The manuscript by Yin et al. describes measurements of atmospheric ions in Beijing. Notably, they quantify the concentrations of ions of specific composition through a rigorous calibration process. For select ions, a steady-state analysis is applied to show how the time series of these specific ions are well represented by known chemical and physical processes and that condensational loss represents the largest ion loss term. Ion composition is compared to the composition of neutral gases measured by a nitrate chemical ionization mass spectrometer (CIMS) and similar to past findings, it is found that there is generally good agreement in the types of organic molecules identified as ambient ions and as neutral gases albeit with different intensities. These measurements from an urban environment are also compared to measurements from the boreal forest with similarities and differences discussed.

In my opinion, the most important contribution of this manuscript is the push towards making quantitative measurements of the chemically resolved composition of ambient ions and in using these quantitative measurements to evaluate our understanding of ion sources and sinks. Quantifying specific ions is a challenging undertaking that few have pursued in recent years (specifically when using time-of-flight mass spectrometers). Although some would argue that the science to effort pay off of such measurements may be minor, I think that there are some important questions that could be addressed if such measurements became more routine. The other aspects of the manuscript (discussion of composition, comparison to other environments, etc.) are only superficially explored and require a more comprehensive analysis before they would provide general insight into atmospheric composition and chemistry. In short, I think this manuscript contributes a technical advancement to the field and thus may be more appropriate for a different journal or as a technical note. In my opinion, to be suitable for publication in a more general journal, more detailed analysis regarding composition is necessary and the scientific motivation and insights of the analysis need to be clearly established in the manuscript.

Major

1. Sect. 2.1: At least a basic overview of the measurements at the boreal forest site needs to be provided so that the reader can understand and correctly interpret the results presented. Given that the measurements have been previously published, it is not necessary to go into a lot of detail, but the basics should be provided so the manuscript stands on its own. These include the dates of the measurements, a brief description of the inlet, how (if?) the transmission efficiency was determined, and any extenuating/unusual circumstances that would influence the measurements and the conclusions drawn here.
2. Sect 2.1: The dates of the measurements are unclear to me. On line 123, it is stated that the study ran from Jan 14^th to Sept 16^th, 2018, while on line 126 it states that the API measurements are from Feb 14^th to Feb 27^th, 2018. Were API measurements only made over this ~2 week period? If so, that needs to be clarified throughout the text. Were the nitrate CIMS measurements made concurrently with the API measurements or are they from a different time period? If a different time period, when exactly was that period and how would that influence the comparison between the API and the CIMS? As it reads now, the manuscript implies the measurements are simultaneous. Further information regarding the nitrate CIMS inlet, sampling protocol, and calibration frequency also need to be given so the reader can judge the likelihood of potential artefacts etc.
3. Sect. 2.1: Please provide more details on the inlet for the NAIS and how the calibration was performed. These details, particularly regarding calibration and inlet co-location/design, are critical for evaluating the API quantification.
4. Sect. 3.2: While this section provides description of the measurements, the scientific motivation of the analysis as well as how the results can be used to further broaden our understanding of atmospheric composition/chemistry are unclear to me. The comparison between Beijing and Hyytiälä is rather superficial, just presenting averages. There is no discussion on how seasonality, day-night differences, transport, etc. would influence the results and the comparisons. The finding that the two locations differ in composition is unsurprising and doesn’t provide new insights at the given level of analysis. I suggest either removing this analysis or significantly expanding it to consider aspects such as how the possible HOM precursors differ and what that implies about HOM molecules that are often important for aerosol growth. Further specific minor comments about this section are listed below.
   1. Lines 330-331: I don’t see how this implies that ion-induced nucleation is stronger under clean conditions. Please provide further analysis supporting this statement.
   2. Lines 332-334: Is the nitrogen-containing organic ions referring to CHONNO₃^-? If so, I don’t understand the point about a higher fraction in Beijing given that Figure 4a shows 27% for Beijing haze while the Hyytiälä pie chart shoes 31% suggesting a larger fraction in Hyytiälä. Moreover, from the pie charts in Fig. 4b, there also appears to be more CHON in Hyytiälä than in the Beijing haze.
   3. Line 340: In (Bianchi et al., 2017) which are measurements also from Hyytiälä, HOMs were observed as adducts with HSO4- as well. This should be discussed. This paper is referenced in line 343, however it should be moved earlier and in the context of relatively little adduct formation with HSO₄^- observed in the dataset used for the comparison here. Furthermore, in the Bianchi et al measurements it appears that ~25-50% of the signal for a given HOM ion was from the HOM HSO4- adduct during the daytime – I’m not sure I would consider this as being particularly low.
   4. Line 341-342: I am not entirely convinced by this argument since in Hyytiälä the H₂SO₄HSO₄^- peak is relatively more intense compared to HSO₄^- than it is in Beijing. Additionally, in Hyytiälä the HNO₃NO₃^- ion is more intense than the NO₃^- ion compared to Beijing. This seems to imply that further nuance needs to be considered such as relative binding strengths of HNO₃ NO₃^- vs HOM NO₃^- adducts (and likewise for HSO₄^- adducts).
   5. Figure 4: Was the Hyytiälä data corrected for the API transmission function? If not, these comparisons are not meaningful.
5. Sect. 3.3: Similar to Sect. 3.2, I find the analysis in this section too superficial to provide meaningful insights that will improve our understanding of atmospheric chemistry/composition. However, compared to Sect. 3.2, I think this section would require less work to add new insights. With the results presented as averages, overly broad generalizations are made an the text mostly focuses on reporting results rather than discussing the implications of those results. For instance, reporting the average charge fractions as a range of 4 orders of magnitude (line 381) does not provide meaningful information given the significant diel pattern of H₂SO₄ and the resulting impacts of charge competition. It would be interesting to know what is influencing such a range. For instance, it would seem reasonable that perhaps HOMs present primarily at night (i.e. formed from NO₃ radical chemistry) might have higher charged fraction because of less charge competition with H₂SO₄. Is there a diel dependence evident in this charged fraction? Similarly, one might expect a day vs night dependence to perhaps influence the NO₃^- vs HSO₄^- charging (line 385). Delving a little more into the details controlling these wide ranges would allow the reader to gain more generalized insight into the chemistry and would be more helpful in analysis of future datasets. Such an analysis need not focus on all the ions – targeting the a select few (i.e. most intense HOMs) would be appropriate. This section would also benefit from clearly articulating the major scientific conclusions the reader should learn. For instance, is there something to be learned about specific conditions where API is capable of providing insight into diel variations of neutral HOMs versus when it cannot?   Further specific minor comments about this section are listed below.
   1. Lines 377-379: What is meant by “neutral molecules detected by the CI-API-LTOF containing the same formula of CHO and CHON are treated as their corresponding precursors”? Does that mean the CHO^- and CHON^- ions were used or is it the formulas after subtracting NO₃^- as the reagent ion? The latter seems more appropriate to me.
   2. Figure 5: Please explain the histograms in panel b in greater detail. Why are the histograms different intensities overall? Are these total formulas detected? The N atom distribution is not shown in Fig. S6.
   3. Figure 6: How was HNO₃ measured? The fact that the measurements are in a different season should be discussed in the text along with how that could influence the interpretation.
   4. Figure S11: If all the sulfuric acid clusters were included, would there be a better correlation with neutral sulfuric acid?

