This is an interesting and well-written paper, and I believe it will make a great addition to this journal. I have identified a few minor issues that I have noted below, but pending these, I believe that the article is suitable for publication.

Line 163: why only 100 times? Usually several thousand times are chosen

Figure 3: Is there a reason that the 25m RMSD contour line is highlighted? If so, state in the caption or main text.

Line 290: Could these anomalies not be further pockets of brine?

Figure 4: How was the extent of the hypothesized brine network chosen? There are many isolated anomalies (orange in Fig. 4e) within the location of the Ocb outcrop that are not identified as brine networks. How/why was this discrimination made?

Table 1 caption. ‘brackets’ should be ‘parantheses’

This manuscript reports on the results of a regional radar survey of the Devon ice cap. The data are interpreted in the context of prior work by the same team in which they proposed the presence of briny subglacial lakes in this study region. The results presented here broadly corroborate this prior contention. However, the authors also see evidence for extensive areas that are not lakes but likely brine-saturated sediments. Generally, the new dataset yields a detailed picture of the complex subglacial hydrology beneath the Devon ice cap and may be helpful in a range of glaciological and microbiological studies in the future. The manuscript includes an excellent discussion of the possible microbial habitats beneath the Devon ice cap and overviews their relevance to search for extraterrestrial life on icy planetary bodies.

Overall, I find this manuscript to be informative and worth publishing. I have several specific comments on the methods and results sections (see below). However, once I got to the discussion and results sections, they seemed to be very well crafted with proper caveats stated where they are necessary. The figures are loaded with information and clear. Citations are extensive and relevant. I did suggest a few additional papers that the authors may want to take into account. I do think that there are several places where more methodological rigor can be introduced and a few places where statements can be made in a more even-handed way. 

Specific comments:

Line 57: It is much more relevant to this study to give the radar wavelength in ice, not in air. 

Line 83: The significant difference between the median and the mean suggests that the cross-over errors are not normally distributed. I would be interested in including a histogram of the errors as a figure. Alternatively, the authors should at least point out the deviation of this distribution from the Gaussian distribution. This is important because it is enough for a standard normal distribution to give the mean and the standard deviation to describe the underlying probability distribution function fully. However, more complex distributions (e.g., multimodal, asymmetric, or skewed distributions) need to be described by more than just the two first moments. With non-Gaussian distributions, one also cannot assume that 68% and 95% of data fall within one and two standard deviations from the mean.

Line 94: This statement is not incorrect, but, in the context of this study, it sets up an unrealistic juxtaposition of subglacial conditions. Why would the subglacial bedrock be dry in the study area if there is so much water in lakes and sediments in the region? Ice over bedrock saturated with brine could produce higher radar reflection strength than ice over a subglacial lake filled with very fresh meltwater  (e.g., Tulaczyk and Foley, 2020). 

Line 113: It is entirely unclear how the authors choose where to draw the line designating Nh. Why is it chosen to be at such a value of correlation coefficient (ca. 0.1)? Why not at 0.2 or 0.3? Is the correlation coefficient magnitude here R or R-squared. Estimation of the attenuation coefficient is an important methodological step, and it needs to be fleshed out more than it is here. 

Figure 2: It is clear from the distribution shown in this figure that quite a range of quite different lines, representing different attenuation coefficients, could be fit reasonably well into this distribution. For one, there is a distinct peak to this distribution (at ca. -42dB and 480m), with the resulting linear fit being determined by extreme tales at low and high frequencies. I'm sorry, but I do not buy the relatively narrow uncertainty of 3.1 dB/km that the authors assign to their fit. Linear regression can be performed in a way that yields the uncertainties in the two parameters that define the linear fit (one of which is the slope of the line, from which attenuation is calculated). The authors need to report these statistically-based uncertainties on their attenuation estimates. The validity of the method used by Schroeder et al. (2016) may be dependent on the specific distribution of the bed power vs. thickness. In this case, this distribution does not support a tight linear fit. 

