|Introduction, pg 4, lines 15 – 35: I found this revised section a little misleading. I think this could be rectified if the magnitudes of modelled to measured HO2 (and modelled to measured p(O3)) disagreement are compared in absolute terms. In the Tan et al (2017) study, modelled and measured HO2 agree within uncertainty at 6 ppbv NO. By eye, (but the authors can provide an accurate number) at 6 ppbv NO in this study P(O3) measured is ~20 ppb hr-1 greater than modelled. The Tan et al (2017) study does not support the magnitude of the P(O3) discrepancy reported in this work and this needs to be reflected in the Introduction.|
The authors have made some attempts to improve the corrections applied to the raw MOPS data by limiting times when RH was below 70%. It is not obvious from looking at the latest time-series in Figure 1 that the MOPS data coverage presented has reduced. Was this threshold RH already applied before the initial submission?
There is still a lot of uncertainty associated with all the corrections applied, however. The authors state that the negative ozone production rates are ‘roughly correlated with temperature, relative humidity, or actinic flux’. Could the authors provide an equation of the form:
Artificial signal = Temperature × a(±b) + RH × c(±d) + hν × e(±f)
This will provide some confidence in the corrections applied.
Related to this point, the authors discuss the days chosen for the zero measurements: ‘zeros that were taken only on days with diurnal patterns and absolute values of relative humidity that are similar to most MOPS measurements days’. The authors need to be specific here, what do they mean by ‘similar’ and ‘most’? Furthermore, this statement begs the question, how similar was temperature and actinic flux on these days also given the correlation with these parameters too?
It is not clear in Figure S2 which line relates to which RH?
Section 3.3 is much improved from the initial submission, however, a couple of modifications are needed:
Pg 12, line 32: ‘either all of these measurements methods contain similar artifacts..’ this argument does not hold. Why, if this is an instrumental problem rather than missing chemistry does this have to relate to a similar artifact? Rather, the MOPS artificial signal may derive from heterogeneous production of radicals or radical precursors whilst the previous FAGE measurements could be influenced by an RO2 interference. This sentence needs to be modified to reflect this.
The authors argue that the positive excursion in P(O3) is apparent even before the zero correction is applied and use this as evidence that the positive excursion is not an instrumental artefact (pg 12, lines 22 – 27). I do not agree with this reasoning. It may be true that the zero correction is not inducing this positive P(O3) observed in the mronings, but other artifacts, for example, artifacts induced by heterogeneous NO2 reactions in the chamber could be contributing to this signal. The authors mention on Pg 7, line 25 ‘excess HONO of up to five times ambient values was measured in the MOPS chambers’ and that the ‘production mechanism has not been identified’ Really, systematic laboratory studies are needed to determine the absolute magnitude of this heterogeneous HONO production as a function of NOx. Failing that, the authors should at least modify the discussion in section 3.3.1 to reflect the fact that the model measurement discrepancy at high NOx could be caused by a currently unidentified HONO (or radical) production mechanisms in the MOPS that may not necessarily scale with NOx as assumed in section 3.3.1.
Figure 6, Some comment is needed about why P(O3) in the MCM3.3.1 RO2=0.0005x[NOx] scenario is lower (despite [RO2] concentrations being higher) than the base MCM case in the afternoon.
Also the scenario where RO2+NO HO2 + NO2 is not shown in Figure 6 as indicated in lines 27, 28, pg 16 (unless it is represented by the green dashed line, in which case the legend needs correcting).