Round 1

Reviewer 1 Report

The paper “Flexural Stresses in Basins due to Glaciations—an Example from the Barents Sea” by Løtveit et al. presents the results of a stress modelling for the Barents Sea. The paper discusses the effects of glacial loading/unloading on the migration of hydrocarbon. The study is based on results by Fjeldskaar et al. using glacial loading/unloading models to simulate the displacement changes. Here, the first and second derivative of the displacement are taken to analyse stress changes (as far as I could understand from the paper). The authors use several assumptions within this study (e.g., obtaining stress from second derivative of the displacement, ice loading at last glacial maximum only) and therefore neglect important processes (e.g., stress migration, isostatic behavior, time-varying stress changes). This makes the study, frankly saying, too simple and needs a complete revision and re-analyses, before it can be considered for publication. I must therefore recommend rejection and encourage the authors to work on the following points. I’m happy to read a revised version and consider this study for publication again.

The assumption of isostatic equilibrium during loading and unloading is completely unrealistic. If the lithosphere is already in isostatic equilibrium, then why do we see uplift in the formerly glaciated areas of North America and Northern Europe of several mm/year? The area around Umeå is uplifting by more than 10 mm/year (which is the largest GNSS signal in the vertical direction in Europe), Hudson Bay by 14 mm/yr, and show no sign that isostatic equilibrium has been reached yet. Isostatic equilibrium could be achieved when we apply a constant load for several 10,000 years (at least several million years most likely), but not for a changing load magnitude over such a short time frame. There is NO disagreement about the definition of the effective elastic thickness of the lithosphere. The effective elastic thickness of the lithosphere is more a material parameter related to the flexural rigidity and is related to the estimation of the rheology based on gravity and topography data. I encourage the authors to read papers by Evgueni Burov, Magdala Tesauro, Pascal Audet, and many others who discuss and estimate effective elastic thicknesses for specific areas but also globally. What the authors are talking about here is the definition of the elastic part of the lithosphere in GIA studies. This is a huge difference, see studies by Anthony Watts. The authors should be aware that the thickness of the lithosphere has several definitions depending on the timescale of the loading and the parameters used to estimate it. And yes, there is disagreement about the thickness of the lithosphere used in GIA studies, but this thickness is not the effective elastic thickness. The method for estimating stresses is completely unclear. Are the authors using the second derivative of the displacement (Fig. 5) as stress changes? If so, why are they no stress changes beneath the ice sheet? Why do you have stresses beneath the margin area only? Where is the ice sheet in Fig. 5? The study area is at the ice margin and I would expect to see a variation from compressional stresses to extensional stresses as you go from beneath the ice sheet to the peripheral bulge (or from extensional to compressional, if you follow the description after Stein). Why do you have only extensional stresses then? What is with the fault stability criterion? Seismologists are using the change in Coulomb Failure Stress to analyse the potential for fault reactivation. Please show a figure describing this parameter. A big problem in this paper is the apparent misconception regarding glacially-induced stresses. Glacial loading/unloading leads to stress changes in the vertical direction (due to the ice load, that are no flexural stresses) and in the horizontal direction. However, the horizontal stresses are not just due to the flexure, but also due to stress migration from the mantle into the lithosphere. Those stresses are important when assessing the stability of faults in currently and formerly glaciated areas. Please read Steffen et al. (2015, Tectonics) for a detailed description about glacially-induced stresses. The authors also estimate the stresses at LGM, as far as I understand the paper. What is with the ocean load? This is especially of importance for the Barents Sea, where the ice was surrounded by water. A thorough analyses of glacially-induced stresses for the Barents Sea has to include the ocean load, especially in dependence of time. The figures were prepared apparently in a hurry and are not of enough quality that is used for scientific papers. All geographical figures miss longitude and latitude (expect Fig. 1 showing latitudes somewhere inside the figure, but hard to see). A colorbar is mostly missing or almost impossible to identify. Descriptions of geographical areas in white over white areas are not possible to see. In general, descriptions are rather small and could be extended and more geographical features added. All geographical features named in the paper should be marked on a map. There is no consistent colorscale between the figures (in particular, between Figs. 2 and 8). The usage of a, b, c or something similar is also suitable for most figures and makes reading them easier. I’m actually wondering, how experienced authors (as it is visible from the reference list) are able to submit a paper with such low-quality figures.

