My comments refer to 'Track change_comment.pdf' found in the online material. Unlike the referees, I found the analysis to be lacking in a number of regards that require clarification and reanalysis. The title is over-generalized; this result is only for desert systems and really only with two respiration chambers. Whereas this is an important measurement flaw that needs to be addressed, I'm not of the opinion that it itself makes the manuscript unpublishable given that eddy covariance observations (likewise a n of 1) are so frequently used to measure ecosystem carbon flux. I don't doubt the basic findings, but the lack of any mechanistic treatment of transport of photosynthate and carbon dioxide within the phloem and soil (respectively) weaken the arguments and compromise their generality.

The text throughout needs to be more efficient. One example is " biologically photosynthesis-related processes". This could also be written "photosynthesis". Every sentence in the manuscript could be made simpler and more effective.

On page 1 line 10, I do not feel that diel hysteresis between respiration and temperature is controversial, rather that both biological and physical mechanisms can explain it (see for example Stoy et al. 2007, http://onlinelibrary.wiley.com/doi/10.1111/j.1365-3040.2007.01655.x/full, and note also Detto et al. for a very nice time series treatment of this challenge http://www.journals.uchicago.edu/doi/abs/10.1086/664628).

The abstract describes the findings succinctly, but the notion that autotrophic respiration is responsible for the changes is merely a hypothesis. Note that this is an important area of future research rather than stating 'it is indicated', which lends false confidence to the findings.

All of the statements that follow "e.g" in the second paragraph of the introduction can easily be argued against and should be clarified or quantified. Note Reichstein et al. 2003 (doi: 10.1029/2003GB002035) regarding statement on line 9 of page 2.

The statement "Some studies have reported that high SWC tends to block CO2" should be strengthened by noting the basic equations for transport in porous media (e.g. Millington and Quirk) demonstrate very convincingly that it does on theoretical grounds, not merely via empirical findings.

The statement "few previous studies address soil respiration dynamics in drylands" is not correct. Many have.

The statements on page 3 lines 7-9 likely would not hold in a system with biological crusts that may hinder gas transport.

"The soil at the research station was of a sandy type" is an insufficient description of the soil in this case in which soil properties are critical for understanding results.

How was the stabilization period determined?

The text surrounding equations 1-3 is confusing; please rewrite for clarity. The description for equation 3 is inaccurate as it refers to the instantaneous importance of different variables for respiration rather than their actual effect, which may be lagged.

The following statement wasn't substantiated is qualitative, it needs to be rewritten: "However, sandy soils with high soil porosity, as on our site, have a minor influence on within-soil gas transport processes." Using an actual physical model of these processes and differences among soil types and moisture contents would improve the manuscript dramatically; at the moment the arguments are empirical and quite frankly often times rather weak.

There are multiple alternative hypotheses to the statement on page 7 line 14, that the dominant respiratory source changes with depth and/or that respiration is suppressed at high temperatures in desert ecosystems (see for example http://link.springer.com/article/10.1007/s10533-010-9448-z).

Very surprised that section 4.2 excludes a discussion of the Birch effect (e.g. Jarvis et al. 2001, http://www.geosciences.ed.ac.uk/homes/lwingate/publications/Jarvis_Birch.pdf).

The statment "Most organic matter and microbes tend to concentrate in the upper part of the soil, whereas plant roots are found much deeper" isn't necessarily true.

As noted also by the referees, the statements regarding heterotrophic versus autotrophic respiration are merely speculative.

The statement "Our work provides urgently needed new knowledge concerning causes/mechanisms" isn't accurate. A mechanistic study of the processes controlling soil respiration were not undertaken; the analysis is entirely empirical. The following statement that a soil moisture threshold of 0.08 is of particular importance is not likely to hold in different desert systems with different soil properties and vegetation.

As a whole, substantial improvements must be made before this manuscript can be reconsidered for publication. Arguments must be strengthened throughout, mechanistic understanding must be incorporated into empirical findings, and the discussion section should not merely be a modified version of the introduction that briefly incorporates the present findings into the existing literature and overextrapolates the findings of the present study across desert ecosystems.

