See reviewers' comments for outstanding issues that require addressing. I would especially draw your attention to the point raised regarding the correlations with Ox. Both reviewers are now requesting this and I happen to concur; If there is a relationship between SSA and Eabs with Ox, then a direct correlation is the best way to test this, rather than a correlation of the diurnal profiles and not showing this in the manuscript undermines the credibility of the manuscript. While examples are given in the rebuttal of this type of graphing, these concern gas phase processes that are more likely to be intrinsically related to actinic flux, which has a very strong diurnal causation. In this instance, if a direct relationship between Ox and the measured parameters doesn't exist, then this would throw into question the conclusions of the paper; it would imply strongly that the correlation noted in diurnal profiles was not causal, i.e. that some other diurnally-modulated processes were responsible for changing the variables in such a way that their average diurnal profiles resembled one another, but they were otherwise unrelated.

I thank the authors for generating the requested graphs vs Ox, however I deem that these are important enough that they should be included in the manuscript alongside the other analyses and the authors should revise some of their interpretations and conclusions accordingly.

While the diurnal patterns may show a nice relationship, I have yet to see any evidence presented that supports the assumption that this relationship is governed by a single common factor such as photochemistry (see below), so this undermines the logic of this being used as a primary basis for the interpretation. For one, I would note that the Eabs vs Ox graph fails to exhibit the uptick in Eabs above 50ppbv and would appear to actually decrease above 80ppbv. I take this as clear evidence that the 3-stage model proposed by the authors is unsound and in need of either revision or complete removal from this paper.

Generally, I feel the authors may have misinterpreted my earlier statement concerning diurnal patterns, as the statement made on page 6 of the revised manuscript is factually incorrect. A clear diurnal pattern does not, as stated by the authors, mean that photochemistry is the intrinsic governing factor because the diurnal patterns of urban pollutant concentrations are also very strongly linked to human activity (e.g. traffic, cooking, heating) and boundary layer dynamics. BC will be subject to all of these factors and in many cases the factors are intrinsically difficult to disentangle based on observations alone. For instance, photochemistry is promoted by the increasing actinic flux during the morning, but this also corresponds to an increase in solar heating of the surface, which in turn promotes vertical mixing and the exchange of fresh pollution in the lower parts of the boundary layer with background air from aloft, which may include more aged pollution. Furthermore, there is often a general reduction in primary emissions after the morning rush hour subsides. The net result is that there can potentially be an apparent 'ageing' of the pollutants without having to invoke any photochemistry at all. To explicitly link observed changes in BC properties to in situ photochemistry alone requires all other confounding factors to be discounted, which isn't done here.

Note that this is not to say that photochemistry isn't responsible on some level; if the pollutants with high Eabs and Ox concentrations are aged transport from sources upwind, it is still reasonable to assume that photochemistry is ultimately responsible for the ageing; it is not simply in situ photochemistry, which seems to be the working hypothesis here. The authors should rephrase these sections accordingly to treat the underlying processes governing the diurnal profiles with more caution.

Furthermore, I'm not convinced with some of the other responses to the latest round of comments. There is simply no direct evidence presented that the observed changes in Eabs are due to morphology rather than coating thickness, so this must be treated as a speculative explanation unless further evidence can be offered to rule out other effects.

Following from these, there are many inferences drawn that should be addressed before this goes to publication. There is simply no basis for saying that the changes in optical properties are caused by the higher Ox (e.g. Page 9, line 17) because this is merely assuming causation, which I regard as being in doubt. The authors must go through the manuscript and temper their language to this effect; I would recommend that they refer to the increases in Eabs being 'associated' with changes in Ox, which is a far safer statement.

Overall, I still consider this paper to be publishable because there are some interesting observations and trends noted, however there is currently a tendency to over-interpret the data and make statements that are not supported by the evidence and this must be addressed.

I am very concerned that the key issue identified by the reviewers and myself is not being addressed to the point that it is being consciously avoided. Specifically, I asked that the analysis vs Ox be included in the manuscript, but instead, the authors have merely included this in the supplement, while leaving the original graphs in place in the main manuscript. Furthermore, while the 3-stage model has been taken out (although the three fit lines are still present in figure 6), the authors still discuss a 2-stage model on page 10 as follows, "In the second region, Eabs was unchanged (2.26 ± 0.06) for Ox mixing ratios between 35 and 50 ppbv. These two regions are most likely corresponded to Peng et al.’s (2016) two-stage morphology variation mechanism, in which collapsed semispherical BC is transformed to a spherical morphology (Gustafsson and Ramanathan, 2016)." This statement is in contradiction to Eabs analysis binned according to Ox on figure S10, which shows a more monotonic increase in Eabs up to about 45 ppbv. Therefore, for the statement on page 10 to stand, the diurnally-averaged method must have to be shown to be more statistically or scientifically valid than the Ox-binned method.

In choosing to ignore the Ox binned data in favour of the diurnally-binned data, the clear implication is that the authors consider the diurnal method to be the more scientifically meaningful, in spite of the fact that the reviewers consider the Ox-binned method to be a more obvious approach. The onus is therefore on the authors to present a robust case for the validity of the diurnal method, but unfortunately, I don't see this in the current manuscript. The justification is given as follows: "Different from the hourly average of all the data points, diurnal analysis reduces the influence caused by weather condition from day to day and provides a more smooth trend of the observed parameter, which has been demonstrated in the study of the main factors governing the diurnal cycles of the aerosol properties (Backman et al., 2012)." This justification I regard as being wholly insufficient. To take it point by point:

1. The 'weather conditions' referred to will include sunlight, so in reducing this influence, this averaging method will accordingly diminish the role of photochemistry relative to activity-based emissions patterns (which will not be diminished), thereby making this analysis less, not more, valid to the working hypothesis.
2. Stating that the data is 'more smooth' is not a complete justification because one also needs to demonstrate that the smoothness is a result of the data being more meaningful, not that the data has been artificially smoothed on a mathematical level, which can introduce erroneous artefacts.
3. The Backman et al. reference does not provide a precedent for the methodology used here. While this paper does present diurnal averages, it does not scatter plot diurnally averaged data, as has been done here.

I had originally hoped that the inclusion of this Ox-binned analysis would be relatively straightforward in this paper as the results are qualitatively the same, so on the last version, I had marked the revisions as 'minor'. However on seeing this version of the paper, I am now concerned that there is too much of the work that is invested in the quantitative comparison of data after diurnal averaging, which I am yet to be convinced is a sound approach. As such, I have decided to mark this version down as needing 'major' revisions. In order for me to consider this publishable, I would consider that the authors must do one of the following:

1. Present a more robust justification of the diurnal methodology (which I am now becoming increasingly concerned is not possible)
2. More clearly compare the diurnal method with other binning approaches (i.e. in the main manuscript) and discuss the similarities and differences, and restrict the interpretation of the diurnal comparisons to purely qualitative, rather than quantitative, analysis.
3. Redo the quantitative analysis using a more scientifically defensible binning approach

The reviewers and I are now happy with how the manuscript has been revised and I thank the authors for taking our comments on board. The reviewers have a few further comments that I would like the authors to address, which I think should be fairly easy to take care of; it should be unlikely that this will need to be reviewed again.