The authors have improved the readability of the manuscript by reorganizing the text, adding helpful subtitles, and moving portions of the text to a supplement. Please address the following comments prior to publication.

1. I appreciate the new text on HONO emissions. However, I agree with Referee 1 that some attempt to quantitatively bound the uncertainty surrounding HONO is necessary and still absent. Use of the HONO-NO emission relationships is apropos considering comparable soil types were studied. But the new text states that conditions were optimum for HONO to NO emission. Does this mean your estimates represent an upper bound to the HONO source? At a minimum provide a statement to whether your HONO estimates are an upper or lower bound. I imagine Oswald et al., provided uncertainty estimates to their emission factors and some way to think qualitatively about whether the HONO:NO emission factor they observed would change with season. Substitute this kind of bounding for your statement, “this may result in a certain error of the calculated HONO emissions, which unfortunately can not be quantified more precisely at the moment.”

Secondly, I do not quite agree with the implication in (page 27, line 24–26): “nevertheless, the qualitative and, in particular, the quantitative agreement between bottom-up and top-down estimates indicates that our assumptions are largely justified.” Instead, you might say the agreement between bottom-up and top-down estimates provides support for broader applicability of the lab derived HONO-NO emission relationships in space and time.

2. Although the new text attempts to clarify use of the term NO2 emission, it is still hindering the readability of the text. This is in part because nothing appears to be gained from employing this unusual convention. The authors state that in using NO2 emission, “the reported mass becomes independent of the ratio of portioning between NO and NO2,” but this is exactly why the convention of ‘NOx emission’ is prevalent in the literature, or even N emission. If regional NOx emission estimates are reported as ‘NO2 emission,’ then regional accounts either mean NOx, or have somehow not accounted for the portion of NOx that is NO. Simply stating that they are reported as ‘NO2 emissions,’ but are in fact ‘NOx emissions’ and then using the latter term would greatly aid the reader. Also, most of the soil emission text and Fig. 7 (and Fig. 6?) discuss NO emission, not NO2 or NOx emission, and there are a number of uses of NOx when, by the authors’ convention, I believe NO2 is meant.

3. Referee 1 technical comment 2: The change does not address the comment. Referee 1 was not asking for clarity in the sentence but for evidence for the claim that a winter and summer peak provide confidence in the method.

4. Referee 1 technical comment 37: The response does not address the comment. The referee was asking for a statistical measure of agreement. Numerical agreement can only be to within uncertainties. That the agreement was surprising to you is irrelevant and should be deleted.

Referee 1 asks for quantification of the rough magnitude of the total error, in addition to discussion of the individual sources of uncertainty. I agree with the referee that this is needed. The new text does not provide this.

5. Referee 2 technical comment 9: I agree with the referee that use of word ‘assimilation’ is unclear.

6. I do not think of agriculture as a biogenic source. Consider replacing ‘biogenic’ with a term that makes it clear you mean the emission from the oasis, where human activities have had a large impact on the NO flux. Also, use of the word ‘anthropogenic’ here really refers combustion emissions, not human activity.

7. Absract, line 24: The paper makes no attempt place results from the Tohsun oasis in the broader context of global managed dry lands. I agree that in this study the oasis source was sizable, but the paper does not address whether Tohsun oasis are scalable such that they are “strong evidence that biogenic emissions from soils of managed drylands … are much more important contributors to regional NO2 budgets … than thought before.” The statement on photochemistry is also not discussed in the text, especially since if the soil HONO is large, than the more important effect may be that soils are directly emitting a HOx source. Additionally, oases should have a disproportionate impact compared to cities as oases are NOx sources to low NOx environments, which will drive O3 production, by contrast increased NOx emission in cities may suppress O3 production, at least in the near field.

8. Section 2.5, line 6: Is not the height of the boundary layer (no caps) assumed? Also, is it not assumed that the boundary layer height does not vary with season, which is likely a poor assumption?

Section 2.5, line 10: Change “the characteristic time (lifetime) of the depletion” to “the NOx chemical lifetime.” I would restate the assumed lifetime here. A second assumption is that the NOx chemical lifetime does not vary seasonally or as a function of the NOx abundance. The NOx lifetime may increase by up to an order of magnitude in the winter. Do you see the same seasonal pattern in urban combustion emissions if the NOx lifetime is treated as longer in the winter, especially in a shallow winter boundary layer? (Some text to this affect appears in Sect 3.3, but should be moved or at least mentioned where described.)

9. Section 3.3, line 29: Rewrite this sentence so as not to say agreement is “perfect.” Instead, agreement should be stated within (or outside) some designated uncertainty range. I recommend that the uncertainty discussion be moved to followed emission estimates. Also, while the discussion is useful, some attempt should be made to quantify total uncertainties. See comment 4.

10. The manuscript has a number of grammatical errors and the revised version should be read carefully to correct these.