Please follow the suggestions of reviewer #1, copied below, for additional minor revisions. In addition, and if possible, please address the following question left open from the response to reviewer #2.

Reviewer #1:

Overall, the authors have done a very good job of revising the manuscript and recommend that the manuscript be published with consideration of the following points about inlets:

1. Inlet characterization - Delay is only one aspect of characterization of an inlet. One can easily correct for delay simply by phase shift of the original signal. I assume that was done. I was asking that you describe the attenuation characteristics (i.e. smoothing) due to the inlet. For example, what was the e-folding time of your 'step change' in your experiment when it appeared at the detector, and how do you extrapolate that to your actual inlet?

There are several sentences starting at line 23 that did not make sense to me. Conclusions are made about inlet properties based on your inferences from the results - which were filtered through the inlet in the first place. That seems circular. Also, the text talks about "underestimating" the concentration - perhaps you mean "underestimating the variance in concentration"? Reporting as "lower limit" does not make sense. That is ok if ambient concentrations are increasing. If they are decreasing then smoothing in the inlet means you have reported an upper limit. Anyway, "underestimating" or "overestimating" this presumes there is no production/loss in the inlet which has not been demonstrated.

2. It is probably not reasonable to consider the inlet as a clean Teflon surface. Once sampling starts it is coated with a complex mixture of organic and inorganic aerosols, adsorbed gases, and reaction products resulting from heterogeneous chemistry. Ozone is continuously deposited to the inlet surface where it can generate ozonides, free radicals, and peroxides on the surface. H2O2 and organic peroxides are also deposited. Strong acids (nitric, sulfuric, SO2 oxidation) and ammonia (or other amines) are also present. Some teflon is also quite transparent, so photochemistry can occur (depending on the type/color of the teflon and whether it was covered.

Sadly, inlets are complex environments. The burden is on us atmospheric chemists to show that what we measure is not an inlet artifact. If the inlet is not characterized, then it should be acknowledged as an uncertainty for future studies to investigate. I don't think it makes sense to minimize the possibility of artifact. Numerous discoveries in atmospheric chemistry have turned out to be artifacts.

3. I am not a synthetic organic chemist but I did not find the argument against formation of MSAM in the inlet to be compelling. Certainly synthesis from a sulfonic acid is unlikely, but perhaps there are other potential precursurs. How about dimethysulfoniopropionate (DMSP)? It has a built-in S+ because it is a zwitterion. I also believe it has been reported in aerosols over the Indian Ocean. It seems more conservative to simply state that you don't know of a pathway to production on the inlet, but it remains a possibility that cannot yet be ruled out. I suppose this is a matter of style rather than fact.


Reviewer #2, remaining question:

Provide a calculation of the required waterside concentration to support a gas-phase MSAM concentration of 50 ppt at typical wind speeds for the region, or state why such a calculation is not feasible.