The manuscript has four main components: (1) measurements of the UV-Vis spectra of several iodates and other salts, (2) measurements of the photochemical decay of ammonium iodate in low temperature ices, (3) an estimation of the absorption cross-sections of NH4IO3 in ice, and (4) modeling of the impact of NH4IO3 photolysis on IO levels in the Antarctic boundary layer. Of these four components, the first should be redone to give accurate molar absorptivities (cross sections), the second is generally fine (though more details are needed), the third component should be completely redone, and the fourth requires much more information to be useful. These points are discussed in more detail below. The authors were sometimes responsive to the comments of past reviewers, but in some important cases were not. While the manuscript has several problematic areas, if the points below are addressed I would recommend that it be accepted after these major revisions.
1. The authors need to properly measure the absorption cross sections (i.e., molar absorptivities) of NH4IO3 in water. This requires approximately 6 solutions of different concentrations; they currently have only 2 concentrations. At a given wavelength, a linear regression of the good Abs data from the 6 solutions (i.e., within the linear range of the instrument, approximately 0.01 - 1 AU) versus (concentration x pathlength) gives a slope equal to the molar absorptivity (in units of L mol-1 cm-1) at that wavelength; this can be converted to typical cross-section units (cm2 mlc-1) if desired. These values should be shown in a figure and tabulated in the supplemental material.
2. The measured rate constants for photolysis of ammonium iodate are the highlight of this paper. More information about the results should be given. For example, on Page 10, lines 8 – 27, the authors describe the rate constant data but don’t show it except for Figure 6, which is difficult to decipher. To accompany this figure there should be a table of the conditions and resulting rate constants for loss of NH4+ from all of the experiments. This would help the reader evaluate the claims on this page.
3. (a) As pointed out by Reviewer #3, the current method for estimating the absorption cross section by frozen NH4IO3 is a very poor choice. There are at least three reasons that this method should not be used: (1) it requires assuming a quantum yield, for which there is no data, (2) the spectrum of NH4IO3 appears to be poorly fit by a single Gaussian, as there seem to be 2 or 3 overlapping peaks in the long-wavelength end of the spectrum, and (3) the assumption that "...approx. 95 % of the value of the integrated cross section would be in the range from 300 to 500 nm..." is a completely arbitrary red-shifting of the spectrum. Several papers have found that the absorbance spectrum of a species in ice is very similar to the solution result (e.g., NO3- and 4-nitrophenol in the work of Dubowski and Hoffman) or is red-shifted somewhat (e.g,. the benzene work of Kahan and Donaldson). It would be a better estimate of the NH4IO3 spectrum on ice to take well-measured solution molar absorptivities (i.e., point #1 above) and red-shift them by the 30 nm seen for benzene on ice. (b) Once the authors have this spectrum they could use it to estimate the quantum yield for loss of NH4+/IO3-; as part of this they should examine how sensitive the result is to the extent of red-shifting of the solution absorbance spectrum.
4. (a) There is so little information given for the model simulations that they are impossible to critically assess. Enough details of the model inputs, along with figures of key model outputs, should be given in the supplement so that the reader can assess this component. (b) Rather than use the "experimentally-derived" (and almost certainly wrong) absorption cross section values and an assumed quantum yield of unity to estimate a rate constant for reactive halogen formation, the authors should simply use their average experimentally measured rate constant, adjusted to polar sunlight conditions as best they can. (c) The assumption that every photon leads to release of a gaseous, reactive iodine species is almost certainly wrong. Even every loss of IO3- probably does not equate to formation of reactive, gaseous iodine since the iodination of ammonium is likely to be a major mechanism for the reactivity. At the very least, a sensitivity study of this parameter should be done in the modeling results.
