General remarks

This is an excellent and novel quantitative analysis of the contribution of the local change in background thermodynamic contribution to the Greenland Ice Sheet surface mass balance loss. It effectively separates out the role of sea-surface temperature and sea-ice concentration forcing, which is found (corroborating some but not all previous studies) to be relatively minor. A valuable analysis of the extreme melt case studies of 2012 and 2019, and the difference in terms of climatic forcing between these events, is provided. The analysis is thorough and the paper is clearly written. It will be of wide interest to Greenland climate scientists and ice-sheet specialists. I recommend publication following a minor revision addressing the points below.

Specific comments

Line 26: please add the following recent relevant references:

Otosaka et al. (2023) https://essd.copernicus.org/articles/15/1597/2023/

Hanna et al. (2024) https://www.nature.com/articles/s43017-023-00509-7#publish-with-us

Figure 1: define PGW-1, PGW-2 etc. I the figure caption.

Lines 167-179: please add that while GCMs may capture the periodicity of internal climate variability they may not capture the magnitude of such variability. Will taking the CESM-LE ensemble mean be affected by signal-to-noise issues with the GCMs in capturing North Atlantic circulation change?

l.201: Are there issues with the accuracy of prescribed SIC and SST for 1880-1899 that may affected the method used?

ll.252 & 480: please add the following highly relevant reference:

Hanna et al. (2021) https://rmets.onlinelibrary.wiley.com/doi/full/10.1002/joc.6771

The green and blue lines on some plots look a bit similar; could they be distinguished more clearly?

l.496: please add the following highly relevant reference to “more persistent circulation regimes under global warming”:

Overland et al. (2012) https://agupubs.onlinelibrary.wiley.com/doi/full/10.1029/2012GL053268

This manuscript presents an interesting analysis using the so-called ‘pseudo global warming’ approach to quantify the thermodynamic contribution to GrIS SMB changes. The manuscript is very well written, and the analysis is easy to follow. I especially appreciate the excellent Introduction and the Discussion sections. Below, I list some critics of the manuscript, which can be addressed in a revised version. I think these all fall on the minor side of the 'major revisions' and I am supportive of this paper’s eventual publication.

I am raising a potential issue with interpreting the ~62% reduction in anomalous surface mass loss under “preindustrial” conditions. As MAR is forced by ERA5 boundary conditions – and the PGW approach is designed to hold the synoptic evolution as similar as possible between experiments – the “62% statement” is inherently conditional on the imposed large-scale circulation. As such, the results quantify thermodynamic amplification given the observed circulation anomalies, but they do not quantify (and should not be worded as if they quantified) the forced versus internal origin of the circulation anomalies themselves, hence are not to be used as full attribution. This distinction should be made explicit in the abstract and conclusions wherever the “62%” number (and related statements about the “substantial contribution of external forcing”) are presented, to avoid the impression of a full causal partitioning of the observed SMB anomaly into ‘dynamic vs anthropogenic’. I’d suggest adding the phrasing for example ‘conditional on the ERA5 2000–2019 circulation’. In addition, consider revising the terminology around ‘anthropogenic’ versus ‘externally forced’ changes unless the perturbation is explicitly anthropogenic-only.

Second, I have a methodological question related to that the PGW perturbations applied at the MAR boundaries are constructed from long-term monthly-mean CESM-LE differences and then linearly interpolated to 6-hourly forcing. To me, this approach yields a regime-invariant mean-state shift and may therefore miss regime-dependent thermodynamic changes that are particularly relevant for Greenland melt and runoff (often a small number of high-impact events related to blocking or moisture intrusions). A single monthly-mean Δq applied to all synoptic situations can misrepresent how moisture and cloud emissivity change specifically during blocking/moisture intrusion events. In addition, extremes are not expected to scale with the mean: any change in the variance/skewness of specific humidity, temperature or coastal inversion will be missed by a monthly-mean shift. Also, a monthly mean perturbation does not preserve event-specific vertical gradients, which may influence cloud phase, boundary-layer stability and downwelling longwave. If the added/removed moisture in PGW1 is not representative during the high-impact synoptic regimes, then the inferred thermodynamic contribution might be biased high or low to some extent. As the manuscript emphasizes a moisture/downwelling-longwave pathway as a key mechanism, I would suggest demonstrating that the imposed monthly Δq (and associated radiative effects) remains representative during the circulation regimes that dominate extreme SMB anomalies, including the extreme years in 2012 and 2019. The authors could condition key diagnostics (near-surface q, integrated water vapor, downwelling longwave or melt onset) on circulation regimes (blocking days vs moisture-intrusion days) to show that the thermodynamic signal is robust across regimes; or provide sensitivity tests using alternative ways of the perturbation (seasonal mean deltas or smoothed daily climatological deltas) to assess how sensitive the ~62% percent reduction is to the monthly-mean assumption. In any case, some discussion on that the current method does not capture changes in the variance could help.

Third, I would be cautious about interpreting the results from the current experimental design as sea-surface conditions exert only a minimal influence on SMB. I think so, because of a lack of atmosphere-only runs (retain CTRL sea-surface conditions (ERA5 SST/SIC) rather than swapping to Hadley-OI 1880-1899 SST/SIC). The manuscript interprets PGW1 as the total thermodynamic contribution and PGW2 as the SST/SIC-only contribution. However, without an atmosphere-only PGW experiment (T/q perturbed with modern SST/SIC), it is not possible to say whether marine boundary effects depend on the atmospheric background state (or to quantify the interaction term between marine boundary changes and the atmospheric background state).

Once PGW_atm exists, you can do the separation: CTRL (modern atm + modern SST/SIC), PGW2 (modern atm + PI SST/SIC), PGW_atm (PI atm + modern SST/SIC), and PGW1 (PI atm + PI-like SST/SIC), one can estimate

• an atmosphere-only main effect as PGW_atm minus CTRL
• a marine-only main effect as PGW2 minus CTRL
• a nonlinear interaction term as PGW1 minus PGW_atm minus PGW2 plus CTRL

The interaction term is especially important given the authors current discussion of katabatic wind adjustments and marine-gradient effects (PGW2) versus water-vapor/longwave effects (PGW1): those pathways might not add linearly. Should the full 2000–2019 reruns be too expensive, a compromise is to run PGW_atm for (a) May–Sep only, or (b) a targeted set of years (e.g., 2012, 2019 plus a few 'typical' years) and show whether the inferred “minimal marine influence” and melt-timing conclusions hold once the interaction term is quantifiable.

Additionally, a comparison between 500hPa geopotential heights or the GBI between the CTRL and all PGW runs would be nice. Just to rule out that by adding a vertically varying T/q perturbation does not influence u/v (by changing pressure gradients) too much (which is assumed in the current manuscript).

My last concern is that CTRL uses ERA5 sea-ice concentration as the modern forcing baseline, and any systematic bias in ERA5 SIC relative to satellite-based products (NSIDC) would directly affect the magnitude of PGW2-minus-CTRL (potentially biasing the conclusion toward a small marine effect if CTRL SIC is already too ice-covered, or inflating it if too low). While Fig. 3 usefully motivates why applying CESM SIC deltas directly can create ice-edge artifacts, it does not validate the modern SIC forcing against independent satellite products. I would suggest including a brief evaluation of ERA5 SIC against a satellite benchmark in the key seas and seasons that matter for Greenland moisture intrusions.