 

In addition, I have several minor comments:

Lines 38/39: There are earlier studies (from before 2009) that discuss the development of stresses due to unloading/loading (e.g., by Patrick Wu, Björn Lund). Line 52: The paper by Lund does not describe locations of glacially-induced faults and the papers 15 to 19 are more qualified for this list. In addition, the studies by Brandes et al. were completely ignored by the authors. Line 74: The models by Steffen et al. are also applicable to areas that are in the peripheral bulge and are therefore not only for areas once covered by continental ice sheets. Despite, the size of the ice sheet does not matter in their studies and the method is applicable to all type of ice loads. Line 94: I’m wondering why reference 35 is used here when the authors talk about the Eurasian Ice sheet. Line 130: How do you know that isostatic equilibrium is achieved in interglacial periods? The new glacial cycle could start before equilibrium is obtained. Figure 2: White box is hard to see. Is the white box the figure on the right? Please state this. Figure 3: What is HCWC? Comes later in the text but has to come here already. How do you come from the right-top to the bottom panel? Where is the ice sheet within these subfigures? Line 137: Do you mean after deglaciation with post-glacial time? If so, please say so. Line 145: “can be found” is written twice. Line 180: The description after Stein is valid only, if compressional stresses are assumed to be positive and extensional stresses negative. I also think that there are more recent and better descriptions explaining glacially-induced stresses than the one from Stein as the assumption of isostatic equilibrium is not correct for glacial loads over such a short time span (less than 1 million years). Line 198: Please list the parameters. Figure 5: Where is the ice sheet in this respect? Figure 6: What does this figure tell us? Is this stress state at LGM? How does this tell us something about the stress state during and after loading? Black square is hard to see. Line 224: Where is the Hoop Fault Complex? Line 237: Is the load a stress load? Provided in MPa? What is with the horizontal background stress? I think the vertical stress is included (according to the description in line 242) and is maybe equivalent to the overburden pressure. However, I’m not sure about this as this information is not provided. The entire stress modelling is unclear and maybe a sketch could be useful. Lines 277/278: I think the sentence was not finished here. Line 281: Is the GIA model not able to include time-varying ice-sheet geometries? Please clarify. Do I understand the authors correctly that the size of the ice sheet at LGM was used to estimate the stress state only and they use this time point to infer the stress state now? Line 288: Which data were matched? RSL, GPS, gravity, …? Line 291: I’m wondering a bit why the authors always claim that 30 km is the correct lithospheric thickness for GIA studies and now obtain a thickness of 70 km in a more recent study. I also think that the 70 km are highly relevant for the study here. It would be interesting to see the stress state also for 70 km. Line 316: Deposenters? Line 322: What are vertical flexural stresses?

Author Response

Please find our reply in the attachment.

Author Response File: Author Response.pdf

Reviewer 2 Report

Review of ms “Flexural Stresses in Basins due to Glaciations—an Example from the Barents Sea” by Ingrid Løtveit, Willy Fjeldskaar, and Magnhild Sydnes submitted to Geosciences.

The study presents the quantification of ice-sheet loading effects on geometry and stress pattern in the SW Barents Sea. Authors show that this effect may have influence on the basin in general and on hydrocarbon potential particular. The models and the results look simple and understandable and support the conclusion that someone indeed should estimate the effect. With some corrections and metallization of models, the study may be useful for bringing the attention to the topic.

I have several major issues with the work presented. First of all, I want to mention about the last section of my review (Line-by-line comments): the text is filled with many incorrect stamens and uncertainties, so that based on that alone I would suggest that the manuscript requires a major revision.

1. The models should be explain better

Tilting model. I still cannot find the source of ice thickness model for LGM. The main parameters here include not only EET, but density structure, e.g., water, ice, and mantle density. Usually, description includes approach used (thin elastic plate vs thick elastic plate vs shear deformable) and some words on model resolution.

Stress model. The geometry of the model is not explained at all (lateral size, depth). Theory (3D? elastic plate?) and resolution behind calculation is also not mentioned. Boundary conditions are also missing. The position of faults in regard to model depth is also not explained. In the description authors write about “adding (horizontal) load in a certain direction” – it is not understandable.

