assumption that the bias-adjustments applied inside the study area (where SUMup data is available) can be applied to outside the study area (where SUMup data is absent). I would like to see a deeper discussion of the uncertainties involved when extrapolating beyond the measurements in flat, low accumulation areas to more topographically complex environments at the margins of the ice sheet.

Finally, I think the manuscript would be more readable if the authors stuck more rigidly to the IMRAD structure. Some of the methods are in the results, results are in the discussion, and discussion points are in the conclusion. I understand that there can be good reasons for doing this. At the same time, I’ve generally found that sticking to the conventional structure almost always results in a more concise and readable manuscript. I’ve highlighted most of these examples in my specific comments.

Specific comments

L4: Do RCMs really contribute to “metre-scale” uncertainties in sea-level rise projections? In L697 the authors state that a 10% bias in snowfall could alter SLR projections by 15 mm.

L5-6: I'm don’t think that any study has used reanalysis datasets to evaluate RCMs. Or are the authors saying that reanalysis datasets are considered to be in-situ? Either way, consider clarifying this sentence.

L10: Describing the extent of SUMup using the number of points is misleading since many points are radar transects. Recommend describing SUMup in terms of temporal and spatial coverage or saying it is the most comprehensive dataset currently available.

L11-12: Applying an “EOF decomposition” to “adjust…EOFs” doesn't make sense, consider revising.

L16-17: This is not really a major finding or very surprising. Consider replacing with a more impactful finding.

L18-19: These numbers appear to be incorrect according to Table 4. These look like the original accumulation rates.

L25-26: Slightly strange choice of references for this statement. I don't think any of them compared Greenland Ice Sheet mass loss against other sources so how can they show that it is the greatest? Thermal expansion is also technically the greatest single contributor so might consider using “cryospheric contributor” to acknowledge that point.

L30-31: Recommend including a reference for this sentence.

L31-32: I would argue that the “complexity” of precipitation patterns themselves does not make them hard to constrain. Instead, it is the “complexity of processes that cause precipitation” that are challenging to for models to constrain (related to grid cell resolution and simplified cloud microphysics).

L32: Poorly constrained “by models”? If so, I recommend clarifying.

L33: The Hanna et al. (2024) is a review paper. I would prefer to see a citation to a study that has investigated this bias more directly (e.g. Ryan et al. 2020).

L47: It’s not immediately clear what the difference is between "accumulation patterns" and "spatial variability". Consider removing “spatial variability”.

L58: Does climate reanalysis assimilate in-situ atmospheric observations over Greenland? Recommend including a citation to provide evidence for this statement.

L60: "Limitations in model physics" is pretty vague, can the authors be more specific about causes of snowfall bias in models? Is it grid cell resolution failing to capture complex, steep topography? Is it simplified cloud microphysics?

L68-69: “better representation” by the model or by the ice cores?

L77: SMB is different to accumulation which is what the previous paragraphs focused on. Consider replacing “SMB” with “accumulation”.

 L81-82: I don't think it's fair to completely dismiss remote sensing technology but then cite a study that has measured snowfall using remote sensing. It can be done with CloudSat, it's just challenging because of sampling limitations and ground clutter (see Ryan et al., 2020).

L83: Not sure the authors can say "today" and reference a paper from 2013. An update is provided by Ryan et al. (2020) and there may be a more recent study.

L85: I would argue that the challenges with in-situ measurements are spatial more than anything (i.e. limited spatial coverage and uncertainties caused by point-to-pixel differences).

L88: Would it be fair to say that this study advances previous studies by incorporating the SUMup dataset for bias correction? If so, I recommend that the authors make this point clearer in the introduction.

L95-102: This is all interesting but it interrupts the flow of the introduction, which at this stage should be setting up the aims of the paper. Consider moving this to the methods.

L107: “accumulation” - do the authors mean “SMB” here?

L107: This sentence seems a little debatable given the challenges of accounting for runoff - recommend removing and putting in the discussion where it can be argued more convincingly.

L141: I think this section needs some sort of explicit statement that says "we assume accumulation = SMB" in our study area.

L141: I also recommend stating the percentage of the ice sheet area and the amount of total ice sheet snowfall that falls in this region. My back-of-the-envelope calculation from MAR suggests the area where runoff is zero is 73% of the ice sheet and 58% of the precipitation.