Lines 131-132: As in the dry bedrock example, the authors use an extreme end-member here and create a false sense of the singular relationship between high specularity and ice-on-water interfaces. In reality, ice overriding sediments can easily have a flat interface, particularly if the sediments are weak. However, I have seen even deglaciated granitic surfaces that are smooth enough on the scale of 1-10m that they would have high specularity. 

Line 156: The mean cross-over error of 17.6 m itself is associated with uncertainty. In reality, you do not know if it is 17.6 m or some larger or smaller value. This is why the concept of uncertainty propagation has been invented. Please, calculate the uncertainty of the mean cross-over error and propagate it into your calculation of uncertainties of the hydraulic head. 

Line 157: Similarly, the uncertainty of 0.5 m for the ArcticDEM seems unrealistic from my experience. The authors should look at independent estimates rather than just quote a potentially optimistic estimate produced by those who generated ArcticDEM. For instance, the analysis of Xing et al. (2020) suggests a 2-sigma error of about +-5 meters for the Greenland ArcticDEM analyzed by them. 

Lines 200-201: This statement is somewhat misleading. The paper by Peters et al. (2005) uses complex permittivity, which incorporates the effects of real permittivity and electrical conductivity on radar reflectivity of the bed. Yet, later (Line 203), the authors interpret the observed spatial variations in the basal reflectivity as transitions between wet and dry bedrock conditions. Whereas this simplified interpretation is commonly used, it is not strictly correct, as pointed out in Tulaczyk and Foley (2020) and in the open discussion to this TC paper. Spatial variations in relative bed reflectivity may be due to changes in the salinity of subglacial water, which influences the imaginary (electrical conductivity) component of complex permittivity. The relative amount of subglacial water (i.e., the wet vs dry language used here), influences the real part of complex permittivity. In reality, the authors could be looking at subglacial materials with the same amount of water but seeing very different radar reflectivities because in some places, this water is fresh meltwater, and in others, it is hypersaline brine. The effect of electrical conductivity seems particularly pertinent to this study, given that the authors propose that very hypersaline brines (five times more saline than seawater) are present in some parts of their study region. The role of electrical conductivity in the radar reflectivity of glacier beds needs to be tackled in this manuscript head-on. The authors cannot say in some parts of this manuscript that there are very saline (conductive) brines in the region and then default to interpreting bed reflectivity as if only the real part of complex permittivity mattered in radar reflection.  

Line 221: There is literature focused on estimating lake bathymetry from their size and the topography of lake surroundings (e.g., Heathcote et al., 2015). Perhaps the authors can lean on such prior research to get a better handle on lake depths? 

Line 231: Can you quantify how 'flat' or 'rough' on the scale of the radar wavelength does the ice bed have to be to yield specularity of >0.4? Just from intuition, it seems that 0.4 can still correspond to pretty rough surfaces. I am not that comfortable associating specularity of such low magnitude with only being consistent with ice-water interfaces. Again, ice-on-weak-sediments can make pretty flat interfaces too. Moreover, such an interface can be highly reflective. Particularly when the subglacial fluid is hypersaline and/or if the subglacial material contains clays (both are electrically conductive materials). Furthermore, an extensive area of weak subglacial sediments would lead to the ice surface slope being shallow, which would also result in hydraulic flatness. All three criteria for subglacial lakes used here can also indicate wet, weak sediments. 

Line 286: Can you elaborate why you do not think that there is a widespread area of wet conditions here? 

Lines 297-298: What about the possibility that less saline fluids (e.g., fresh subglacial meltwaters) cause the low bed reflectivity in this high specularity area? This seems like an equally plausible explanation as compared to the 'dry bedrock' one.

Lines 454-455: Three papers have been published in GRL this summer, casting doubt on the interpretation of high reflectivity anomalies beneath the Martian SPLD as liquid brines (Bierson et al., 2021; Khuller and Plaut, 2021; Smith et al., 2021