This is a high-quality piece of work that advances both process understanding and practical modeling approaches for coastal sea level. The suggested revisions are mostly clarifications and modest quantitative additions rather than new analyses. Once the IB handling is clearly explained and a few supporting quantifications are added, the manuscript will be a valuable contribution to the coastal ocean modeling and sea-level forecasting literature. I am happy to review a revised version.

1. In Section 2.2 and the results, the authors state that “both SPEAR and NWA12 oceans do not feel atmospheric pressure variations” and therefore add the IB effect offline for comparison to GESLA observations. This needs careful clarification.

• In the coupled SPEAR system, does the saved sea level field already include the IB response to the atmospheric pressure field, or was it excluded/post-processed? If SPEAR sea level already contains the IB signal, adding it again would double-count the contribution.
• Please explicitly state how the IB term was calculated (which pressure field, reference pressure, etc.) and whether high-frequency (sub-daily) pressure variability was neglected. This matters most at higher latitudes where IB can explain ~33% of variance.
• A short additional sentence or two explaining why pressure forcing was omitted (or not saved) in the NWA12 configuration would help readers understand the experimental design.

1. The claim that downscaling “enhances variability by nearly an order of magnitude across all resolved frequencies” is central to the paper and visually supported by the spectra. However, it would be much stronger if supported by quantitative ratios.

• Please add a supplementary table or a small panel showing NWA12/SPEAR variance ratios at the tide-gauge stations for the key frequency bands (or at least for the 5-day–2-week and >10-week bands).
• In Figure 6, the difference maps are shown after coarsening NWA12 to the SPEAR grid. It would be helpful to also show (or describe) the raw high-resolution NWA12 variance field so readers can appreciate the full magnitude of the enhancement before any spatial averaging.

1. NWA12 and SPEAR differ in horizontal resolution, bathymetry, and likely in some aspects of vertical mixing, bottom friction, or tide implementation. Although the use of identical surface forcing helps isolate the ocean response, the paper should briefly acknowledge that not every difference is purely attributable to resolved shelf/slope dynamics. A short sentence in Section 2.1 or 4 noting that the dominant differences are still expected to arise from bathymetric resolution and the ability to represent coastal trapped waves and cross-shelf transport would be sufficient and intellectually honest.
2. The 5th and 95th percentiles in Figures 10–12 are based on roughly 150 daily values per lead month (5 members × ~30 days). This is acceptable, but the tails are sensitive to sample size.

• Please add a brief comment on the robustness of these percentiles (e.g., via bootstrap resampling across ensemble members or years, or by noting that the patterns are consistent across individual ensemble members).
• Consider also showing the inter-ensemble spread (shading) on the percentile curves in Figure 12 or in a supplementary figure.

1. The introduction and conclusions position the work as a step toward a “practical time-varying statistics” framework for forecasting. This is a fair aspiration, but the current experiments are 1-year retrospective hindcasts initialized on 1 December.

• A short paragraph (or expanded sentence in the conclusions) discussing computational feasibility for true operational use, the need for real-time bias correction or anomaly nesting, and the missing ocean–atmosphere feedback would strengthen the applied relevance without over-selling the current setup.
• The ocean-only configuration means that SST differences can alter surface heat fluxes even though the wind field is identical. While this is probably secondary for shelf sea level, it is worth a one-sentence acknowledgment.

1. Summary and Overall Assessment

This manuscript evaluates a 100-member ensemble of one-year dynamical downscaling hindcasts for the period 1999–2018 along the U.S. East and Gulf Coasts. The hindcasts are produced using the high-resolution, 1/12° Northwest Atlantic regional ocean model (NWA12), driven by retrospective seasonal forecasts from the global coupled SPEAR model, which has an atmospheric resolution of 0.5° and an ocean resolution of 1°.

The authors investigate how increased ocean-model horizontal resolution and improved representation of continental-shelf and slope bathymetry affect subannual coastal sea-level variability and short-term daily extremes.

Overall, this is a well-designed, timely, and insightful study that addresses an important gap in coastal sea-level forecasting: the need to connect global climate and seasonal prediction systems with fine-scale ocean dynamics over the continental shelf and slope. The methodology is robust and makes effective use of a comprehensive 100-member ensemble dataset. The manuscript is logically organized, and the figures are generally clear and of high quality.

The physical interpretations linking model resolution, shelf hypsometry and bathymetry, coastal-trapped waves, and western boundary-current behavior are physically sound and well supported by the results. The study also provides useful and actionable insights for regional coastal-risk assessment and the prediction of extreme water levels.

Recommendation: Minor Revision. The manuscript is suitable for publication after the authors address several methodological clarifications, expand the discussion of certain physical mechanisms, and correct a small number of technical and typographical issues.