2. For the study presented numerical model there too few numerical estimations

The best example here is Fig. 3. Authors draw the conclusion about importance of tilting based on this figure, while no single number is presented. I see no problem to take at least a single example of the HC field in the area and quantify how large is the tilting.

Lateral length-scale on figures is missing (e.g., I cannot even approximate what 3 m/km means on the map, because I do not understand the extent of the map, is it 20 km or 300?). Generally, the absolute values or amplitude of the subsidence due to ice loading is missing, in general and in application to a particular HC field.

3. Section “Conclusions” does not present results of study

The final section is filled with unsubstantiated statements, which I found a bit wrong. The first paragraph deals mainly with glacial erosion, while no research about this topic was presented. The statements about stress evolution in the second paragraph are not supported. Third paragraph stated about amplitude of stresses, which is set absolutely arbitrary in the numerical model and thus words “greatly affected” is inappropriate here. I also question need for statements about future research in the last paragraph. I also have several questions to particular statements in the “line-by-line” comments. I suggest shortening conclusion section. If authors insist on keeping their speculative statements, I would suggest putting them into subsections above.

4. Very optional: comparison with study of the reviewer

Majority of the referred works in the presented manuscript supports the idea of importance of glacial loading. In contrast, our research (although related to the North Sea) showed that influence of ice sheet loading does not result in a significant tilting. I think it would be interesting to compare results and find differences. That is of course reflects difference in the gradients of ice thickness during LGM between the North Sea and SW of the Barents Sea. This discussion, however, needs to state the ice thickness data source a bit more precise.

Note of course, that my judgment would not be based on the decision of authors to bring this discussion into the study.

Medvedev, S., Hartz, E. H., Schmid, D. W., Zakariassen, E., and Varhaug, P., 2019, Influence of glaciations on North Sea petroleum systems: Geological Society, London, Special Publications, v. 494, p. SP494-2018-2183.

http://folk.uio.no/sergeim/public/North_Sea_2019.pdf

5. Line-by-line comments

15: “…caused by glacier loading and lateral movements of sediments. The driving factor of these movements is isostasy”. I suggest removing “and lateral movements of sediments”: (1) there is no r4esults presented about this in the study, and (2) it will remove confusion of the following statement, because the direct cause of lateral motion of sediments is not isostasy.

26: How strong the term “glacial erosion” is linked to the submitted study?

41-43 and 55-58: The same text is presented twice. Also the same references in the repeated statement are presented as new. I did not look for other repeated references; I hope authors can check for that.

109: I did not find thickness model in the reference 36. The referred article talks about maximum extent if ice during LGM. Word “thickness” is used only once in that paper and not to present some results.

110: Production licenses also need (correct) reference. Also useful is to mention that contours are 500 m apart.

126-127: Please, specify what is that? Where this statement came from? I think not only me, but most of the readers would not take this statement without any explanation.

128-129: Reference is needed here

138: What word “this” refers to? The last sentence of the previous paragraph presents several effects…

135: Would be nice to explain abbreviation for HCWC here as well.

156: The paragraph is filled with non-understandable terms. What is “the gradient of deformation”? “orientation of structure”? “point orientation”?

208: I understand that the curvature measurement is not very common parameter and the amplitude does not say much to common reader, but the color bar should accompany such maps. I assume, the curvature in this case should be of order mm per km per km.

240: Reference is needed here.

241-243: What is this statement? Is it results of calculations? Assumption? Intuition about linear dependence? That statement makes me think that the model presented here is 3d, so that boundary tractions are applied with linear variations with depth. While the previous sentence claim about “map view model”.

242: Geometry of the modelling domain is not explained. Nice to mentioned lateral size and (!) depth of the model. Boundary conditions are also nice to be explained. I assume free-slip at the top and bottom?

244: Validity of linear theory of elasticity is not about earth materials. Above 2% of strain, the non-linear effects of elasticity may be important. This theory has nothing to do with permanent damage in the crust and cannot be used as a limit here. In fact, authors do not use this limit.

265: (The following is debatable concern, more like my opinion). The color scale here is decided by the maximum stress, which occurs on the tips of the faults. I believe that position of faults has some uncertainties, and even much bigger uncertainties we can expect from the position and structure of fault tips. Thus, at the moment, the map represents mainly uncertain position of the fault tips. I suggest to reduce color scale down to 5-7 MPa, so that readers observe stress distribution between faults, and not uncertain position of the fault tips.

