Savolainen and co-authors present in-situ measurements of air pollutants in a street canyon in wintertime Helsinki and investigate road traffic emissions and their impact on air quality. Measurement data evaluated in this study are from a five-week campaign in 2022, and emission factors (EFs) of particulate and gaseous pollutants were calculated based on linear regressions between geometric means of air pollutant concentrations and binned CO₂ mixing ratios. In addition to regulated air pollutants typically associated with road traffic emissions, the authors also investigate additional compounds such as organic and inorganic chemical components of particulate matter (PM), volatile organic compounds (VOC), and even compounds such as ozone, which is not directly emitted by traffic. Field-based measurements of EFs from road traffic are extremely valuable in order to be able to compare estimates representing real-world conditions with bottom-up estimates and regulatory requirements. Thus, the topic is very important and well within the scope of ACP. However, interpretation of the calculated EF metric and the so-called impact factors is at times misleading and many statements should be presented more carefully. My major comments are summarized in the following:

1) The methodology to calculate EFs presented in section 2.3 is based on the assumption that road traffic is the major source of CO₂ and the measured pollutants. However, the authors themselves state "that the method is susceptible to non-vehicle influences [...], such as regional wood combustion and long-range transported pollution" (l. 183/184). Could the authors give a quantitative estimate of the contribution of other sources to CO₂ mixing ratios at the site under wintertime conditions?

2) While it is not explicitly stated in the manuscript, the emission ratio ERp in equation 1 (l. 156/157) is probably derived from the slope of the linear regression fit between geometric mean values of pollutant concentrations and CO₂ mixing ratios in 5 ppm CO₂ mixing ratio bins. When averaging pollutant concentrations in CO₂ mixing ratio bins, the change in pollutant concentration per change in CO₂ mixing ratio is not only related to emissions from a common source but there could also be non-causal correlations, for example, simply due to related diurnal cycles of the pollutant concentrations and CO₂ mixing ratios. I expect that CO₂ mixing ratios exhibit a clear diurnal cycle, and one would probably obtain rather good linear fits with high R² values for many atmospheric variables not related to road traffic emissions, e.g. meteorological variables such as air temperature and wind speed. Therefore, R² values of the averaged linear fits close to 1 do not necessarily indicate that the pollutants are mainly derived from road traffic, as stated e.g. in l.209-211 ("R² values of the averaged linear fits were above 0.93, showing that the pollutants were mainly derived from road traffic at the studied site"). This is a major limitation of the study, and interpretation of the calculated EFs must be presented in a more careful way.

3) Related to my first two comments, there are several instances when the authors acknowledge that the CO₂-based EF calculation can be difficult to interpret, e.g.:

l.483/484: "Thus, even though CO₂ is generally a good tracer for road traffic, the CO₂-based EF calculation could be challenging if there are other major sources of the studied pollutants and CO₂ nearby." 

l.487-489: Even though the results of this study show that CO₂ EF-calculation is a good method to observe the direct, and indirect, effects of road traffic, the mentioned uncertainty related to other contributing pollution sources should generally be better acknowledged."

l.491/492: "...based on the episodic data, one could misinterpret the data to conclude road traffic as a clear source of sulfate."

l.539/540: "...the data measured during the pollution episodes showed that the method is also vulnerable to misinterpretations if background concentrations or effects of other sources cannot be recognized."

However, the mentioned limitations are not considered throughout the manuscript when interpreting results and there are many instances when the authors discuss their results without acknowledging these challenges, e.g.:

l.281/282: "Despite this challenge, strong connection between LDSA^al and CO₂ shows the clear contribution of road traffic on the metric." - The good averaged linear fit does not necessarily indicate that particles contributing to LDSA^al are mainly derived from road traffic.

l.415/416: "...whereas the concentrations of intermediate ions (3-7 nm, Tammet, 1995) and larger ions increase as a function of increased traffic."

l.430-432: "Overall, the analysis of the small ion concentrations as a function of CO₂ enables in-detail detection of the effects of road traffic as a sink for small ion concentration. By combining this analysis with size-resolved EF of particle number, the method could be potential for estimating the production and removal processes of ions in urban environments." - In my opinion, "enables in-detail detection of the effects of road traffic" is an overstatement.

l.441/442: "However, the results suggest that terpenoids could be more directly linked to road traffic than previously considered." - I don't see any evidence for this statement.

l.445/446: "As limonene is found in many cleanser products, the correlation with the CO₂ and road traffic could potentially be related to the number of recently washed vehicles on the street and the use of windshield washer fluid." - There are other, probably simpler explanations. For example, with wood combustion as a potential source, both terpenoids and CO₂ would be co-emitted.