Other minor comments

6. In several locations of the manuscript, I think that the wording unnecessarily oversells the impact/implications of the manuscript. In my opinion, this detracts from the work and may make the reader less inclined to appreciate the advancements that the work does make. Examples of this include line 92 and 457. The introduction does not justify why it is particularly urgent to quantify specific ions nor does the manuscript address how these will ultimately aid in human health, air quality, and global climate. These should be removed or should be better justified.
7. Lines 184-190: Since there is overlap in the region where the densities of 1.3 and 1.1 g/cm³ transition and since at higher masses, the densities appear to go back down to 1.1 g/cm³, why not use both 1.1 and 1.3 g/cm³ to develop a range of possibilities and generate something like a range of values (error bars). This would avoid the sudden, non-physical, stepwise transition and it would avoid implying precision in the answer that isn’t there. It would be a better reflection of our current state of understanding.
8. Line 205: How were the sampling losses in the API determined? This is necessary for others wishing to implement this type of analysis in the future.
9. Lines 222-232: Please include the time resolution required for the stated detection limits. I think it would also be more meaningful to provide the range of the API detection limit  (given the m/z dependent transmission) rather than focusing just on the minimum. The range would be more comparable to the range given for the NAIS.
10. Figure 1: What is causing the dip in the data from m/z 200-300? How does the relatively poor fit in that range affect the interpretation?

