Review of ‚ The Turbulent Enhancement Ratio as a novel Approach for Characterizing Local Emission Sources in Complex Environments’ by Lamprecht et al.,

Summary statement:

First, I would like to apologize to the authors for the late turn-in of the review. I hope this report is stil of use to you.

This study proposes a statistical quantity termed the ‘Turbulent Enhancement Ratio (TER)’ to detect and evaluate different scalar sinks and sources of reactive trace gases in urban airflows. The terminology TER is chosen in analogy to a commonly used quantity NER, which has been used in atmospheric chemistry studies when the background concentrations needed to compute excess mixing ratios (EMRs) are unknown. The difference between NER and TER is that NER are computed from slow-response analyzers or time-averaged quantities from fast-response analyzers, while the instrumentation for quantifying the TER can resolve the turbulent motions and hence the variability on shorter timescales. In a first step, TERs from long-term observations are compared against a third quantify termed ‘flux ratio’ FR for validation, before they are used to study bulk statistics and case studies for the observations in Innsbruck partly dedicated to separating the effects of the anomalous covid-19 lockdown to ‘normal’ conditions.

I find the current study already has some merit, but to tap into its full potential and merit full publication it requires a much more thorough presentation and discussion of the definitions, similarities, and differences across the statistical flow and flux quantities. Since this journal is concerned with ‘techniques’, these questions need to be answered unambiguously. Based on the current draft I cannot tell whether the authors are aware that mathematically the TER is identical to the NER, or if it is just a poor explanation/ presentation of the statistics or an oversight. What is correct is that our physical interpretation of these quantities may be different because these quantities may represent different portions of the turbulence spectrum and/ or the mean flow, and hence the processes contained in these statistical quantities may be different. I explicitly say ‘may’ because the authors do not define the meaning of their triangular brackets usually indicating some spatial or conditional averaging in Eq. 3, and hence I cannot tell if true physical or mathematical differences exist. To me, the TER is rather a spectral similarity ratio rather than a novel quantity separating sink and sources since it is almost identical to the FR, but again, the authors need to improve its explanation. The later part dedicated to bulk statistics and case studies is informative, I have some minor questions about specific statements listed below.

In summary, I believe that the current draft may offer substantial merit after the statistical questions are clarified. The study fits well into the scope of the journal. I recommend reassessment after major revisions.

Major comments:

1. Definition and novelty of the TER: As mentioned above, mathematically the TER in Eq. 4 is identical to the NER in Eq. 3. What remains unclear, why and at what timescales you apply the averaging. Recall that Reynold’s first postulate states that the average over all perturbations is zero by definition (I save the time to type this simple equation in the processor), so your triangular brackets cannot mean averaging over the length of the perturbation time scale to derive the perturbations indicated by the primes. So what do they mean? Some physical averaging in the analyzers because it does not capture the full turbulence spectrum down to the Kolmogorov length scale? And what do the triangular brackets mean in Eq. 3? A longer time scale? Please clarify. Deriving Eq.3 from Eq. 2 is not trivial and involves some differential calculus operations, so you need to walk the reader through this process or reference an appropriate source, since this a technical ‘techniques’ journal and at the heart of your supposedly novel quantity. In addition, it is unclear to me why you claim the validity of Reynold’s second postulate to lead from the LHS to the RHS of Eq. 4. This would imply that $\overbar{Y}$ and $\overbar{X}$ are zero, which is difficult to imagine given the supposedly shorter averaging time scales indicated by the triangular bracketing $ \langle \rangle$ (see earlier argument). Only at the averaging time scale indicated by the overbar (i.e. the perturbation time scale), the advective term becomes zero as $\overbar{w} \equiv 0$ because of the rotation. I am confused, please explain all steps and assumptions of the derivation clearly. Similarly, in Eq. 5 you need to explain, if the triangular and overbar averaging are identical to the one used in Eqs. 3 and 4. You may also link your derivation of Eq. 3 to the set of equations for the Relaxed Eddy Accumulation technique, which uses a very similar definition of the b-coefficient as the slope ratio of plotting $w\prime$ versus $c\prime$ in a quadrant analysis plot. Actually, explaining your perturbations and averages using a set of quadrant plots of $w\prime$ versus $CO2\prime$, and $w\prime$ versus $NO_x\prime$, and a scalar-scalar plot of $CO2\prime$ versus $NO_x\prime$’ for the different analyzers may be very illustrative to explain the differences.
2. Following the comment in A, I think the authors need to include the sampled turbulence spectra for their quantities to make any inferences about which portion of the power-/ cospectrum is resolved and their physical interpretation.
3. Section 4.1: It is difficult to truly understand the very close to 1:1 relationship of the TER versus FR for NO_x and CO$_2$ without the information requested in comment A. It would suggest that the denominator in the RHS term of Eq. 4 is identical to the denominator in Eq. 5, assuming that the numerators are identical. Hence, I think the TER can rather be interpreted as a spectral similarity ratio rather than a novel quantity representing differences in sink / source. The use of TER reminds me of the triple decomposition (Antonia, R.A., Browne, L.W.B., Bisset, D.K., Fulachier, L., 1987. A description of the organized motion in the turbulent far wake of a cylinder at low Reynolds numbers. J. Fluid Mech. 184, 423–444.) often used in turbulence analysis, which decomposes the excursions from a mean into two different time scales, which are subject to different forcings. I think the authors want to root their statistical quantities in the existing turbulence literature and point out similarities and important differences. Please add the data density isopleths to the plots, these scatter plots with most datapoints overlapping each other centered around the line of unity may give a false representation of the variability. Bars indicating variability (not uncertainty) need to be added to both axes (ordinate and abscissa), I suggest using an bin averaging operator of variable width such that the number of data points included on the a-axis are identical (and hence the standard error defined by $sigma \sqrt{N}^{-1}$), since N varies dramatically across bins because of the uneven pdf.

