Dear authors,

I have read your revised manuscript very carefully. Both referees‘ criticisms and recommendations have been adequately dealt with, and the data and scientific results can be published in Atmospheric Chemistry and Physics subject to only two small technical corrections:

Page 2, lines 11 – 13: this list of references is unbalanced and somewhat arbitrary. You cite almost every relevant paper published in the 60s and 70s, but ignore much of the work in the 1990s and all of the work done on the subject since 2000. Maybe you can find some recent papers that give an overview and cite “and references therein”.

Page 16, line 7/8: “…up to more than…” doesn’t make sense, because that would technically include every possible value. It should be either one or the other, or maybe you want to give an actual range.


However, I would also like to mention that, as I’m sure you are aware, some of your results raise important questions and/or are in conflict with our current understanding of OCS cycling (and to some extent atmospheric transport). I do not ask you to answer all these questions, but I think the paper - and the OCS research community - would benefit from pointing out some of these questions and conflicts more explicitly and maybe with some sense of urgency. Note that I do not REQUEST this for the paper to be published, and I leave it up to you whether and how to deal with the SUGGESTIONS that I make below.

1. Differences between MIPAS and ACE-FTS in the 13-16 km altitude region

I find the large difference in the region just around the tropopause (probably slightly below in the tropics and slightly above at higher latitudes) disturbing, because our understanding of OCS cycling and transport and its parameterization in models would be significantly different depending on which satellite data set we use to constrain our models. If I just look at the general shape of the ACE-FTS profiles shown, i.e. quite homogeneous throughout the free troposphere and starting to decrease with altitude right around the tropopause, they seem to go along well at least with my understanding of OCS cycling and atmospheric transport. The MIPAS profiles shown in Figure 5 always have higher OCS in the tropopause region compared to the free troposphere by 10s of ppt. To explain this, you would either need a fast transport mechanism from an OCS loaded boundary layer that completely bypasses the 5-10 km altitude region, or you would need an OCS source gas that is transported to the UTLS and only there is converted to OCS. I’m not saying that the MIPAS data are wrong and ACE is right, but the implications for our scientific understanding are so tremendous that I want to ask you to correspond a greater sense of urgency to look into this difference and try to understand and eventually resolve it (ideally on both the ACE and MIPAS sides). A better consistency between the two major satellite data sets of OCS would also be helpful for the manuscript in preparation by Deshler et al. that is mentioned in your conclusions as it actually uses both ACE and MIPAS data.

2. Time lag of the seasonal cycle in the northern hemisphere free troposphere

You describe the observed seasonality of OCS at 10 km altitude in the N.H. high and mid-latitudes to be “caused by overlap of oceanic release and of vegetative uptake of OCS during the growing season, which affects the free troposphere with a delay of some months.” (later, this phase lag is quantified as “4-6 months”). Such a long phase lag between surface and free troposphere seasonality contradicts Figure 6 in Montzka et al. (2007), where the phase lag in aircraft measurements compared to the surface is on the order of 1 to 2 months, and a phase lag of several months is also not observed for the fairly similar seasonality of CO2 (e.g. Gurk et al., ACP 8, 6395, 2008). In a way, what you are suggesting here is some kind of “tropospheric tape recorder”, which does not exactly represent our current understanding of atmospheric transport in the troposphere. From the timing, the observed seasonality could be better explained by influence from the stratosphere (downward mixing of low OCS polar vortex air in spring, lower TP height in fall/winter so that stratospheric air makes a larger contribution to the MIPAS averaging kernel centered at 10 km), but this would be inconsistent with your rather high OCS mixing ratios at this altitude already mentioned in the comparison with ACE above. Unless there is some information that I’m lacking or misunderstanding, I suggest that you state in the discussion that there is currently no plausible explanation for the observed OCS seasonality at 10 km.

3. Difference to EMAC in the NH free troposphere

Even when folded with the MIPAS averaging kernels, the EMAC model produces an OCS minimum throughout the entire mid and high latitude NH troposphere in boreal summer and fall (Figure 9). In the model, this minimum is without doubt caused by the strong seasonal vegetation sink. Looking at the way you draw conclusions from less pronounced signals (in terms of OCS differences) in your observations, it is surprising that such a strong signal as suggested by EMAC does not show in the MIPAS data at all (Figure 9). Since you propose in your conclusions that the new “data set can be used to constrain future model runs and thus can help to improve the understanding of the global sulfur cycle”, you may want to mention that the comparison study in your paper already suggests that, at least in the northern hemisphere, the vegetation sink for OCS may not be as large as some people currently believe.

4. Tropical ocean source of OCS

In several places in the paper (Abstract and Sections 4.1.3, 4.3.3 and 5), the observation of enhanced OCS in the upper troposphere, particularly over the Pacific and Indian Oceans in boreal summer, is attributed to an oceanic release in a manner suggesting that this attribution is straightforward and uncontested. But how do you know it is oceanic release? Can you provide arguments that the enhanced OCS really comes from the ocean? There has been one recent ocean modelling study (not well constrained by observations) by Launois et al. (ACP 15, 2295, 2015) suggesting high OCS fluxes from the tropical oceans, but observational evidence in the marine boundary layer and in the water column draws a very different picture (Lennartz et al., ACP 17, 385, 2017; and none of the many process studies of oceanic OCS release made in the 1990s and early 2000s would warrant a strong source in the tropical oceans). Furthermore, Blake et al. (JGR 109, D15S05, 2004) have also observed enhanced OCS in the free troposphere over much of the Pacific ocean, but they suggest a very different explanation, i.e. a continental and most likely anthropogenic source, and they do so on the basis of explicit transport studies. I suggest you at least mention this alternative explanation, and give some acknowledgement that the idea of the tropical ocean being a strong source of atmospheric OCS is at least highly contested.

Best regards,
Marc von Hobe