General evaluation

By analyzing the differences between two InSAR velocity fields in the north-central Gulf of Mexico, this manuscript highlights the reproducibility challenges arising from methodological choices in data processing, including filtering and instrumental, environmental and geophysical corrections. Such discrepancies have been noted in previous studies. The authors advocate for the development of a harmonized processing framework and for cross-validation exercises within the InSAR community, similar to existing initiatives in other Earth sciences areas such as climate science (e.g., CMIP for climate models) or geodesy (e.g., IGS for the GNSS), where such efforts have led to the definition of minimum agreed-upon modelling standards. An open question, however, is whether the InSAR community is currently sufficiently mature and organized to mobilize the resources required to establish such a framework.

In the absence of such coordinated international efforts, meaningful inter-comparisons will remain challenging, given the inherent complexity of InSAR processing the multitude of possible methodological differences. The authors make a commendable effort to identify which discrepancies can be considered negligible in order to enable a meaningful comparison. While I am not fully convinced that all such differences are adequately accounted for, their attempt is valuable and their experience worth sharing.

In this context, I have several concerns regarding the GNSS data used to assess the two InSAR velocity fields. First, it is unclear whether the GNSS observations used for validation are fully independent from those used to calibrate the respective InSAR products. More specifically, are the 41 GNSS stations used in the comparison distinct from those employed to align the InSAR products to their reference frames?

Second, regarding the use of NGL GNSS velocities, it would be useful to assess how these compare with independent solutions, particularly those produced by groups using different processing strategies, software, or orbit and clock products (e.g., not relying on JPL products). 

Another point concerns temporal variability and the use of two different time spans (2007- 2020 and 2017-2020). The authors conclude that the impact of this difference can be neglected. However, Figure S7 appears to show a systematic bias, with the shorter time span exhibiting larger subsidence rates than the longer one. Unlike the more localized (individual) discrepancies, this overall shift seems significant. It could even be more pronounced if time periods of equal duration were compared (e.g., 2007-2010 versus 2017 to 2020) if the underlying geological process is accelerating. I encourage the authors to further investigate and discuss this aspect.

Recommendations for improvement (specific points)

To strengthen the manuscript and improve readability, I suggest addressing the following points (minor).

Table 1 appears both in the main ma,nuscript and in the Supplemental Material.

Figure S1: please consider adding GNSS station identifiers to the map (see data file in Supp.). Given the relatively limited number of stations (41), the map should remain readable while providing useful detail for reproducibility. A similar comment applies to Figure 5, which includes even fewer stations.

Figures S3: confusing, please revisit panels and captions.

Please verify the reference frame of the daily GNSS data from NGL. I found indications that they may be aligned to IGS20 rather than IGS14. While differences between these frames are likely negligible compared to other sources of uncertainty, this should be clarified.

Section 3.2: the mean record length is reported, but the median record length would be a more robust and informative statistic.

Concluding remark

Overall, the manuscript is well written, clear, and logically structured, making it easy to follow. The topic and the material are stimulating, and the authors draw on extensive experience and expertise in assessing the respective strengths and limitations of InSAR and GNSS. Their effort to compare products that are inherently difficult to reconcile, due to the complexity of InSAR processing, is commendable. The manuscript provides interesting insights, particularly regarding land coverage distinction and the specific GIA context, both of which merit further investigation. The statistical analyses are applied rigorously and appeared sound overall. I believe the manuscript can be further strengthened by addressing the points raised above, as well as the more detailed comments provided.

This is an important study that should be published. The authors review two recent publications that use InSAR (interferometric synthetic aperture radar) to assess coastal subsidence, and point out various discrepancies between the studies.  This kind of rigorous comparison is long-overdue, as InSAR-related studies have proliferated, sometimes with conflicting results.

I just have a few comments/suggestions the authors may wish to consider.

1. Figure 2 is a good summary of the paper. The best fit lines could be omitted, I don’t think they add much, but I leave that to the authors’ discretion. One statistic I would like to see here is the RMS difference between the 1 to 1 line and the combined InSAR data. Without any judgement as to which InSAR study is better, that single number gives a rough estimate of the utility of the InSAR approach in the various types of terrain. It’s pretty clear the technique works well in developed areas (Figure 2e) given the presence of numerous strong scatterers, as the authors point out.
2. Tropospheric error: the authors point out that errors related to tropospheric water vapor could bias the InSAR results. This is true, but there are ways around this problem – see for example Zebker et al. (IEEE Trans Geosci & RS, 2023). So it’s worth considering in some detail how the two InSAR studies being assessed dealt with the problem. I agree that if not done carefully, this is certainly a potential source of error.
3. Section 3.2: re: GNSS measurements restricted to VLM: Karegar et al (GRL, 2020) attempted to quantify this aspect of the problem. While their analysis was restricted to just a few sites, I believe their results support the point you are making here.
4. Section 3.2, exclusion of Texas sites: this is unfortunate, as the western part of the state is characterized by relatively dry landscape with limited vegetation, hence optimum for InSAR. It may be worth pointing out that petroleum-related activities can sometimes lead to uplift, in the case of fluid injection for fracking, waste water injection, or secondary oil recovery. It’s possible to match injected volumes to observed uplift with physically plausible models, providing some verification.  See for example Deng et al (JGR, 2020).
5. Section 3.5 (GIA): Do the results of Zumberge et al (JGR, 2022) bear on this issue?

6. I suggest adding a separate section describing how the two InSAR studies deal with the issue of reference sites (this is separate from reference frame). This is an obvious source of mismatch between the studies. Unlike GNSS, InSAR is a relative technique. To turn InSAR data  into rates of VLM or SEC, it is necessary to make some assumptions concerning a stable area (VLM/SEC assumed to be zero) to which the rest of the results are referenced, or one or more GPS/GNSS sites whose rates of motion are well understood, and a least squares or similar adjustment is applied to minimize misfit between the reference sites and the larger data set. If the latter, then the difference between VLM and SEC, as well as the anchor depth of the GNSS monument, is certainly relevant.