The revised paper shows a significant improvement in terms of clarity and justification of the main statements. I find that most of the technical comments raised by the reviewers were addressed in this revision. At the same time, there remain several conceptual issues that are being debated by the author. Resolving these issues (mainly, by revising the current text and conclusions) would make the paper acceptable to publication in NPG.

One of the main concerns is that the SSP, the main methodological tool of the work, has not been shown to be a physically justified principle that drives the observed seismicity. Specifically, the SSP seems to be a practical toy model that can be appropriately ramified (e.g., by adding noise, like in Fig. 4) to look consistent with the data. This might be not surprising though: the activity (suitably defined) of aftershocks generally decays away from a mainshock, so a model formulated in terms of decay (continuous or step-like) could be made consistent with data. This observation alone is insufficient to prove the validity of SSP. Nevertheless, the paper claims that the SSP has been validated (l. 16) and the SSP is a “proper approach” (l. 367) that can explain “most empirical laws observed in seismicity” (l. 356). These claims are unsupported by the analysis presented in the work; I think such claims can distract a reader and harm a potential impact of the work. A possible resolution would be to explicitly introduce SSP as an assumption and illustrate how it can be used to make inference regarding the productivity law. Such analysis might be interesting from various points of view and can stimulate further research. The work nicely illustrates how a basic assumption can be transformed into testable statements regarding the main laws of seismicity; however an attempt to claim that such an assumption is an actual law of seismicity might be premature.

I consider the suggested revisions as minor. However, if the author insists on physical validity of the SSP as a new paradigm in understanding seismicity, a substantial further research and justification will be required.

I list other comments below:

It is worth adding a brief summary and discussion of the findings by Hainzl et al. (2010). Their results seem important for understanding the motivation and some of the results of this work.

l. 11: parameter K needs a better definition, e.g. “K is the number of aftershocks triggered by a given mainshock of magnitude M “
l. 14: “Solid Seismicity Postulate” (please insert Postulate)
ll. 25-28: Please rewrite the sentence, possibly splitting it into two: one regarding the estimations and the other on the necessity to prove the existence of the kink.
l. 31: explain “most robust”
ll. 32-33: explain what empirical laws are mentioned here
l. 45, Eq(2): Define N and A
ll. 65: “Solid Seismicity Postulate” (add Postulate)
l. 71: Revise the subsection title (sounds vague at the moment)
l. 72: “a geometrical theory of seismicity” does not seem justified. Is it possible to merely formulate the postulate, without calling it a “theory”?
l. 75: “strictly categorized” needs to be explained
l. 79, Eq. (5): Please define sigma and delta (explanation + units), and “background stress amplitude range”.
l. 92: Please define r and explain the equation.
l. 113, Eq. (7): the comma must appear after the Eq. in line 113, not in line 114.
l. 120: “rupture surface area” (add area)
l. 163: Please explain “step-like spatial behavior”. Does this refer to the spatial density of aftershocks?
l. 173: “discredited” in this context sounds as too strong of a term. Can you revise?
l. 244: Why “Poisson process”?
l. 351: Please justify “physical”. Eq. (12) is a consequence of an ad-hoc SS postulate; its connection to physical principles has not been established.
l. 355-357: I do not find this conclusion justified by the presented analysis (see above).
ll. 365-367: The ability to reproduce the scaling parameter q should be critically assessed against the number of assumptions and parameters involved in this estimation.

Throughout the paper:
Please avoid using consecutive parentheses, like in “(Kanamori and Anderson, 1975) (Fig. 1d).”
Please check punctuation marks (commas, periods) in equations.

I would like to thank the author for the next round of revisions, which further improved the readability of the paper. The revised version reveals a methodological issue that needs to be clarified.

It is stated in ll. 71-72 (marked version of the paper) that “The aim of the present article is to explain the Utsu aftershock productivity equation”. At the moment is it not clear, however, how the derivations of Section 2.1 can explain the Utsu law and why the SSP is important here. Specifically, my understanding is that Eq. (12) is the final suggested explanation for the Utsu law. Furthermore, only a part of this equation — I mean S(M) in some power — is used to explain the Utsu law. I list here the assumptions used to derive Eq. (12): (i) rupture surface area S(M) scales with event magnitude, (ii) there exist a connected region around the mainshock rupture that accommodates the aftershocks (aftershock solid), and (iii) large EQs rupture the seismogenic layer, while small ones develop in a volume. The key equations that gives the sought result are: r(M) ~ S(M)^alpha (alpha=1/2 or 0 depending on the mainshock size) and V(M) ~ r(M)S(M).

If my understanding is correct, the role of the SSP remains unclear. One can make multiple alternative assumptions regarding the intensity of events, and arrive at a similar scaling, which follows from straightforward geometric considerations and scaling of the surface area with magnitude. In other words, the presented derivations show that the SPP does not contradict the Utsu law, and can suggest a particular parameterization for the law’s constants. This is different from “explaining” the law. Accordingly, it is important to justify the necessity of SPP in the presented derivations and separate the routine calculation of parameters (constants) from the derivation of the main scaling part of the equation.

The above issue can be readily addressed by removing the claims that SPP explains the Utsu law, and presenting SPP as a particular parameterization for this and other empirical regularities.

Thank you. The revised version satisfactorily addresses my earlier comments and is accepted for publication in NPG.

I ask to make one minor edit (no further review is required): in l. 46, please indicate that N is the _average_ number of events (otherwise, the claim is not true).

I would like to thank you for choosing NPG as a venue for you work.

Sincerely,
Ilya Zaliapin