l.446-449: "As the contribution of natural sources in this study should be minimal, it is likely that road traffic contributes directly also to the other terpenoids. Hence, the results indicate that road traffic could have previously unconsidered direct effects on terpenoid concentrations in urban environments." - I don't see evidence that road traffic "likely" contributes directly to emissions of terpenoids. Also, road traffic effects on terpenoid concentrations have been considered in previous studies (e.g. Borbon et al. 2023, JGR 128, e2022JD037566. https://doi.org/10.1029/2022JD037566).

l.525: "For example, it was found that in cases of high CO₂ concentration, i.e. high traffic volume, NO2 concentration remained constant regardless of increasing CO₂ and the increase of NOx was almost completely contributed by NO. This phenomenon was linked to near-zero O₃ concentration which caused that NO was no further oxidized to NO₂. The approach could, hence, be useful when estimating NO/NO₂ concentrations in urban environments." - Again, in the first sentence, high CO₂ concentrations are equated with high traffic volume. However, elevated CO₂ concentrations might be observed in shallow boundary layers, for example at nighttime, when traffic volume is typically lower than during daytime. The observed phenomenon is consistent with the well-established diurnal cycle of nighttime ozone titration and daytime photochemical formation but I don't see an advantage in calculating the CO₂-based EFs to study the interactions between NO, NO₂ and O₃.

l.530-532: "Even though terpenoid VOC concentrations have been earlier connected with human activity, the results indicate that road traffic could also have direct effects on these compounds, which is not generally well understood." - In my opinion, the presented data support several previous studies but it is not really additional evidence for direct road traffic emission of these compounds. For example, wood combustion would co-emit terpenoid VOCs and CO₂ as well.

4) The concept of the so-called impact factor (IF) used for assessing indirect effects of road traffic on air quality is somewhat confusing. While the authors acknowledge that the concept of LDSA^al EF is tricky (l.278), it becomes even more difficult when looking at ozone IF. Clearly, a change in O₃ mixing ratios is not dependent only on the kg of burned fuel but also on solar radiation and on mixing ratios of NO, NO₂ and VOCs. In that sense, the IF indicates the relationship between ozone and CO₂ (as a proxy for road traffic) while averaging all other influencing factors. This should be clearly stated. Also, the authors should carefully revise the manuscript to change instances when they refer to EFs for ozone (e.g. l.86/87, l.91/92).

Regarding the statements "In addition to direct EFs, we show that CO₂-based EF determination enables detection of inverse and indirect effects of road traffic" (l.24/25) and "Also, the findings related to the terpenoid VOCs, together with the observed inverse IFs on O₃ and small ions, show that the CO₂-based EF calculation is an effective approach to investigate not only the direct emissions but also the indirect and unconventional effect of road traffic on urban air" (l.534-537), the authors must clearly show and better explain what the advantage of the CO₂-based EF/IF calculation is. What are the main advantages of this particular approach?

5) In the beginning of section 2.3 in l.150-152, the statement that the "EF for each pollutant metric was calculated [...] with a time resolution of 1 min" is misleading. Later in l.173, it is explained that in "case of the DMPS, NAIS, SP-AMS, and VOC sampling, the measurement intervals were longer than 1 min". It is important to keep in mind different averaging intervals when interpreting results throughout the manuscript. Indeed, the time resolution defines whether or not dynamic emission processes can be resolved, and especially in urban environments, high time resolution is required. For example, Lamprecht et al. (2025; Atmos. Meas. Tech., 18, 5003–5016, 2025, https://doi.org/10.5194/amt-18-5003-2025) show that normalized enhancement ratios based on excess mixing ratios of NOx and CO₂ can strongly differ for different averaging intervals.  

6) When comparing the calculated PN EF of approximately 2.1E14 #/km and the EU EURO standards for primary particle emissions (> 23 nm) of 6.0E11 #/km, the discrepancy is briefly explained as "likely related to the emissions of (semi-)volatile compounds" (l.227). I recommend to clarify that the EURO emission standards are defined for solid, non-volatile particles, while the ambient measurements include both volatile and non-volatile particles. In addition, the PN measurements in this study include particles > 5.4 nm. Only with a measurement setup separating volatile and non-volatile particles (e.g. using a thermodenuder), and covering the diameter range > 23 nm (e.g. from the DMPS data), a direct comparison would be reasonable.

7) When looking at the size-resolved PN EFs of the DMPS and NAIS instruments in Figure 2, I consider the "shapes of the EF size distributions determined from the DMPS and NAIS data seemed to agree well" (l.235/236) an overstatement. Also, why is the observed difference for particles < 30 nm expected to be due to the "different scanning times of the measurements" in particular (l.238)?