Technical

1. Line 48: The Lee et al 2004 reference is for indoor air quality and uses artificially generated ions. This is very different from what is implied by the current sentence structure and I recommend removing the reference or clarifying what the study actually shows.
2. Lines 87-88: I recommend citing some of the seminal work by Arnold et al as well. For instance (but not limited to), Arnold et al., 1982, 1978.
3. Lines 87-88 & 89-90: I recommend starting these lines of references with “e.g.” to indicate that these are non-exhaustive.
4. The data availability statement is not aligned with the journal standards https://www.atmospheric-chemistry-and-physics.net/policies/data_policy.html.
5. Figure S2: I recommend moving the API labels (red text) to the right y-axis to improve readability.
6. Line 253: I would tend to call these mass balance equations. I also recommend specifying that you are assuming steady-state in deriving equations 6 and 7.
7. Lines 319-321: Why not compare the detection of organosulfur molecules with the nitrate CIMS in Beijing rather than citing other measurements that are from significantly different atmospheric conditions?
8. Line 324: Please include in the text, not just the figure legend, how haze periods are identified.
9. Line 328: The C₁₀H₁₆NO₁₁NO₃^- formula would correspond to an open shelled neutral assuming NO₃^- as the charging ion. Is there a typo here and in Figure 4?
10. Line 354-355: As the (HNO₃)_xNO₃^- ions are formed as part of the reagent ion generation, I don’t think it is appropriate to include them in this list.
11. Lines 398-400: This point about the phenol related ions should be made at the beginning of the discussion so the reader understands the parameters of the analysis.
12. Line 415: What specifically is meant by “total ion clusters”? Please clarify.

References

Arnold, F., Böhringer, H., and Henschen, G.: Composition measurements of stratospheric positive ions, Geophys. Res. Lett., 5, 653–656, https://doi.org/10.1029/GL005i008p00653, 1978.

Arnold, F., Viggiano, A. A., and Schlager, H.: Implications for trace gases and aerosols of large negative ion clusters in the stratosphere, Nature, 297, 371–376, https://doi.org/10.1038/297371a0, 1982.

Bianchi, F., Garmash, O., He, X., Yan, C., Iyer, S., Rosendahl, I., Xu, Z., Rissanen, M. P., Riva, M., Taipale, R., Sarnela, N., Petäjä, T., Worsnop, D. R., Kulmala, M., Ehn, M., and Junninen, H.: The role of highly oxygenated molecules (HOMs) in determining the composition of ambient ions in the boreal forest, Atmos Chem Phys, 17, 13819–13831, https://doi.org/10.5194/acp-17-13819-2017, 2017.

Yin et al. report measurements of negative atmospheric ions in Beijing. They used an improved calibration technique by comparing the API-TOF signal with NAIS. Concentration and composition of atmospheric ions in Beijing are reported and are further compared with those measured in a boreal forest environment. Sources and sinks of ions are discussed and the concentrations of select ions are simulated, the results of which agree well with measurements. I find the results presented in this work interesting and the manuscript can be accepted after the following comments are addressed.

Major:

1. Is it possible to relate the sampling efficiency to more fundamental parameters, e.g., sampling tube length and flowrates? The current method requires that one has to have a well-calibrated NAIS to calibrate an API-TOF, which is demanding on available instruments for a lot of observation sites.
2. It is not clear to me why only negative ions are discussed, which makes the story not complete. Are there problems with positive ions measurements?
3. It is stated that organic ions with the HSO₄^- adduct is one of the most abundant organic ions, doesn’t this imply that HSO₄^- clustering with organics should be included in the kinetic model for HSO₄^-? From Fig. 4a it seems that this sink should be comparable to the H₂SO₄ + HSO₄^-
4. The concentration of ions is determined by the balance between the source and sink terms. Is there any available information on the comparison between ion production rates between Hyytiälä and Beijing?
5. Line 129: how were the voltages adjusted to minimize fragments? Which ion fragmentation is minimized? Please add sentences to provide these details since ion fragmentation is quite important for the current study.

Minor comments:

1. Line 23, ‘We demonstrate the feasibility of quantifying cluster ion compositions with simultaneous in-situ measurements by a neutral cluster and air ion spectrometer.’ I find this sentence hard to understand, why is ion composition measurement dependent on neutral cluster spectrometer?
2. Line 332: This sentence is misleading since nitrogen containing organic ions do not seem to be in higher fractions in Beijing.
3. Line 430: The reaction between H₂SO₄ and HSO₄^- does not transform ions back to neutral molecules.
4. Line 412: I’m not really sure if this the NO₃^- has ‘opposite’ diurnal variations from CS. If the author wants to make this statement, please show their correlation quantitatively.

Technical corrections:

Line 257: typo, should be n+

Line 319: I would replace ‘distinguished’ by ‘misidentified’.