2. Major Comments

2.1 Uncoupled Air–Sea Interaction and Surface-Stress Formulation

The authors acknowledge in Section 2.1, Lines 97–104, that NWA12 is an ocean-only model forced by atmospheric fields from SPEAR. Consequently, regional ocean sea-surface temperatures and currents do not feed back onto the atmospheric circulation or surface winds.

Please clarify whether the wind-stress calculation in NWA12 accounts for relative air–sea velocity, that is, whether the stress is calculated using surface wind velocity minus ocean surface-current velocity. In regions of strong horizontal shear, particularly near the Gulf Stream, current–wind stress feedback can substantially influence upper-ocean energetics and shelf–slope exchange.

A brief statement indicating whether absolute winds or relative winds are used in the NWA12 bulk-flux formulation would strengthen the methodological description in Section 2.1.

2.2 Treatment of Tides and Nonlinear Tide–Surge Interactions

NWA12 includes tidal constituents, which are removed offline using UTide before the model output is averaged to daily resolution. In contrast, SPEAR does not explicitly resolve tides.

Nonlinear tide–surge interactions, including the modulation of bottom friction by tidal currents, can influence non-tidal residual sea level in shallow coastal regions. The authors should briefly discuss whether some portion of the enhanced coastal variance in NWA12 relative to SPEAR could arise from nonlinear tidal interactions represented in NWA12, rather than solely from improved bathymetric resolution, shelf dynamics, and wind-driven Ekman transport.

The authors do not necessarily need to quantify this contribution but acknowledging it as a possible source of difference between the two models would provide a more complete interpretation of the results.

2.3 Temporal Resolution of the Inverted Barometer Correction

The inverted barometer effect is added offline using daily averaged atmospheric surface pressure from SPEAR.

Because synoptic storms and coastal-flooding events often involve substantial pressure changes on hourly to six-hourly timescales, the use of daily averaged pressure may smooth short-lived pressure minima. Could this procedure lead to an underestimation of the upper tails of the daily sea-level distributions, particularly in Figures 10 and 12 and at higher-latitude stations such as Boston and Portland?

Please clarify whether higher-frequency pressure fields were available and, if so, why daily averaged pressure was selected. At minimum, the manuscript should acknowledge the potential effect of temporal averaging on the representation of extreme sea-level events.

2.4 Coastal-Waveguide “Choke Point” Near Cape Hatteras

The manuscript identifies Cape Hatteras as a critical geographic transition where the continental shelf narrows, and the Gulf Stream separates from the coast. The discussion in Section 3.3 would benefit from a more explicit physical explanation of why SPEAR performs poorly south of Cape Hatteras.

Please discuss whether the 1° SPEAR ocean grid is too coarse to resolve either the relevant coastal Rossby radius of deformation or the physical width and bathymetric structure of the narrow continental-shelf waveguide. Such a discussion would help clarify the spatial-resolution threshold required to represent coastal-trapped-wave propagation and related shelf dynamics in this region.

It would also strengthen the broader interpretation of why dynamical downscaling provides substantially greater benefits in some coastal regions than in others.

3. Minor Comments and Technical Corrections

Line 248: 

“...after removal a monthly seasonal climatology...”

to:

“...after removal of a monthly seasonal climatology....”

Line 411, References: In the citation for Wise et al. (2020), “oddshore-forced” should be corrected to “offshore-forced.”

Please ensure that the terms “non-tidal residual” and “sea-level anomaly,” as well as the abbreviations NTR and SLA, are used consistently throughout the text, figure legends, and captions. In particular, the terminology appears to differ between Figure 3 and Figures 10–11. If the terms refer to distinct quantities, the distinction should be clearly defined; otherwise, consistent terminology should be adopted throughout the manuscript.

This manuscript presents a useful comparison of the representation of coastal sea-level variability along the U.S. East and Gulf coasts in a high-resolution regional ocean model (NWA12) and its coarser parent model (SPEAR). The 20-year, five-member ensemble is a clear strength, and the paper addresses an important problem for coastal sea-level modeling and potential forecasting applications. I found the study interesting and generally well motivated, and I hope that the framework is used more extensively going forward.

The manuscript occasionally makes stronger interpretive and forecasting claims than the analysis fully supports. In particular, the paper emphasizes improved predictability or forecast relevance, but it does not formally evaluate forecast skill (or even correlations/RMSE for hindcasts, which I think is an easily achievable improvement). I also think the mechanistic interpretation relies too heavily on alongshore winds without fully isolating causality (or its relationship to the spectral analyses), and the manuscript would benefit from a more quantitative treatment of uncertainty and ensemble spread. 