8) In l.500-503, the authors state: "In this study, the non-episodic EFs and IFs identified can be considered to accurately represent the effects of wintertime road traffic in Helsinki central area, as the regional pollution levels during the non-episodic periods were low and the linkages of studied pollutants were strong with CO₂." - I agree that non-episodic periods were selected when regional pollution levels were low but as mentioned before, good correlation with CO₂ does not necessarily indicate road traffic as the dominant source. Obviously, the differences in magnitude of EFs derived during pollution periods and non-episodic periods suggest that factors other than road traffic can affect the results. Why should non-episodic periods be representative for road traffic only? 

9) In l.521/522, the authors state: "In addition to direct EFs, we showed that the CO₂-based EF-calculation is suitable when investigating inversely proportional impact factors (IF) related to road traffic." How exactly did the authors show the suitability? They further state in l.524/525 : "...the approach utilized can be fruitful in terms of air quality modelling and when estimating the formation and removal processes of atmospheric gases and ions." How exactly could this approach be utilized? Do the authors suggest to use the calculated IFs in model parameterizations? I doubt that the calculated IFs will be transferrable to other seasons and conditions or even other sites.

Additional minor comments:

In l. 59/60, the authors state that BTEX group VOCs (benzene, toluene, ethyl benzene, and xylenes) have been recognized as carcinogenic compounds. Indeed, benzene and ethylbenzene are classified as carcinogenic by the International Agency for Research on Cancer (IARC), while toluene and xylene are categorized in IARC Group 3: Not classifiable as to its carcinogenicity to humans.

In l. 105, regarding the dilution of pollutants at the measurement site, it would be interesting to add information about the orientation of the street, e.g. with respect to the main wind direction.

In Table 1 (l. 215), the EF values of NO and NO₂ indicate emission of 1.98 g NO and 2.41 g NO₂ per kg fuel, i.e. a total of 4.39 g for the sum of NO and NO₂, while the NOx EF indicates emission of 5.59 g NOx per kg fuel. Please discuss this discrepancy.

In l.224, for conversion of the EF values from units "per kg fuel to "per km", fuel consumption of 11.0 l/100 km is assumed. What is the reasoning for this particular estimate?

In l.261 it is stated that the "obtained PM10 EF was 2.81 times higher than the PM2.5 EF, suggesting contribution by non-exhaust emissions". Is the reasoning for this statement that non-exhaust emissions contribute mainly to the coarse fraction > 2.5 µm? Please clarify, and also give a reason why the diurnal pattern of PN EF is different from PM2.5/PM10 EF (Figure S2).

In l.277/278, it is stated that "LDSA^al is especially dependent on the ultrafine particles, which deposit efficiently in the lung alveoli, as well as on BC". Why is LDSA^al considered to be dependent on BC?

In l.323-325, I recommend to change "Organics had also a strong R² of the averaged linear fit (0.977), whereas other compounds, i.e., sulfate, ammonium, nitrate and chloride, had larger confidence intervals" to "R² of the averaged linear fit for organics was 0.977, whereas other compounds, i.e., sulfate, ammonium, nitrate and chloride, had R² values < 0.8".

When discussing R² values presented in Table 3, I recommend to point out the lower R² values of 1,3-diethylbenzene and acenaphthylene in l.350, and add that "most studied alkane hydrocarbons except for heptane and octane" correlated well with CO₂ in l.351. For 1,3-diethylbenzene, Fig. S3 in the supplementary material shows R² = 0.961, not 0.761. Which one is the right R² value?

In l.418/419 it is stated that "recombination could affect the inverse IFs of the small ions which could partially explain why the impact of CO₂ is more significant with the positive ions in Figure 4." Please explain your reasoning.

In l.424, regarding the emission of small ions derived from engine exhaust measurements, also automotive braking as a source of highly charged aerosol particles could be mentioned (e.g. Thomas et al., 2024, PNAS 121, e2313897121, https://doi.org/10.1073/pnas.2313897121).

Technical comments

l.50: Please change "indications that even majority of" to "indications that even the majority of".

l.101: Please change "The station located at" to "The station is located at".

l.109: Please change "Kuuluvainen et al., (2018) and Barreira et al., (2021)" to "Kuuluvainen et al. (2018) and Barreira et al. (2021)".

l.118: Please change "Teinilä et al., (2025)" to "Teinilä et al. (2025)"

l.188: I recommend to simplify the statement "some of the studied pollutant metrics had inverse trends as a function of increasing CO₂ concentration", for example, to "some of the studied pollutant concentrations decreased with increasing CO₂ concentration".

l.209: I suggest to change "The concentrations of PN, BC, PM10, PM2.5 and LDSA^al were strongly connected with the CO₂ concentration" to "Average concentrations of PN, BC, PM10, PM2.5 and LDSA^al were statistically related to the average CO₂ concentration".

l.251: Please change "and median and" to "and median".

l.369: Please change "Naphtalene" and "Acenaphtylene" to "Naphthalene" and "Acenaphthylene" in Table 3, in Figure S5 (supplementary material) and in Table S5 (supplementary material).

l.410: In Figure 4, is the mean diameter of the largest ion fraction shown in blue 38.5 nm as stated in the figure caption?

l.436: Instead of referring to Table S5, where also p-cymene shows poor correlation during pollution events, I recommend to refer to Table 4.