5. Page 6, line 27 – page 7, line 11. (a) It is not clear how the authors estimated that 42% of the lamp power is emitted between 300 - 900 nm. This should be described in detail, along with the corresponding calculations, in the supplement. They should also indicate why it matters that 42% of lamp power is between 300 - 900 nm. The wavelengths above 400 nm likely play no role in photochemistry since frozen IO3- probably does not absorb in this range. (b) Similarly more details about the calculations of the incident photons are needed. Were wavelengths below 300 nm ignored? If so, this should be changed: the authors should show the product of (the IO3- cross section) x (the % transmittance of the glass) x (the lamp output). This action spectrum for light absorption will show which wavelengths are likely most important. Based on the steep curve of the solution IO3- results, and the shallow cut-off of the glass, I suspect wavelengths below 300 nm are important. The lamp output, calculated action spectrum and calculations should be shown in the supplement. (c) I agree with one of the reviewers that the Thermopile likely does a poor job of revealing the photon flux in the ice sample. Part of the problem is that it measures a wide wavelength range, but the more serious problem is that it cannot account for internal reflections in the ice sample. For example, if the Si substrate is highly reflecting, the photon flux in the ice sample will be approximately twice (or more) as high as the incident photon flux measured by the Thermopile. Unfortunately, I don't think actinometry will work under the cold, high vacuum, conditions of this experiment. But the authors should acknowledge the potential large bias of the thermopile in the manuscript.
6. Page 8, lines 6 – 17. (a) The linear slopes in Figure 4 don't necessarily mean a 1:1 relationship between NH4+ loss and IO3- loss. The authors should look more carefully at this data to understand the ratio of loss. One way to do this is to plot ln((NH4+)t/(NH4+)0) vs. ln ((IO3-)t/(IO3-)0) for each experiment, where (x)t and (x)0 are concentrations of x (ammonium or iodate) at times t and zero, respectively. The slope of this plot will give the stoichiometry between NH4+ loss and IO3- loss; from the current plot it is difficult to assess the stoichiometry. (b) Equation E2 assumes a 1:1 stoichiometry, so it should be modified if the stoichiometry is different. (c) The manuscript should show a Figure 4 equivalent figure for samples containing water in the supplement. (d) Some of the accompanying dark data should be shown on Figure 4.
7. Page 9, lines 18 – 27, and other locations throughout the manuscript. I agree with Reviewer 1 that the there is no good evidence for the previously hypothesized reactions and that they should have been removed from the manuscript (which they were). I have a problem with the new R1, which is cited as coming from Klaning et al. (1981), but I don’t see this reaction in the Klaning paper. If it is not in this reference, it should be removed from the manuscript. Similarly, R2 seems an unlikely conjecture that should be removed and the suggestion that O- reacts with NH4+ seems unlikely. Oxidation of NH4+ is very difficult; even OH has a relatively slow rate constant. Thus I think it is unlikely that O- or OH is oxidizing NH4+. Rather, I suspect that the ammonia is getting iodinated, perhaps by I2, to form species such as NH2I and, perhaps eventually, NI3. Some of the information is in the McAlpine reference. I suggest that the possible mechanism be discussed in one short paragraph, keeping the current caveat that it’s largely unknown.
1. I agree with one of the Reviewer’s comments that the title should indicate “ammonium iodate” rather than “iodate salts” since only the photochemistry of NH4IO3 was studied.
2. page 3, lines 12-16. This paragraph states that the IR absorption coefficient of iodate is not known, so that IO3- couldn’t be quantified in samples. But later in the paper the authors quantify IO3- with its IR absorption. This apparent discrepancy should be clarified.
3. page 4, line 20 – page 5, line 29. (a) The description of sample preparation is confusing. The necessary information is present in this section, but it needs to be better organized. (b) page 5, line 4: It’s not clear which process is being cited here: water sublimation or preservation in original diluted salt proportion? (c) page 5, line 16. What temperature and time was used to transform amorphous ice to cubic ice? (d) page 5, lines 23 – 29. What times and temperatures were used for annealing in these various steps.
4. page 6, line 19. The calculation of the integrated absorption coefficient for IO3- should be shown in the supplement. Is it based only on one sample or multiple samples for both NH4+ and IO3-? The authors should give an uncertainty on this value, by propagating uncertainties in experimental data and in the literature value for NH4+ band.
5. page 6, lines 21 – 24. It's not clear what this sentence means (i.e., only the highest frequency photons were considered) since in the rest of the paragraph the authors discuss the very large 300 - 900 nm range.