L150: I think the term “accumulation zone mask” is a little misleading here because the real accumulation zone is actually much bigger than this (i.e. runoff is greater than zero but still less than snowfall). I recommend replacing the term with “study area” or something similar so as not to confuse a reader who only skims the paper.

L163: “assess”

L171: Is this the actual accumulation zone or the "accumulation zone mask" that was defined previously?

L187-190: Are the authors implying that the radar data represent less than 12 months of accumulation? If so, they could be more explicit about that. Relatedly, do the authors use the radar data “as is” or is a correction applied to the radar data to account for the fact that the snow layer represents less than 12 months? It would be useful to clarify that here.

L95-102: Detailed description about EOF technique should be moved to the methods.  

Figure 2: Should RACMO not be blue (not orange)?

L277-278: the three “ands” in this sentence makes it difficult to understand what is being adjusted.

Figure 3: The difference between the yellow vs. orange and dark blue vs. light blue is really not clear. Suggest separating on another panel or changing color scheme

L371-376: See general comment but this is example of a paragraph that could be removed without losing much. The reader should be able to deduce all this information from the figure and caption alone.

L499: Fig. 3?

L512: “overestimate”

L498-513: This is all description of the findings so should be placed in the Results section. The Discussion really starts at L513.

L515: In Greenland? Please clarify.

L527-528: This is pretty vague. Could the authors be more specific about how higher spatial resolution enhances "sensitivity to intense precipitation events"? Consider adding citations as evidence.

L531: Ryan et al. (2020) confirms this bias using CloudSat.

L536-537: This is a confusing sentence because it seems to imply that the bias is larger in the southwest but it looks like the authors are only considering the area of bias. Recommend the authors quantify the total bias to investigate whether snowfall is more biased in the southeast or southwest (i.e. in km3 or Gt).

L540: Again, recommend the authors quantify the contribution of northern interior bias, perhaps as a percentage.

L549: Repetition of previous paragraph, consider removing.

L551: “are seen” is poor wording.

L553-554: This seems important because this bias should not be attributed to model. Can the authors provide a reference for this?

L556: Please provide a reference for this statement. I understand that reanalysis assimilates observations but are there any observations that are assimilated over Greenland?

L561: This seems like pure speculation. Can the authors provide a reference as evidence for winder conditions in the winter and spring months?

L564-565: Why would more frequent storms make them more likely to be "lifted over steep terrain"?

L565-567: I’m not sure I follow, doesn’t RACMO overestimate snowfall in the southeast? Surely a finer resolution model would overestimate snowfall more because the topography is steeper? Please consider citing a figure (or reference) as evidence for this statement.

L573: This is sentence is just a repetition of the previous sentence. Doesn't reduction in accumulation trends by bias-adjustment show that the models are overly sensitive to warming air temperatures?

L574: “are seen” is poor wording.

L582: The more robust trends in HIRHAM could be simply caused by the longer time period. Recommend comparing models over common time period before dismissing trends in RACMO and CARRA.

L583-588: I’m not sure that this paragraph adds much so it could be deleted.

L603: I would encourage the authors to reserve the word “significantly” for statistical statements.

L604: “may point” is poor wording

L616-653: This text presents new findings so should be moved to the Results section.

L619: first and second EOFs “of snowfall”?

L662: Can the authors be more specific about what they mean by “correlated time series”? Air temperature? SST?

L691-692: These look like the original numbers, not the bias-adjusted. It would also be better to use a common time period like in Table 4 so the comparison is “apples-to-apples”.

L694-702: This is all interesting but the Conclusion section shouldn’t introduce new information. It would be better to place this text in the Discussion.

References

Ryan, J. C., Smith, L. C., Wu, M., et al. (2020). Evaluation of Cloudsat's cloud‐profiling radar for mapping snowfall rates across the Greenland Ice Sheet. Journal of Geophysical Research: Atmospheres, (4), e2019JD031411.

General comments

Lindsey-Clark et al. describe a statistical method to bias-correct and present arguably the most accurate estimates to date of mean annual and seasonal 1960 to 2020 Greenland Ice Sheet (GrIS) snow accumulation rates. The work is motivated by GrIS snow accumulation uncertainty, most of which the authors attribute to poor observation sampling and limited underlying model resolution in regional climate models (RCMs) and in reanalyses. The methodology, a principal component analysis (PCA) applied using GrIS accumulation estimates from RCMs, the Copernicus Arctic Regional Reanalysis (CARRA), and observations of SMB components, is compelling and well executed. The figures and tables are labeled and presented clearly and, combined with the conclusions, are of good quality.

