Dear Mr. Zhang,

Based on the concerns of the first set of reviews, I sent your manuscript for re-review. I now have two new review reports: one that recommends "rejection" and another that recommends "major revision". Their concerns centre around three issues: (1) missing references to key works, (2) insufficient discussion of the data and, importantly, (3) the absence of significant novelty. Because I think that these concerns can be remedied, I'd like to give you the opportunity to further improve your manuscript and resubmit to Solid Earth. I have therefore selected "major revisions". However, please be aware that I consider that addressing these comments will require large changes to the manuscript, rather than the addition of a few new sentences. If you are willing, please now prepare and upload a detailed point-by-point rebuttal letter and a revised manuscript.

Thanks,

Mike Heap (Topical Editor of Solid Earth)

Report #1
The paper presents experimental data of different nature including NMR and SIP in order to characterize the pore size distribution of sandstones. In my opinion, there is nothing fundamentally new with respect to the work done by Niu Q. and Zhang C. 2017. Joint inversion of NMR and SIP data to estimate pore size distribution of geomaterials. Geophysical Journal International. The second biggest problem I see in this paper is the use of the Debye deocmpostion which is fundamentally in error with respect to the basic physics of the problem. If my understanding is correct, it was shown that such a kernel inplies that if all the pore have the same size, the spectra are described by a Debye model. No metallic-free rocks is described by a Debyt. At best (very uniform materials), the transfer function is a Warburg (a Cole-Cole with an exponent c = ½ to be compared with a Debye for which c = 1). Using a Debye decomposition is therefore a huge mistake in recovering the pore size distribution. Why this has been described in many papers in the last few years since Florsch N., et al, Inversion of generalized relaxation time distributions with optimized damping parameter, Journal of Applied Geophysics, 109, 119–132, 2014., it seems that the authors are not aware of these works. I think they should spend more time in reviewing precisely the literature on the subject and redo the analysis with a Warburg decomposition instead of a Debye decomposition. Other issues include a very poor review of the existing literature on these techniques in the introduction. I also disagree with this statement “Rouquerol et al. (1994) reported that no experimental method provides the absolute value of parameters such as porosity, pore size, surface area”. I am also surprised that the earlier works by Slater and Lesmes are not cited. No discussion is given for the small pore sizes that are hidden by the Maxwell Wagner relaxation.

Report #2
Though I appreciate the efforts made by the authors to respond to my earlier comments, I still feel that this contribution is lacking essential material to support the results that are reported. The assimilation of the MIP data to a pore throat size distribution on one hand and of the NMR data to a pore body size distribution is not substantiated. The authors do not offer a single image of a pore space representing what they think the techniques are measuring. There is more than one way to generate distributions such as the ones showed for the pore body radius, and the very large contrast that is observed with the MIP results should warrant further investigation, starting with reviewing graphically how pore bodies are segmented and tagged. Then one would have to explain what these individual pores might have to do with the NMR signal. As already mentioned in the previous review, I also think that the data set could be made more complete by adding an MIP simulation based on the images as well as a distribution of the maximum inscribed sphere radii in the pore space prior to pore separation.

Dear Mr. Zhang and co-authors,

Firstly, the reviewers I invited to re-review your manuscript are prominent experts in the field. It is my understanding that they did not think that your paper warranted publication in it’s current form (i.e. following the first review), rather than that they didn’t “fully acknowledge” your changes following the first round of reviews. I also disagree that their comments are “not quite helpful”. Before I reconsider the manuscript for publication in Solid Earth, the authors should consider the following points.

Although reviewer #1 disagrees with the use of the Debye model, I appreciate that the authors now include a more detailed reasoning. However, I would like the authors to include more information that outlines why Revil et al. (2014) consider that, to quote their paper: “…the Warburg function, rather than the Debye function, is the correct transfer function to determine the pore size or the pore size distribution”. Revil et al. (2014) provide a lengthy discussion on this topic. Since the authors disagree with the reasoning of Revil et al. (2014), I would like them, in a few sentences or short paragraph, to explain why they disagree and why they have decided to use the Debye model.

There are still several instances where the authors mention that MIP yields the pore radii, rather than the pore throat radii. For example, on line 373: “The MIP yields the widest range of pore radii.” Due to the subject matter of the paper, I think it’s important to be precise here and elsewhere in the manuscript.

I think that the authors should offer more information on their method of permeability. Gas permeability measurements on porous sandstones typically require a Forchheimer correction. Did you correct for turbulent flow? Under what confining pressure were the measurements performed?

Regarding the comment of reviewer #1 about the "very poor review of the existing literature", the 2005 paper of Louis et al., for example, discusses the microstructure of Bentheim and Rothbach sandstone. Perhaps the authors can compare their results with those in this paper?

Louis, L., David, C., Metz, V., Robion, P., Menendez, B., & Kissel, C. (2005). Microstructural control on the anisotropy of elastic and transport properties in undeformed sandstones. International Journal of Rock Mechanics and Mining Sciences, 42(7-8), 911-923.

There’s a typo on line 87: “intention”.

Mike Heap (Topical Editor of Solid Earth)

Dear Zeyu Zhang,

Thanks for implementing my requested changes. I'm pleased to inform you that I have recommended that your manuscript is now accepted. There are however two more technical changes that I'd like you to address. First, on line 259, I think you mean "pressure differentials", rather than "pressure drops". Since you're using the steady-state method, I think it's perhaps confusing to use the phrase "pressure drop". Second, although your flow rates were small, I still think that one can't definitively rule out the Forchheimer effect without checking. Can you change the sentence on lines 261-262 to say that "due to the low flow rates, you consider that the Forchheimer effect can be neglected", or something similar?

Thanks for submitting your work to Solid Earth; we hope you consider us again for your future manuscripts.

Mike Heap (Topical Editor of Solid Earth)

Dear Authors, based on the TE's reccomendation and overall assessment of the review process, I am pleased to accept your manuscript for publication in Solid Earth, pending the corrections proposed by the TE (Dr. Heap).

sincerely,
federico rossetti