The study by Ylivinkka et al. presents a comprehensive analysis of particulate matter (PM) measurements from 2005 to 2020, employing three distinct methods to derive PM mass—an approach that adds significant value to the work. The authors transparently address the limitations of their methodologies, which is commendable and not often seen in similar studies.

The key finding—a declining trend in PM₁ mass at a high-latitude station with historically low PM levels—is noteworthy and merits publication. However, several issues should be clarified and revisions made before final acceptance.

Major Points

1. Size-Resolved PM Trends: Two of the three methods allow for the segregation of PM mass into PM₁–₂.₅ and PM₂.₅–₁₀. This valuable data could help determine which size fraction drives the observed decline and to what extent. Given that these methods generally agree, such an analysis would strengthen the study’s conclusions.
2. Annual vs. Seasonal Trends: While the authors discuss seasonal variations, they should also present total annual trends for a more complete picture. A summary table (similar to Table S1) with annual and seasonal trends—for at least one method, if not all three—is critically missing.
3. Introduction Focus: The introduction heavily emphasizes the role of PM components (organics, sulfate, nitrate) in influencing PM levels, which, while relevant, deviates from the manuscript’s focus on PM mass. Instead, I recommend including:

• A discussion of long-term PM trends from other locations.
• Key findings from prior studies at the same site (e.g., Laakso et al., 2003; Keskinen et al., 2020) that focus on PM.

Minor Points

• Comparative Analysis (Lines 378–386): The discussion should be expanded to compare SMEARII with other regional stations in Europe or elsewhere. Comparison against heavily polluted sites does not add value.
• Comparative Analysis of trends: What is critically missing is a comparison of the declining trends reported in this work, with those observed in other sites. A summary table (if feasible) would greatly enhance the study’s context.
• Language & Clarity: Grammar and vocabulary need refinement in several sections (e.g., Lines 48, 59, 70, 346).
• Misleading Statement (Lines 372–373): The claim that Figure S5 demonstrates evidence of long-range transported pollutants is misleading. While it shows air mass origin frequency, it does not establish a direct link to PM mass. Local sources could still dominate pollution levels, even if air masses originate from specific regions.
• Figure 4: Each subplot should be clearly labeled with its corresponding season for easier interpretation.

The manuscript provides a valuable 15-year dataset of PM10, PM2.5, and PM1 in southern Finland, with a comparative evaluation of gravimetric, SHARP, and DMPS-APS methods. The integration of multi-technique measurements with seasonal and episodic event analysis is it is an important scientific contribution. 

This is a solid and relevant study which presents novel comparative insights, and has high relevance for long-term air quality monitoring and that could be further improved by addressing these points:

- Uncertainties for each method should be quantified more explicitly, including potential biases when it is possible to quantify them (e.g., constant density assumption for DMPS+APS, semi-volatile losses in SHARP)

- The relative contribution of episodic events to annual loads and further chemical markers for natural sources (biogenic, combustion) would strengthen the interpretation.

Small corrections to the lines:

428: Possible typo: “warn” should be “warm”.

431: Perhaps “at the 95% confidence level” is more correct.

465: Unnecessary comma after “SHARP”.

470: “Reason why” or simply “cause” is better.

GENERAL COMMENTS

The study by I. Ylivinkka et al. analyzes three long-term (2005–2020) ground-based particulate matter (PM) datasets collected at a rural boreal forest site, with the aim of comparing the respective measurement techniques and evaluating temporal trends. This work builds upon the earlier preprint by Kersiken et al. (2020), which was submitted to Atmospheric Measurement Techniques Discussions. Compared to that manuscript, the current one attempts to improve the analysis of seasonal dependencies, to extend the dataset, and to strengthen the overall conclusions. The manuscript is generally clear and well written, and the research objectives are clearly stated. However, certain aspects of the study could be improved, further clarified, or made more robust before the manuscript is suitable for publication.

