The manuscript "Finely-resolved along-track wave attenuation estimates in the Antarctic marginal ice zone from ICESat-2" by Voermans et al. evaluates wave attenuation rates from a novel dataset in the Antarctic marginal ice zone (MIZ), based on measurements from ICESat-2 (IS2). This is a revised manuscript based on comments from two reviewers, and I did not review the original manuscript; however, I will consider the authors’ responses to previous comments from Reviewer #1 as part of my assessment of the manuscript.
Unfortunately, my general outlook of this study is not particularly favourable. I appreciate the work done here, and I believe the authors were trying to conduct a thorough analysis. However, it seems that the manuscript is subject to some inherent flaws that are common to wave-ice literature and discussions of wave attenuation. Through some of their framing and analysis choices, the authors exacerbate some of these issues. Moreover, I felt that many of the previous comments from Reviewer #1 were not adequately addressed.
In many regards, I agree with the comments made by the previous Reviewer #1 and my comments below will reiterate some points that were part of the initial review. In fact, I formulated some of these comments before reading the initial review comments/authors’ responses, so the fact these points still came to mind highlights that the authors’ adjustments from the original manuscript were insufficient.
The biggest failings of the manuscript come from a number of assumptions made—either explicitly or implicitly—that could significantly impact the analysis, such as:
- Wave attenuation is exponential
- Wave direction is aligned with the satellite track
- Waves energy at some point in the ice only depends on along-track attenuated energy
- The MIZ width as defined by the waves (i.e., xMIZ) is a tangible quantity
The authors justify some assumptions based on similar use in past studies, some of which are quite common (e.g., exponential attenuation), and spend some time discussing the impacts of some of their choices (e.g., §3.2 discussing the sensitivity of wave direction). My major comments, below, largely discuss my issues with these assumptions and how they were applied.
Major comments:
1. Exponential attenuation: The authors make the common assumption of exponential wave attenuation between each set of points in their tracks and thus calculate alpha(x) along each IS2 track based on two-point differences (eq. 2), a method commonly adopted for buoy measurements. Since continuous along-track data is available, the choice of eq. 2 is not an appropriate choice to determine an attenuation coefficient--they should instead fit an exponential function to their curves (or to subset regions of each curve) and assess the goodness of that fit. However, it is clear from the example tracks that they've shown (figs 1,3-6) that along-track attenuation is rarely, if ever, exponential in form, which would be reflected in any goodness-of-fit tests performed. In their responses to the previous Reviewer #1 (who raised a similar point), the authors assert that the attenuation is indeed exponential locally, but that spatial heterogeneity in sea ice properties (and thus the values of alpha) consistently occur over small enough scales as to obfuscate any ability to see an exponential decay. This is certainly reasonable for the imagery that they show in fig. 5a, but it is not obvious if this would always true in general. In many cases, satellite imagery might suggest that sea ice concentration (SIC) or floe size distribution (FSD) might frequently be (statistically) coherent for long ranges. If the authors are going to maintain there assumption of exponential decay and use of eq. 2, they should, to the degree possible, quantify (or reference) the decorrelation scales of sea ice properties, showing that those properties vary on scales comparable to their segment lengths (<=8km). Alternatively, they could acknowledge that the decay is NOT exponential but instead introduce alpha as an "effective" attenuation rate that--rather than being a physical effect--is a construct for evaluating wave height changes in the context of past literature. Currently, they provide no examples or evidence that support their assumption of exponential attenuation.
2. Wave direction: For simplicity, the authors assume that wave directions are aligned with the IS2 transects. The authors acknowledge some challenges associated with this choice in their §3.2, highlighting in particular how the combination of wave direction and ice cover heterogeneity can impact the interpretation of attenuation rates. Though, in §3.3, they go on to state that because there is no expected correlation between IS2 track direction and local wave conditions, both overestimates and underestimates of the attenuation rate could be included due to this effect, and so an average attenuation is still instructive. The authors also briefly include a statement (on L116) indicating that the assumption likely means that attenuation rates are underestimated (due to incorrect values of Delta x in eq. 2). This effect would not be corrected by averaging over many IS2 tracks and instead would lead to a systematic bias. Some rough estimation of the magnitude of this error should be performed; for example, by looking at the relative difference in direction between IS2 tracks and wave direction at the sea ice edge taken from re-analysis. More problematic is that the authors fail to explain how the wave direction assumption impacts their results in regard to wavelengths/periods. In the study, attenuation is calculated for four different wavelengths/periods, and statistics are aggregated for each wavelength/period (fig 7), and compared to past literature on frequency-dependence (fig 9). However, the apparent along-track wavenumber is systematically longer than the true wavelength by an amount that will depend on the wave direction/IS2 track misalignment and varies for each track—so the aggregate results are likely combing data across different wave periods. As shown by Hell & Horvat (2024), the apparent wavelength along IS2 tracks can be more than double the value of the corrected wavelength when wave direction is accounted for. The choice to assume that wave directions are aligned with the IS2 transects is inappropriate given that methods are available to estimate wave direction for these data (and these methods are cited in the manuscript).