The authors present a study using observations in a street canyon in Helsinki, Finland, to determine emissions factors (EFs) of the wintertime vehicle fleet, using CO2 as a tracer for fuel consumption. EFs are reported for a number of particle and trace gas observations, as well as inorganic and organic components of PM and VOCs, including aromatic hydrocarbons, alkanes, and PAHs. Their findings show that older fleet vehicles are contributing significantly to the emissions, and exceed recent (2014) emissions standards. Further, they investigate the emissions impact on O3 (inverse), and introduce impact factor (IF) to describe the direct and inverse impacts of on-road emissions.

I agree with Anonymous Referee #1 that the topic is important and that it is within the scope of ACP, but I also agree that there is problematic terminology and oversimplification in both the approach to separating episodic and non-episodic data, and in the definition of IF which does not take into account all the other factors that would be contributing to ozone impacts beyond simple CO2 comparisons. The authors should address these limitations on their methodology and provide bounds for the general usefulness of IF applicability to other study regions.

Major comments:

There are several instances where the authors describe emission factors for ozone, which needs to be corrected as ozone is not emitted (e.g., lines 92, 378, Figure S6). By definition, an emission factor cannot be negative, so the terminology is problematic regarding negative EFs. Species may have an inverse relationship, but using EF is not correct. Even qualifying it as an inverse effect, i.e., negative EF (line 26), is not the right terminology.

The binary episodic/non-episodic seems problematic – assuming that there are other influences (e.g., long-range and regional biomass burning emissions, an inversion triggering a build-up of pollutants) that impact the canyon site significantly on occasion, one can only deduce that there is the potential for these impacts to contribute to the background levels during the non-episodic times. Thus, conclusions attributing findings during the non-episodic time periods to “on-road traffic” alone need to either (a) provide sufficient evidence that they are not influenced by other factors, or (b) quantify the possible extent of the other factors in the findings.

The resolution of several figures is too low, including Figures 3, S3, S4, S7. Some others are acceptable but not great, while others are very high resolution, i.e., S1 and S2. Recommend using whatever methodology was used for the latter for the remainder of the figures.

Technical Comments

Line 101 – The station “is/was” located… (and consider using present tense when describing the measurement site that is likely still there with the same features – for this whole paragraph.)

Line 101 and throughout – per the style guide, dates should be in [dd month yyyy] notation.

Line 102 – “similarly, coordinates need a degree sign and a space when naming the direction (e.g. 30° N, 25° E).”

Line 109 (and throughout) – the commas after “et al.” are unneeded when preceding a parenthetical date.

Lines 119-120 – The times need a qualifying “local time, LT” or otherwise.

Line 158 (and throughout) – per the style guide, units should be written with negative exponents, not in the format J/(K mol), or km/h, etc.

Lines 186-187, 189, 194 (and throughout) – “The abbreviation "Sect." should be used when it appears in running text and should be followed by a number unless it comes at the beginning of a sentence.” Similarly, Fig. should be used for figures not at the beginning of sentences.

Line 196 – remove the space before “-based EF calculation.”

Line 206 – “Figs. 6 and S9” and “Figs. S3-S5”

Lines 224, 225, 251, 297, etc. – the abbreviation for litres should be a capital L

Lines 231 and 360 – “in downtown Toronto”.

Line 273 – likely better to say “diesel city buses” (as in line 305)

Line 295 – perhaps “road traffic is no longer a significant…”

Line 319 – “so-called super emitters”

Line 338 – “to the authors’ knowledge”

Line 367 – consider uniformly capitalizing the VOCs in Table 3 (i.e., o-Xylene, 3-Ethyltoluene, 2-Ethyl-p-xylene, etc.)

Line 391 – the x in NOx should be subscripted

Line 392 – the 2 in NO2 should be subscripted

Line 404 – radon should not be capitalized

Line 423 – add commas before and after “e.g.”: “before, e.g., Hirskko et al…”

Line 425 – “paradox: road traffic” (road should not be capitalized).

Line 515 – “In the case of PN…”

Tables S1, S2 and S4, S6, and also Tables 3 and 4 – I recommend not having the data in the table in italics for better readability.