SPECIFIC COMMENTS

• Statistical significance vs. measurement uncertainty: While the identified trends may be statistically significant based on the calculations, it remains unclear whether the instrumental accuracy is sufficient to attribute these trends confidently to environmental changes rather than to potential instrumental drift. Hence, the measurement uncertainties (e.g., line 468) should be explicitly discussed to support the conclusion that the observed reduction in PM is attributable to a decline in emissions, rather than to instrumental artifacts.
• Introduction and motivation: The Introduction emphasizes the health effects of particulate matter and references the Ambient Air Quality Directive. However, the measurements are conducted at a remote background site located more than 50 km from the nearest urban areas where the majority of the population resides. While this context may be clear to the authors, the connection between public health concerns and observations at such a remote site requires further clarification. In this context, the comparison of PM10 concentrations at the SMEAR II site with those in a highly urbanized and polluted environment such as Beijing (lines 378–386) appears inappropriate and potentially misleading. I recommend removing this paragraph.
• Humidity control and sampling methodology: A more detailed discussion is needed regarding the methods used to control or reduce humidity in the sampled air across the different measurement techniques. For instance, in Section 2.2, are the filters used for gravimetric analysis conditioned after sampling? If so, under what temperature and humidity conditions? How might this conditioning influence the comparison with other techniques? Similarly, what humidity control mechanisms are implemented in the DMPS+APS system? Additionally, can the height of the inlet affect the comparability or representativeness of the measurements, especially in case of vertical gradients in aerosol properties?
• Density assumptions (lines 196 and 276): The assumption of constant particle density may not be strictly necessary, as particle density can vary with size and season (and composition, if analyzed). A discussion of how incorporating size-dependent or seasonally varying density values might affect the results would be valuable.
• Choice of diameter conversion approach (line 228 and Eq. 4): The decision to convert aerodynamic diameter to electrical mobility equivalent diameter (as done in Eq. 4) needs further justification. Why was this direction of conversion chosen, rather than the reverse? Given that the first two techniques report mass as a function of aerodynamic diameter, converting to mobility diameter may reduce the direct comparability between methods.
• Outlier filtering (lines 249–251): The use of the 6-MAD criterion to filter out data points should be further explained. How was this threshold determined? Are the excluded values considered to be erroneous measurements, or might they reflect real but localized events? Does excluding these points significantly improve the agreement between instruments?
• Role of size fraction dominance (line 294): The analysis could be further enhanced by exploring how the relative contribution of fine and coarse particles within PM10 influences the comparisons among instruments. Have the authors investigated whether the agreement between techniques depends on the dominance of one size fraction over the other?
• Discrepancies in 2011–2015 (lines 331–333): The observed divergence between DMPS+APS and impactor-based trends during 2011–2015 deserves a more detailed explanation. Can the authors elaborate on potential causes, such as instrumental drift, calibration issues, or changes in aerosol density or composition, that may have contributed to these differences?
• Literature review: Some parts of the manuscript, particularly lines 349–362, read more like a review of previous findings rather than a direct contribution to the current analysis. I suggest either removing or substantially condensing these sections. Alternatively, if context is needed, such content could be relocated to the Introduction or incorporated into a newly structured Discussion section, where previous studies could be more directly integrated into the interpretation of the present findings.

TECHNICAL REMARKS

• The title could be more specific. The measurements were conducted in a rural boreal forest environment, which may not be representative of all of "southern Finland".
• Abstract: The time period covered (2005–2020) should be explicitly stated at the beginning of the abstract (line 19) rather than at the end (line 28).
• Lines 24–25: Pearson's correlation coefficient alone does not adequately characterize the quality of a comparison. Two datasets can be highly correlated and yet exhibit considerable differences in slope or systematic offsets. Therefore, additional metrics, such as the slope and intercept of the regression line, root mean square error (RMSE), or bias, should be included already in the abstract to provide a more comprehensive evaluation of the agreement between datasets.
• Lines 27 and 31–32: Since the manuscript includes a statistical analysis of trends, the abstract should mention their statistical significance.
• Line 27: Alongside absolute variations, percentage (relative) variations should also be reported. This is especially important because mass concentration levels, and therefore their trends, can differ substantially across particle size classes. Expressing variations in both absolute and relative terms would enhance the interpretability of the findings.
• Line 43: The phrase "large uncertainty is related to aerosol particles" is unclear. Consider rephrasing.
• Line 63: The term "variant" does not sound appropriate in this context. Also, "long-range transported emissions" is an imprecise expression. Finally, aerosol lifetime in the atmosphere ("one week"?) is variable and depends on particle size, composition, and source region. Consider rephrasing the sentence entirely for clarity. 
• Lines 96–108: This paragraph contains general background information that may be redundant or too detailed for the Introduction. Consider omitting or significantly condensing it.
• Lines 110–118: There is some content overlap with lines 53–57. To avoid redundancy and maintain a concise Introduction, consider removing the repeated information.
• Section 2.5: Are black carbon concentrations monitored at the site? If so, it would be valuable to explain why BC data were not included in the current analysis, especially since BC could help distinguish between different aerosol types and sources.
• Lines 243–245: The description of the backtrajectory analysis could be improved. Please provide details such as the duration of the trajectories and the method used to define the three source sectors. This would allow readers to better understand the methodology without referring back to Räty et al. (2023).
• Lines 270–271: The statement might suggest that comparison is sufficient for validation. Comparison does not, by itself, constitute validation. Consider rephrasing.
• Figure 4 (caption): Please clarify the axis labeling by specifying that the tick marks refer to the x-axis.
• Lines 329–338: This paragraph discusses temporal trends and would be more appropriately placed in Section 3.3. Consider starting Section 3.2 at line 340, since the seasonal cycle is a more dominant feature.
• Line 345–346: Are pollen or other biological particles expected to peak during summer or in other seasons (e.g. spring or autumn)?
• Lines 371–373: The claim appears to be based on general patterns, but is it also supported by analyses of specific episodes or case studies?
• I recommend adding a dedicated Discussion section to the manuscript. This could include interpretive content currently located between lines 412 and 455.
• Line 433: Consider specifying "anthropogenic precursors" instead of just "precursors" for clarity.
• Figure S1: It would be helpful to include Pearson's correlation coefficient in Figure S1.