Depending on its applicability to the next generation of GrIS precipitation hind-casts and as forcing data for dynamic ice sheet and climate models, the manuscript presents a good level of substantial progress and novelty and could be fairly significant to the community researching ice sheet-climate interactions. The PCA and resulting improvements to observation-based RMSE scores are well suited for GrIS snow accumulation dependent studies and should be interesting to readers of The Cryosphere. On the other hand, the authors discuss their own findings in detail but not in the context of a substantially relevant body of literature. A more developed discussion of more recent work would improve the manuscript’s fair to poor scientific quality in this regard.

Specific comments:

1. The abstract is heavy on background material and light on quantitative results. To improve conciseness, the authors could cut most of lines 2-8, most of which could be merged with the introduction or removed altogether. While the authors present over 40 subpanels of maps and plots plus several meaningful statistics throughout the body of the manuscript, few of these results are reported in the abstract. To improve completeness, the authors should consider summarizing more of their results in the abstract or submit for publication with their manuscript a supplement that repurposes extraneous figures. I suggest that the authors consider which subset of their numerous results are essential to the main findings (i.e., those reported in the abstract and conclusions) and streamline the presentation of data by moving figures that can be interpreted more as supporting evidence to a supplement.
2. To improve the overall presentation quality, parts of the data section (section 2) could benefit from better organization, which suffers from a poor balance of details regarding the gridded data sets compared with the observations. Much of section 2.3 could be cut and merged with material in section 5, which would improve the discussion of other recent related work and better enable readers’ understanding of the broader context.
3. In my view, the work’s significance and its application to GrIS precipitation estimates depends on it being reproducible and/or the accessibility of the resulting data sets for use with impact studies (e.g., forcing data for firn, ice sheet, and sea level rise modeling and projections). To improve the work’s potential impact, I recommend that the authors clarify details of their input data and methods where possible. For example, there are lacking details regarding the RCMs and CARRA data sets (section 2.1) and of the applied regularization process (lines 291-296). HIRHAM is mentioned several times but no citation appears until section 2.1.1. Regarding the RCM and CARRA data sets, there are so few details provided that an unfamiliar reader must refer to other sources to learn what the acronyms represent and to understand basic components of the modeling systems, let alone their more technical nuances and strengths and weaknesses regarding estimating GrIS precipitation rates. While I understand that the authors need not fully describe previously published data sets, the level of details regarding these “main characters” is severely out of balance compared to that provided for the observational data (section 2.3). And while the detail of the methodological description is sufficient, due to the size of data sets and complexity of algorithms involved, full traceability of results would almost certainly require that the authors submit for publication with their manuscript archived source codes and/or software containers that have been tested on commonly used computing platforms and operating systems.
4. The authors’ discussion of other work lacks consideration of underlying physical processes, quantification of modeling errors and uncertainty, and limitations of data assimilation methods used by reanalysis systems. Beyond their own findings, discussion of mean annual and seasonality of biases and trend and EOF analysis includes only four studies published within the last seven years (van der Schot et al., 2024; Box et al., 2023; Gan et al., 2023, Matsumura et al., 2021). Underlying data assimilation challenges inherited by reanalyses, sources of model biases inherited by both reanalyses and RCMs, and North Atlantic teleconnections are closely related areas of research but are not discussed in the manuscript. For example, the authors mention that GrIS surface temperature variability and its related impact on precipitation is driven by El Niño events but do not elaborate on the "...teleconnections with North Atlantic atmospheric conditions…." (line numbers 620-635) nor develop the current body of research in this area. To improve scientific quality, I suggest the authors refine the discussion of their results with respect to the context of more recent relevant work, particularly regarding driving processes, uncertainty quantification and speculations of error sources in fit-for-purpose models and reanalyses (including those considered and not considered in their study).

Technical corrections:

1. Line 15: Please define the acronyms HIRHAM5, RACMO, and CARRA in the abstract.
2. Line 29: Further articulate the SMB definition(s), considering if the terms "specific SMB" and/or "climatic mass balance" are more appropriate for use with this manuscript.
3. Lines 103-105: The purpose of the work, which is to improve GrIS SMB estimates and downstream modeling of sea level rise, is not stated accurately or is misrepresented.