Detailed comments:

1. Page 4, line 18ff: Please briefly add the most important EC processing steps, this information is important to understand the behavior of the FR and the results of evaluating TER vs. FR in Section 4.1.Do you mean a correlation coefficient $r\geq$ 0.5 or its magnitude? Please clarify.
2. Page 8, line 5ff: not sure what you call the 'bias', but you essentially evaluate the loss of co-variance from 5s to 30min, compared to 0.2s to 30min. Factor of 1/0.43 approx. 2.2 is reasonable. Again, if you show the turbulence cospectra, or even better its cumulative Ogives, then this ratio (and not bias) can be explained.
3. Figure 3: It may be misleading to express the ratio in percent, please use fractions. Since the number of trucks on Sundays is so small and the bar invisible, please use relative scaling in the y-axis.
4. Page 10, line 22ff: I recommend checking for excursion from common wind patterns when nocturnal winds are up-valley, and daytime winds are down-valley (which must exist) to separate differences in sinks/ sources from their advective distribution.
5. Section 4.3.1: it is unclear to me why $F_{CO_2}$ by depending solely on temperature? The net CO$_2$ flux integrates over all sinks and sources including plant uptake (photosynthesis), and plant release /respiration) and release from combustion etc. You had mentioned in the introductory section that you see CO2_s uptake by plants during daytime (leading to negative CO_2 fluxes which is surprising given your height well above the buildings), so why is the net flux always positive here? In urban environments it usually is, I am confused. I think this section needs to be improved. Similarly, is the ‘heizgrenze’ temperature visible only in the transitionary seasons (spring, fall), or also during the summer? Even in the summer the daytime/ daily temperatures may drop down to 10 deg C. This analysis would lend better support to your claimed explanations.
6. Page 13, Line 6: The term RCP for me is taken by the IPCC’s ‘representative concentration pathway’, please check if there is alternative terminology for your field.
7. Page 13, line 28: please only note significant digits.
8. Page 14: Lines 6-11: I would like to see wind speed and dynamic stability / cross wind variance be included in the discussion, as wind direction alone oversimplifies the interpretation. The flux footprint will vary also with the additional quantities.
9. Section 5: I think some portion may need to be rewritten after addressing the major comments.

The paper presents a novel method of examining sources of pollutants (in this case NOx) in an urban environment using a ‘Turbulent Enhancement Ratio (TER)’. The quantity is calculated from fast response analysers, thus resolving the turbulent motion of the pollutant. The TER is compared to a flux ratio (FR) of the pollutants (NOx / CO2), calculated using the widely used eddy covariance technique for each species. Once it has been shown that the agreement between the TER and FR is good,  the authors use TER to examine sources of NOx in the Innsbruck area, in particular using the difference between COVID19 lockdown and ‘normal’ times.

This is an interesting paper describing a novel technique that could lead to important insights into air pollutant emissions in urban environments. I recommend publication subject to the following revisions and additions.

General comments

1. I think the manuscript needs more discussion as to why the TER is preferable to standard Eddy covariance fluxes? It seems that they essentially give the same thing (especially when looking at ratios), and both require high time resolution measurements. So what are the main benefits of TER.
2. On page 8 line 10 it is stated that TER is the preferred methodology (compared to the more widely used normalised emission ratio (NER)). It is not clear to me why this is the case, and this section would benefit from an expansion to better explain this.
3. Page 13 line 8. This paragraph would benefit from expansion. It says that higher CO2 fluxes are seen in the colder seasons the result of increased domestic heating in these seasons. This is almost certainly true but why do the NOx fluxes not also increase in the colder season? Presumably there is also a NOx emission from heating – is this not observed at all? Please comment on this.
4. In section 4.3.2, the authors could comment on whether their data shows a change of dominant source during the lockdown period (i.e. does the NOx / CO2 ratio suggest a change from traffic dominated to domestic heating dominated emissions), as has been seen in other studies (e.g. Cliff et al., ACP, 2023).
5. The authors state that they have a data series from mid 2018 to early 2022 but do not comment on any longer term trend. It would be nice to see if the NOx / CO2 ratio has changed from the start to the end of their dataset (when COVID restrictions had been lifted) and what any change could be attributed to.

Specific comments

2.2 Instrumentation section: It is not clear which of the two NO2 measurements is used for the calculations (of TER, NER and fluxes). If it is the Moly converter NO2, have the authors investigated any potential issues with the residence time of air in the converter and the validity of 5Hz measurements?

Table 1: what do 'dd' and 'ff' represent in the measured parameters from the sonic anemometer? It is probably obvious but should be made clearer.

P 13 line 24: It says ‘the TER remains higher’ but higher than what. Please better explain this sentence.

Section 2.3: I think it would benefit from a slightly more detailed description of how the eddy covariance fluxes are calculated, including the key parameters and filtering methodology used. I realise it is in the literature but just a few sentences would greatly benefit this paper.