|I have read the revised version of the manuscript entitled “The competition between fracture nucleation, propagation, and coalescence in dry and water-saturated crystalline continental upper crust” by McBeck, Zhu, and Renard, and their responses to the reviewer comments. The authors have made substantial improvements based on the comments provided by reviewers and editor, which have improved the readability and clarity of the manuscript, particularly the aim and the conclusion. However, I have comments on some of the author’s responses, primarily on the discussion section which remains overly cumbersome and distracting due to many tangents and unnecessarily cited literature. I have detailed my comments below. |
Comments 7 & 8, Section 4.1, and majority of section 4.2: On the excursions to literature on other lithologies and larger scale systems:
I understand the reply from the authors to some degree, but I continue to feel that a disproportionate part of the discussion is devoted to this generalisation and is distracting to the story. I support the idea of the authors on: “Our general view is that rock deformation analyses benefit from reasonable generalization between different rock types”, but the data presented in this study simply cannot help to achieve such a reasonable generalization without doing (or finding in literature) similar types of analysis on different rock types. Without this, the discussion will remain qualitative and “hand-wavy” and does not contribute to informing the reader on the main aims and conclusions of the paper. This may result in an enumerating literature study rather than a focussed scientific manuscript. I suggest to keep these discussions short and concise rather than write lengthy paragraphs, and use analogous sparingly.
First, for section 4.1, the last paragraph should be placed after the 1st sentence of section 4.1; it adequately explains why isolated propagation is favourable to nucleation of smaller flaws. I understand from lines 258-276 that the authors attempt to discuss the initial flaw distributions in other rock types, and how that may influence the outcome measured on monzonites? This discussion does not provide an informative conclusion (line 268), and may at most provide a hypothesis for future experiments (line 275). I could not be convinced on how the discussion on the amount of stress concentrators in sandstones is germane to the main outcome of this section that isolated propagation of larger fractures is favourable to nucleation of smaller ones in crystalline rock.
The next paragraph continues the discussion with sedimentary volumes (with different lithologies, different scales, and different boundary conditions relative to the experiment) as an analogue to the experiment. I do not see clearly how this serves the main explanation of why isolated propagation is favourable to nucleation of smaller flaws; as the authors state, this is well explained by LEFM and examples from the LEFM literature may serve as better analogues/examples (e.g., Weibull theory).
For section 4.2:
Line 306-316: Here, the authors describe the fairly well established evolution of macroscopic failure evolving from tensile to shear with increasing confining pressure. Why is it important to understand this, and the relative proportion of shear and tensile deformation, in light of the results that were obtained before macroscopic failure?
Line 320: Why does a tensile fracture enable greater access to preexisting fractures than a shear fracture? Line 322: Why do mixed-mode fractures have a larger surface area than shear fractures? Is their roughness larger? How does that relate to the aperture?
Line 323: I am not convinced that fault damage zones need to be mentioned here: A fault zone is a shear fracture that may be compared to the macroscopic shear fracture developed at failure in triaxial experiments. The analysed fractures in this study are all tensile, near-zero offset microfractures, so do not directly compare with a shear fault. At failure, the macroscopic shear rupture and subsequent slip will create additional microfractures surrounding the shear fault by dynamic transient stresses and slip over a rough interface, but these microfractures damage zone (or meso-fracture damage zone in the field) have few to do with the pre-failure microfractures studied here.
Line 345: Saturated gouges: These are shear systems, opposed to mode-I opening of microfractures. Gouge-filled fault systems with dilation may be described not by fracture mechanics, but by frictional processes.
Comment 4: What was the axial loading rate, how was axial shortening measured? Loading rate is an important parameter, as it may influence strength and whether the system will be (partially) undrained during a load step.
Comment 9: The comment on the representative elementary volume has been addressed by the authors, but I would recommend to remove the general remarks on the existence of an REV for softening materials and the upper limit of a REV for glass beads – both are not applicable to the rheology tested here. Without these remarks, the authors already show that they have considered this problem, and support the reproducibility by previous work.
On some linguistics:
The authors aim to track which mode of fracture network development is dominant as a function of axial load, presenting it as a “competition”. I am not convinced this should be presented as a competition, as one mode of fracture network development naturally leads to the next: If all fractures continue propagating in isolation, at some point the fracture population will have grown to fracture lengths where it is not possible anymore to stay within isolation, and all fractures are near to each other. This eliminates the mode of propagation-in-isolation. Similarly, when sufficient fractures have reached a substantial length, nucleation of smaller fractures becomes unfavorable as the longer fractures “shadow” them (this is all explained in the manuscript as well). Thus, in my view, rather than a competition between modes, it is an unavoidable sequence of modes as a function of load that have some intervals of differential stress in which both modes may contribute to fracture network evolution before one of the modes is eliminated by evolving geometrical properties (fracture length, fracture spacing). This sequence seems, pardon the pun, set in stone, so that the “winner” of the “competition” is known, so is it not a sequence rather than a competition, with the main aim of quantifying in terms of load the transition from one mode to the other?
Line 24: shortly before failure close to the peak stress
Line 9: Specify what behavior. Also, state in the first sentence that the paper looks at fracture development in crystalline rock.
Line 37: The word “struggle” implies to a reader that LEFM tries to describe interaction between fractures, but fails at it. Since LEFM does not attempt to describe this at all, I suggest to replace it by “does not”.
Line 38-39: The transition from dispersed to localized networks: This is not very clear, and may need some additional explanation. First, what is the driving force for evolving a network of fractures (e.g., continuous deformation, thermal cracking, etc), and which one will this study target? Second, how can a distributed disperse network become a localized network of connected larger fractures? What happens to the smaller fractures from the dispersed state that did not develop in larger fractures, are they healed or do we zoom out to the scale of larger fractures only for the localized network, ignoring the smaller fractures?
Line 85: Methods –> method
Line 193: stage VI stage IV
Line 231-234: This part of the data analysis should be mentioned in section 2 (method section).
Line 245: Be aware of the positive feedback through fracture length, which essentially does not allow for “far” fracture couples to exist anymore!