266: Need to present, what is “tensile” and what is “shear” stress. The result of stress modelling is stress tensor, the calculation of stress characteristics presented on the map does not have obvious form. And how this map view was build is not explained anywhere (note that authors mentioned that model has non-trivial depth distribution).

281: I do not see meaning of this paragraph. Also authors should remember that they presented two models (tilting and stresses) and reference to “the model” does not have obvious meaning.

294: Need a color bar

303: “the size of the added load” sounds really strange. Is it about amplitude of prescribed boundary stress?

304: “…contrast in stiffness, that is the relative difference” is questionable and not really understandable. Usually used, ratio of moduli represents better that contrast.

305: As I understand, the model uses prescribed boundary stresses. With this condition, increase of moduli would not change amplitude of resulting stresses much. So, the statement is wrong.

314-316: This statement cannot be in conclusions as it is not supported by anything in the text before.

321: “The flexural stresses are adding to background stresses in the area.” – I do not see any discussion on this topic in the text. And the approach presented in the study (arbitrarily chosen flexure-related stress amplitude and no estimations of background stress) does not allow to discuss this issue.

322: What is “vertical flexural stresses”? The same question to the later “horizontal”. These terms are confusing. The model does not really calculate the flexural stresses; it uses some arbitrary model to estimate distribution of membrane stresses with some link to flexure. Thus, I would suggest term “flexure-related stresses”. But I still confused on the parts of term related to orientation. Need more accurate use of terms.

 

Author Response

Please find our reply in the attachment.

Author Response File: Author Response.pdf

Reviewer 3 Report

Dear Authors,

The ms is well written and presents original work. Some small remarks I marked in the text file.

I recommend publication of your work

with my best wishes

 

Comments for author File: Comments.pdf

Author Response

Dear Reviewer,

thank you for your feedback on our paper. We have modified the text after your suggestions. Most of the suggested references are included.

Kind regards

Ingrid F. Løtveit

 

Reviewer 4 Report

Brief summary:

Based on modelling in the Barents Sea, the authors show that tilt and stress changes due to the loading and unloading of ice sheets may have been large enough to create increased fracture-related permeability and lead to potential migration of hydrocarbons out of the reservoirs. The authors stress that their results demonstrate that future basin modeling should consider including the effect of glaciations when dealing with petroleum potential in former glaciated areas.

General comments and suggestions:

The paper is well written and a pleasure to read. The subject is highly relevant, not only in relation to hydrocarbons exploration, but also in relation to general understanding of sedimentary basins during the Quaternary. The paper brings the effect of the repeated loading and unloading of the ice sheets in focus. The possible impacts on hydrocarbon pathways is important.

A general comment is that the paper describes modelling of the lithosphere, but very few details about the modelling itself is included. The paper is relatively short and contains few details. Therefore, the text appears more like a review paper or a textbook chapter than a paper conveying new specific model results. Many of the references used are around two decades old, which leaves the reader with an impression that the modelling in the paper is not new. Generally, I find the discussion of model results too short and I miss comparisons with previous – but recent - work in the area.

I suggest that the authors add more detail and more discussion (see also specific comments below). It would be good to mention the modelling more specifically in the abstract, and put more focus on describing the modelling in the text. The modelling would stand out more clearly if given a section of its own and highlighting the results.  

 

Specific comments:

Text:

Line 117: You mention that in the literature there is a disagreement on the effective elastic thickness of the lithosphere. You have chosen a thickness in the low range for your modelling. Can you add some text where you elaborate a bit on the disagreement and the consequences for choosing either a low value or a high value? Or maybe just refer to 4.2 and Figure 8?

Line 143-158: Concerning Figure 3: As a geologist outside the oil/gas industry, I would like to have a bit more explaining text here. The figure 3 is a bit sketchy.

Line 145: Delete one of the two ‘can be found’.

Line 154: ‘Trap’ instead of ‘tap’.