I thank the authors for their careful responses. The edited manuscript was difficult to read in places due to the pdf markup used (I couldn’t figure out how some changes were being resolved nor read added text). A draft in which additions to the text can be identified would be appreciated.

My concern with the manuscript is that I still don’t agree with equation 2 given the necessary lag between photosynthesis and respiration, which is likely to increase under drought stress depending on the response of phloem velocity to changes in xylem velocity. These terms will change as a function of drought stress. There is also of course the argument root-to-soil carbon flux occurs shortly after photosynthetic inputs to the plant due to osmoregulatory constraints, but it is unclear how large this effect is. Work by Mencuccini and others may add insight into time lags of transport between photosynthesis and respiration; the response in the letter regarding these dynamics was too terse. In brief, I feel that this manuscript is confirmatory and makes some interesting points regarding seasonal changes in photosynthesis/respiration coupling. At the same time, it is far less rigorous than many manuscripts that address similar issues, hence my concern that it is not sufficiently advancing the science. In summary, I would appreciate it if the authors could send a draft in which changes to the manuscript were more clear, and cite more relevant literature on photosynthesis/respiration coupling, which they might have but again these additions from the pdf that was uploaded is unclear.

A couple of minor notes:
Regarding the statement ‘rather than rely on relating daytime simulations of Rs to night-time respiration-temperature relationship’, note that many partitioning approaches don’t, but I agree that it is the normal course of affairs.

‘No consensus has been reached’ implies that there is a single cause of hysteresis. But there are many, and different ecosystems should behave somewhat differently with respect to this hysteresis.

The manuscript represents an improvement, but the authors still seem to be affixed to the idea that there is a discrepancy in the literature regarding physical vs. biological controls over soil respiration and erroneously describe manuscripts in the literature as 'contradictory' when no contradiction exists. Physical and biological controls are both important, and their degree of control will differ in different ecosystems. By reframing the manuscript to actually describe the findings of the manuscripts that the authors incorrectly identify as 'contradictory' (see for example page 9 line 5. Eight citations without describing a single one!!!), the authors will be able to contribute to the literature rather than create an artificial debate where little debate exists. There is still an alarming lack of mechanistic reasoning for key passages in the manuscript as described in more detail below. Please note the approach and conclusions of Detto et al. (doi: 10.1086/664628) as it applies to photosynthesis/respiration coupling as you see fit.

In the title write 'desert shrubland'.

I basically disagree with line 12. The implications of Stoy et al. (2007) and other manuscripts is that physical and biological mechanisms cannot be fully separated from photosynthesis / soil respiration measurements because the time scales of biological and physical transport processes are concomitant (see also page 3 line 12). That being said, I agree that there is a substantial role for biology in determining hysteresis. In other words, when you write "Currently, it is not clear whether physical or biological processes (or their combination) dominate the control of diel hysteresis in drylands" it is in fact clear. Both do. The relative degree of control of each is what is of more interest. By framing the manuscript with respect to the degree of control of physical and biological processes, rather than trying to find out which is the control when both are important, would lead to a much less questionable argument to motivate the analysis.

On page 2 line 16 (from here on out please always only use continuous line numbering when preparing manuscripts) one might argue that substrate in addition to temperature are equally important for determining soil respiration.

There is no information to support the following statement: "At our study sites, it is likely that Rs-effluxes at the surface originated from biogeochemical processes in the deep soil." There is also no reason to frame the references in the previous sentence (p9 L5) to be 'contradictory'. The authors still seem like they are trying to solve some challenge in science with respect to physical vs. biological controls over soil respiration. Because both are important, this isn't a particularly useful way of thinking about the processes at hand.

On page 9 line 20, please describe how these processes could occur on the order of minutes in sandy soils.

Please cite Jorge's name as "Curiel Yuste" correctly on page 11 line 20.

Thank you for reframing the arguements in the manuscript, it mow provides a better contribution to the body of literature on photosynthesis/soil respiration coupling.

Sincerely,
Paul C. Stoy