Major comments

1. Forecast-skill language should be more carefully qualified.

The paper does show improved hindcast fidelity and more realistic variability in several respects, but it does not demonstrate event-by-event forecast skill. I recommend that the authors soften the language throughout the abstract, discussion, and conclusions so that the distinction between hindcast fidelity and forecast skill is explicit.

Suggestions for the authors: replace broad forecasting claims with phrasing such as “forecasting-relevant hindcasts” or “frameworks that may inform forecasting". Also, see later suggestion about correlation analyses that can enhance the paper's relevance to forcasting.

2. The mechanistic interpretation is too strongly centered on alongshore winds without fully demonstrating causality (or its relationship to the spectral analyses).

The Methods emphasize alongshore wind stress as a key diagnostic. In the Results, the discussion of Atlantic City and Charleston again leans on wind-stress regressions and correlations (p. 8-9, lines 175-195). The Conclusions then state that the observed differences are attributed to the “differing resolution-dependent ability of along-shore winds to excite cross-shore transport and along-shore wave propagation” (p. 16, lines 257-260).

This interpretation is plausible, but I do not think the analysis as presented isolates winds as the dominant mechanism. The title and abstract emphasize shelf and slope ocean dynamics, and the paper itself also discusses boundary currents and shelf-slope structure, yet the quantitative attribution remains limited. In my view, the current wording risks sounding more definitive than the evidence warrants.

Suggestions for the authors: as much as possible, add quantitative evidence such as variance-explained diagnostics, coherence/cross-spectral analysis, or a partial attribution framework that separates wind forcing from shelf/slope and boundary-current effects.

3. The paper would be stronger with a more quantitative uncertainty analysis.

The ensemble design is an important strength, but most of the analysis is presented through ensemble means and qualitative comparisons. This is evident in Figures 5, 10, 11, and 12, where the ensemble-mean behavior is emphasized, but uncertainty bounds, confidence intervals, or ensemble spread are not clearly summarized in the text. The Results do note that the spectral and variance differences appear across all ensemble members or multiple initialization years (e.g., p. 7, lines 150-155), but the manuscript does not show the degree of consistency in a compact quantitative way.

Suggestions for the authors: add a table reporting station-level metrics such as mean spectral ratio, variance ratio, correlation/coherence, and/or ensemble spread, together with confidence intervals or another uncertainty measure for the key comparisons.

Specific comments

Abstract (p. 1, lines 7-17)

- “forecasting framework” should be softened. Perhaps "framework suitable for forecasting".

- “particularly from an extremes perspective” would be clearer if the relevant timescales are stated directly.

- “nearly an order of magnitude” would be stronger if quantified more precisely.

- “practical” is vague and should be replaced with a more specific description of the intended utility.

- add "that the" before "added"

- "developed with" -> and"

Introduction (p. 1-2, lines 19-30 and 32-35)

- The introduction, before line 48, could use a fair bit of refocusing. In particular, I think the second half of the first paragraph is misdirected, or at least confusing. The cited approaches (CORA/statistical) actually do account for coast-to-open ocean processes. It's the large-scale models that don't represent them. Furthermore, I don't agree with the necessity of resolving the coast-to-open ocean transition to gain meaningful skill. Maybe to understand the processes underlying such skill.

Methods (p. 4-5, lines 85-125)

- Please state more explicitly how winds were interpolated to the NWA12 grid.

Figure 3 and related discussion (p. 6, lines 130-137)

- Figure 3 appears important, but the discussion moves quickly from the time series to the spectra. I recommend including correlations, and possibly coherence or cross-spectral measures, to bridge the gap between visual time-series agreement and the later frequency-domain analysis.

- Is the light blue line really showing non-tidal residuals? What's causing the diurnal variability?

Frequency spectra and band-passed variance (p. 7, lines 140-171)

- The frequency bands are useful, but they should be defined consistently and linked more explicitly to the physical interpretation. (Note lines 154 and 164 state two different frequency bands that we "expect" to resolve).

- The comment that NWA12 adds grid-scale variance through more realistic mesoscale eddy turbulence is plausible, but the impact of those eddies on coastal sea level is not clear.

- Strongly recommend adding a small table with summary statistics by station, and some interpretation.

  - Add uncertainty ranges, ensemble spread, or confidence intervals for key comparisons: spectral differences, uncertainty across ensemble members, significance of latitude-dependent changes, station-to-station variability

  - Highlight site by site differences: Why is SPEAR so much better at Charleston (and maybe st petersburg) than elsewhere south of Hatteras?

  - shouldn't the observational spectra vary depending on start date? why not include that range? 

Wind-stress regression analysis (p. 8-9, lines 175-195)

- The alongshore-wind focus is interesting, but I suggest stating more clearly why this is the key diagnostic and what it can and cannot show.

- Interpret the regression coefficient in terms of added noise or weaker signal.