3. Along-track attenuation only: Inherent in the analysis process in this study is the common assumption that the wave energy measured at some point in the sea ice, “B,” depends only on the attenuation of energy from some point, “A,” earlier in the track. Leaving aside the validity of the assumption that wave directions are aligned with IS2 tracks, this ignores that waves in open water could be coming simultaneously from a variety of different directions and that the waves are directionally spread, so that waves at point “B” are influenced by a wide, two-dimensional upstream region (e.g., see Figure 1 in Herman, 2024). In addition, the analysis ignores the potential for local wave generation within and between the sea ice (Li et al., 2015; Cooper et al., 2022; Brenner & Horvat, 2024), which could change the apparent attenuation rates (and, in addition to the reasons stated in the manuscript, could also be a source of negative attenuation).
4. MIZ Width: While I appreciate the challenges associated with defining a “wave-affected MIZ” width (rather than other MIZ metrics, such as SIC-based), I am a little unsatisfied with the defined xMIZ used in the present study. Since nearly all results are plotted in normalized coordinates of x/xMIZ, this definition becomes important. First, there is some inconsistency in the description of this definition: in L86-87, the authors quote Brouwer et al. (2022) in a definition of MIZ width based on significant wave height, but in the following line, they mention using the median of the set of widths determined at different wavelengths. Are the two definitions equal? More fundamentally, this definition of xMIZ depends on (a) the signal-to-noise ratio (SNR) of a given instrument, (b) the incident wave energy, and (c) the mean along-track attenuation rate. The inclusion of (a) makes this especially problematic because it stops being a physical quantity and starts being dependent on the measurement platform and analysis techniques. The dependence on the mean along-track attenuation rate (c) makes it feel like there is some circular argument when you then compare attenuation rates to x/xMIZ. The authors state in the manuscript and in their reply to questions from Reviewer #1 that the definition of xMIZ is close to corresponding to where variance in each profile becomes ice-roughness dominated---perhaps a better definition would be based on that fact (e.g., when the ratio of wave-dominated variance to ice-dominated variance reaches some threshold?), though that doesn’t solve the potential issues in other applications of xMIZ in models (as mentioned on L270-271).
5. The authors decide to consider their results all as a function of a normalized distance, x/xMIZ, without stating any reason to expect that the attenuation rate should vary with x/xMIZ. The authors should demonstrate that alpha vs x/xMIZ does better than just alpha vs x. Also, they indicate throughout that alpha varies depending on the inhomogeneity of the sea ice and imply that this exists over relatively small scales. However, by suggesting that alpha is a function of x/xMIZ, they imply that all of the sea ice heterogeneity is also a function of x/xMIZ, and so, in some statistical way, it is not actually that heterogeneous and the variations in ice properties are effectively smoothly varying. Moreover, the authors state that x/xMIZ has better predictive power than either SIC or sea ice thickness (SIT; on L198-199), but to my eye, the correlations in figs 6a,b, and c all look comparable. It would be interesting to see how statistics of sea ice properties (SIC or SIT) vary as a function of distance into the ice. If interesting, then a further seasonal breakdown of SIC & SIT vs distance seasonally to accompany fig. 8 would also be useful, given that the explanation for seasonal variations as seen in the figure relies on differences in ice conditions between seasons.
Of the above, comments 1–3 reflected methodological flaws that I think should be addressed or the impacts on the results better explained in the text. In particular, without currently accounting for wave direction, it is incorrect to do any analysis relying on wavelengths/periods/frequencies (comment 2). In contrast, comments 4–5 could potentially be considered in the context of framing. For example, the L260-265 frames the results as useful for model parameterization, but due to issues with the definition of xMIZ (comment 4), this is unlikely to be true. Instead, per comment 5, this may tell us something about the average variability of the sea ice.
Other general comments
- How do you define the sea ice edge (x=0)? Is that SIC-based? Do you use a threshold (e.g., 15%)?
- Why only consider 4 discrete wavelengths instead of a full spectrum? Even if not assessing full spectral attenuation, it would be interesting/instructive to show a few spectra along a track in one of the example track figures (e.g., in fig 3 and/or 4)
- In light of the results from Thomson et al. (2021), you should mention the expected spectral shape of the noise from these measurements.
- The remote sensing products used (SAR imagery, SIC, and SIT) should be introduced in the methods section, along with associated uncertainties (particularly for SIT).
Specific comments
- Fig. 2: I would be helpful to also show the ice edge position for each of the months shown.
- L157: This equation is produced somewhat out of the air here. Only afterwards is there a reference made to an appendix where it is (somewhat) explained. I would reorganize the description of this approach so that readers aren’t left wondering what this “proxy attenuation” is. Explain what it is in principle, then refer to appendix, and then (if still necessary) include the equation.
- L175: You can't claim that accounting for misalignment doesn't improve things just because it didn't in this case (where you used a contrived attenuation function just for the purpose of demonstration).
- Fig. 6: Why show grey shading for percentiles in panel a, but for bootstrapping uncertainty in panels b-d? You should be consistent between panels. |