Line 226: The fault geometries you use are from 1992. You mention that newer fault interpretations may differ from the ones you have used. If present, why not use new data? Please explain your choice and describe what the consequences might have been if using newer data. You leave the reader wondering whether new data could lead to different results. In line 301-303 you mention it again and you say that ‘a more detailed fault map may give a slightly different stress pattern….’. Please reconsider the use of the word ‘slightly’. It attracts my attention, because it is not supported by any data or references. More discussion here is welcomed.

Line 239-240: Reference?

Line 272: Can you be more specific about ’the models’? Or do you mean ‘the results’?

Line 279: Discussion and conclusion: Please include a discussion of other modelling efforts in the region. Do the results point in the same direction?

 

Figures:

Figure 1: The production licenses on the Norwegian continental shelf are shown by grey polygons, but they are barely visible. Could they be shown in red or another vivid colour?

Figure 2: The figures are barely legible. Could the figures be enlarged? Please check: The reference /15/ is not correct.

Figure 3: Please explain annotations in the caption and add ‘a-c’ on the figures to correspond with text.

Figure 6: Please indicate map scale. Please mark the model area more clearly.

Figure 7: Please add map scale.

Figure 8: Please add legend.

Author Response

Dear Reviewer

We would like to thank you for a thorough review and valuable feedback. Your constructive comments have to a great extent contributed in improving the manuscript.

Please find our reply attached.

Kind regards,

Ingrid F. Løtveit

Author Response File: Author Response.docx

Round 2

Reviewer 1 Report

The paper “Tilting and Flexural Stresses in Basins due to Glaciations—an Example from the Barents Sea” by Løtveit et al. presents the results of a stress and tilt modelling for the Barents Sea. The paper has been greatly improved, but several things still remain unclear and are too simple.

The main problem comes with the stress modelling. The authors ignore the effect of vertical stresses due to the ice load and/or ocean load as well as stress migration, and the obtained stresses are therefore no glacial stresses. This should be made clear in the abstract as well as introduction otherwise the reader is misinformed about the scope of the study. I would suggest adding the following sentence to the abstract in line 13 “… unloading, and flexural stresses. However, we neglect other important components of glacially-induced stresses. The driving factor …”. You are dealing with isostatic stresses that could also be created due to volcanic loading and these have nothing to do with glacially-induced stresses as important components are not included here.

Secondly, the figures have been improved a bit, but are still not of high enough quality for a scientific paper. The reader has to search for longitude and latitude values as well as color bars. Why is it not possible to add longitude and latitude values at the map boundaries as well as putting the colorbar outside the map? This would increase visibility. This would also allow the authors to add the unit to the colorbar directly instead of writing it in the caption where the reader then has to search for it. Fig. 7 should be mainly improved to include map information (latitude, longitude). A change of the colormap is of advantage here as well.

In addition, I have several minor comments:

Title: Maybe it is better to write “isostasy” instead of “Glaciations” as this would fit better with the stress modelling. Line 14: Please add “the area of” between “inside” and “the former”. Line 17/18: Please replace “the unloading after LGM deglaciation” to “isostatic processes”. Line 21: Please replace “glaciations” with “isostasy”. Line 41: Please replace “lead to flexural stresses [6]” with “during a glacial cycle lead to stresses, e.g., flexural stresses, vertical stresses, stresses due to stress migration [Steffen et al., 2015, Tectonics]”. Line 52: Faults have been found in northern Europe and not only in northern Scandinavia. Line 52/53: Second part of sentence does not make sense. Please rephrase. Line 55: Add the specific reference to the countries as done for the areas before. It would be also good to include the first works on German glacially-triggered faults by Brandes et al. Line 55: Please replace “Such” with “Therefore, such”. Line 59: Delete the first “the”. Line 62: There are three main effects for glacially-induced stresses. You neglected the stress migration. Refs. 28 and 29 are also not suitable here. It would be better to refer to works by Wu, Lund, Steffen, and many others. Line 75: The models by Steffen et al. are also applicable to areas that are in the peripheral bulge and are therefore not only for areas once covered by continental ice sheets. Despite, the size of the ice sheet does not matter in their studies and the method is applicable to all type of ice loads. Even though this is not within the scope of your study, you should write it correctly when referring to other articles. In addition, it would be worth mentioning that the effect of stress migration was included there. Line 84: Please add “flexural” before “stress effects”. Line 85: Please add “and neglects stresses due to stress migration and vertical loading”. Line 94: Which period are you referring to here? 24,000 to 18,000 BP? Line 118: It would be better to write “thickness of the elastic lithosphere (used in GIA modelling)”. Also, in the following lines, please write “thickness of the elastic lithosphere” to differentiate this from other estimates in geophysics. Line 123/125: Please reformulate this as you use “significant” twice. Line 129: Please add “the” in front of “SW Barents Sea”. Line 131/132: Please provide a reference for “rise again to isostatic equilibrium in interglacial periods” and if possible one without a contribution by one of the authors. Line 149: Which two extreme positions? Line 152: Delete “will”. Line 173: Do you want to estimate the stress regime? I have not seen any results on this here? Lines 184-190: How do stresses of the surrounding loading affect your area (e.g., Svalbard, northern Norwegian coast), which were and are still not completely ice free? Isostasy is a regional to global scale process and not a local scale process. Could you please provide other references for a relaxation time of 4000 years except articles written by the authors itself? Lines 205-209: Is your calculation for one time point only or a change in time? Lines 241-252: It is still not clear how the results from before are applied? Do you apply f’’ as boundary condition? In addition, what is with the compressional stress field that exists at LGM due to the flexure even though that the area is in equilibrium as you assume it here. The stresses would still be existent due to the loading from before. Line 252: Please delete “glacially induced flexure” as this gives the impression that you are modelling glacially-induced stresses. Line 287: The second part of the sentence needs to be re-written. Line 310: No effective elastic thickness here. Line 331: I know what depocenters are, but not deposenters. Maybe this is Norwegian for depocenters. General question: Are your stresses time dependent? General question: As far as I know is the Barents Sea covered by oceanic water now (comment to your response 6.2). Even though that the study area was within the ice margin, the area was flooded by water as soon as the ice melted. This also induces flexural stresses as well as vertical stresses. Have these stresses been considered here? Apparently not, but they might be quite important as the assumption of having only extensional stresses is then not valid anymore. General question: I’m still puzzled about the modelling in general. Are you obtaining time-dependent rates or are the results for a specific time point?

Author Response

Please see attachment.

Author Response File: Author Response.docx

Reviewer 2 Report

Sergei Medvedev (University of Oslo, Centre for Earth Evolution and Dynamics)

Second review of ms “Tilting and Flexural Stresses in Basins due to Glaciations—an Example from the Barents Sea” by Ingrid Løtveit, Willy Fjeldskaar, and Magnhild Sydnes submitted to Geosciences.

 

I first want to argue for some points presented in the review by the reviewer #1:

I totally disagree with misconception of EET presented in that review. By referring to published papers, the reviewer1 presents EET as a final product of the research. It is the same as to claim that viscosity of the rocks is what people are measured in labs. No, like viscosities are estimated to be used in the numerical modelling, the EET estimations are to be used in simple models representing the lithosphere as an elastic plate with effective properties. It is exactly what authors are doing in their study. The use of “mechanical thickness of the lithosphere” in the Appendix now just presents an additional confusion. The discussion of isostasy is also not very relevant as the remaining disequilibrium is definitely within the accuracy of the model, and the model does not pretend to estimate exact values, but to estimate order of the effects. Thus, it is ok to me as well to ignore the list of time-varying effects mentioned by the reviewer1. Assuming isostasy (within accuracy of the model), the authors ignore viscous properties of the mantle, the usual part of GIA models. The model estimates the amplitude of isostatic motions (not evolution), which depends of viscos properties of the lithosphere/mantle only in a limitted manner. Thus their model is a simple elastic plate within inviscid dense substratum subjected to field of gravity. And that is clearly should be described by EET. The value of EET is always a question, of course. In our paper (Medvedev et al., 2018) we compare effect of erosion with gravity anomalies in the Arctic and got better fit with EET 30-40 km. In the other paper (Medvedev and Hartz, 2015) we compared different models including variable EET. Important conclusion from the latter paper may be expressed with the application to the Barents Sea, as for example the results in the area of Bjorn Island do not depend on the EET values for the northern Norway, but depend mainly on the EET values within a single wavelength (200-300 km). Use EET=70 km for the study of hyperextended lithosphere of the Barents Sea is maybe not very appropriate. And thus, EET=30 km is an acceptable value in the case of particular interest within the Barents Sea.