--  Strongly recommend at least avariance-explained metric

-- line 195: this seems like a key point that remains ambiguous. With the addition of some analysis of the variance explained by wind I think the figure will be sufficient to look at differences between spear and NWA. However, the increasing and more uniform regression coefficients as a function of time scale is going to be really tough to disentangle from the changing (increasing spatial coherence) of winds. I wonder if there is a better way to do the analysis, or to have a supplementary analysis of the fingerprint of wind/spatial decorrelation scale at lower frequencies.

Seasonal distributions and extremes (p. 13, lines 217-240; p. 16-17, lines 251-273)

- The section would benefit from a clearer purpose statement at the start, and some connection to the spectral (and if added, other time-series analyses).

Discussion and conclusions (p. 17, lines 266-281)

- The ending would be stronger if it concluded with one or two concrete implications for coastal forecasting and flood-risk applications. For example, what are the implications for a statistical transfer function? Minimum resolution? Are results generalizable to other coastlines? Etc.

- Operational relevance should be stated carefully and conservatively.

- I would replace “dynamically downscaled forecasts” with “dynamically downscaled simulations” unless the paper directly evaluates forecasts.

There are quite a few typos that should be cleaned up -- I have noted them in some cases.

- “underpredction” should be corrected to “underprediction.”

- “frequencieis” should be corrected to “frequencies.”

- “conclusiosn” should be corrected to “conclusions.”

- Please check for other minor grammar issues such as missing articles, extra “that,” and inconsistent capitalization of place names.

Figure captions are relatively terse. if possible, please make captions more self-contained and define abbreviations.

Final assessment

I think the paper addresses an important and timely question, and the ensemble hindcast experiment is a real strength. My concerns are justified, but they can be addressed with modest revisions: more careful language about forecast skill, stronger mechanistic support for the wind-based interpretation, and a more quantitative uncertainty analysis. With those changes, the paper would read as more rigorous, more balanced, and more convincing.

An analysis of dynamically downscaled seasonal predictions from SPEAR global seasonal predictions using regional MOM6 is presented. The downscaled predictions are compared with the native global predictions to show the benefit of downscaling. Improved spatial resolution in MOM6 allows realistic bathymetry and an enhanced shelf response to overlying winds. These improvements then lead to improved coastal sea level characteristics in the downscaled predictions. The presented analysis shows mechanistic underpinnings of the open-ocean to coastal dynamical transition which I believe adds to our understanding of the added value of dynamical downscaling. The manuscript is well composed and focused. I have only minor comments. It would help the readers if the authors consider the following comments and suggestions regarding their manuscript:

Methodology:

How were the SPEAR seasonal retrospective predictions generated? The authors, at multiple instances (Lines 119-120, 233-234), state that the winds in both SPEAR and the regional downscaled model are the same and hence any improvement in the quality of hindcasts has to be due to other factors or to the differing response to the same wind field. But, I believe the authors are aware that SPEAR is a coupled model and the SPEAR ocean would feed back onto the SPEAR atmosphere. Such feedback is, by design, absent in the regional MOM6 retrospective predictions. The authors point this out in Lines 97-100 but then still assert that both SPEAR ocean and MOM6 ocean see the same winds. I would suggest that the authors be careful about their statement that the atmosphere in SPEAR and the sampled (6-hourly or daily) atmospheric forcing from SPEAR, with which MOM6 was forced, are identical and hence the consequences on their interpretation of results.

Can the authors add an objective analysis to support that five ensemble members are sufficient for their seasonal prediction framework in the context of Figures 10, 11 and 12?

Results:

In Figures 6, 7, 8 and 9, observations-based maps and differences are not shown. The regression pattern in Figure 7 and 8 seems to be same in SPEAR and MOM6 with only the magnitude of the regression coefficients changing. It would help to see how much underestimation does SPEAR have and how much under- or overestimation, if any, does MOM6 have. Is the enhanced response of MOM6 to SPEAR-derived winds realistic?

I am not fully convinced with the reasoning to completely exclude the established deterministic and probabilistic skill metric to evaluate both SPEAR and the downscaled predictions against observations. What information do Figures 10, 11 and 12 convey that can not be summarized into a skill metric at each lead time? Is it the size of your ensemble that would prevent any meaningful estimate of the the skill, for example, of short-term extremes in coastal sea level?

Figures:

Figure 1: Are the NWA12 maps from the same 30-year ERA-forced simulation from which the initial conditions were derived for the downscaled predictions? Please add this detail in the figure caption.

Mention the frequency band in the caption for Figure 9

Mention that IB effect is included in SPEAR and NWA12 in Figure 12 caption

All figure legends, axis labels are too small to read on an A4 page, which some of us still read from.