I understand that authors have answered these critical comments already in their reply, but I am not sure that all the comments should result in changes in the manuscript. Below some comments on my previously major concerns and line-by-line comments:

1. The models should be explain better

Done more or less. I assume the stress model description can be clarified a bit with presenting the choice of the elastic model “plane strain” or “plane stress”.

But now I see (eq. in Appendix) that the tilting model does not include effect of amplification of vertical movements under water. It is unfortunate as the underwater isostatic response is ca. 30% stronger.

2. For the study presented numerical model there too few numerical estimations

Somewhat ok. I wanted to compare with our model (see 4 below) using your estimates, but suggest you to use my calculations from a minute ago. Our estimates for the North Sea give 0.5-0.7 m/km tilting as max. Then it would be a bit clearer to say that the effect is larger in the SW Barents Sea. Then this comparison would be appropriate in the results section.

3. Section “Conclusions” does not present results of study

Ok

4. Very optional: comparison with study of the reviewer

Two factors control limited tilting in the North Sea: smaller ice thickness (in some models it is really minor) and smaller gradients of ice thickness. See also 2 above.

5. Line-by-line comments

 

126: Still not understandable. I may assume that tilts somewhere in Himalaya maybe even larger. Do you mean “in the map” not “of the Earth’s surface”?

160: I still consider that any “point orientation” is confusing. Authors can put reference to their published definition of this term here.

257: I think word “limited” would be better here than “determined”.

299: I would state “is not intended” rather than “incapable”.

335-337 and 339-341: These two parts of the text look very similar.

351: Should it be h_k instead of h₀?

354: Mechanical thickness of the lithosphere needs definition. Authors are now in the strange situation to either use conventional EET, or introduce this new term.

355-358: Introduce D in a similar way as H here and remove words “Flexural rigidity” from line 357.

367: I am not anonymous

 

Medvedev, S., and Hartz, E. H., 2015, Evolution of topography of post-Devonian Scandinavia: Effects and rates of erosion: Geomorphology, v. 231, p. 229-245.

Medvedev, S., Hartz, E. H., and Faleide, J. I., 2018, Erosion-driven vertical motions of the circum Arctic: Comparative analysis of modern topography: Journal of Geodynamics, v. 119, p. 62-81.

 

Author Response

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Author Response File: Author Response.docx

Round 3

Reviewer 1 Report

I think that there is misunderstanding. The authors are not modelling flexural stresses due to glaciations but flexural stresses due to long-term loading in general. Naming them “flexural stresses due to glaciation” does not make it right. The stresses would be the same as due to a volcanic island (e.g., Hawaii islands) or other types of long-term loading scenarios. Stresses due to glaciation are, however, three-folded (not two-folded as the authors are trying to say) and it seems that the authors also have missed to read the publication by Steffen et al. (2015, doi: 10.1002/2015TC003992). I would encourage the authors to read the paper. Three types of stresses are induced by glacial loads: 1) vertical stress, 2) horizontal stress due to the flexure, and 3) horizontal stresses due to stress migration, which is depending on loading time and mantle viscosity. It is not possible to separate these stresses as they depend on each other. So, the statement made in lines 63/64 is completely wrong.

The authors also claim that they write in their Introduction that “The stress effects of vertical ice load and related stress migration are not calculated here.” They should also add then: “However, these stresses are not negligible when estimating stresses during a glacial cycle.” In addition, the authors constantly state that they are dealing with flexural stresses and that’s why they ignore stress migration. However, it cannot be ignored when dealing with stresses due to glaciations. The response by the authors to my comment 11) from the second review is also completely wrong as stress migration is an effect of glaciation. The authors also point out eventually that the Barents Sea is covered by ocean water and this is a vertical load. Of course, this load influences the stresses again. That’s why, vertical stresses, stress migration and flexural stresses must be used together when analyzing the potential of stress effects during a glacial cycle.

The authors state in their response that “effects of glaciations are not commonly included in basin modelling software”, which I think is unfortunate but does not allow the authors to publish results, which are then based on wrong implementations. This could be a possible way to improve the basin modelling software and incorporate all stress effects.

If figure 7 is not a map, then please add x and y axis. Also please avoid using “jet” as colormap.

Author Response

Please find comments attached

Author Response File: Author Response.docx