This manuscript presents the GloSVeT dataset, a global 0.05° monthly soil and vegetation component temperature product derived using the FuSVeT framework (Liu et al., 2025). The study addresses an important gap in separating apparent LST into more physically meaningful components and provides a potentially valuable dataset for land–atmosphere interaction studies. Overall, this is an interesting study.

However, I have several major concerns regarding the physical definition of the retrieved variables, the consistency of the validation framework, and the interpretation of the results. In addition, some claims are overstated or insufficiently supported, and parts of the methodology lack transparency or justification. I recommend major revision before the manuscript can be considered for publication.

Major Comments

1. The physical definition of “soil temperature” is currently not sufficiently rigorous and may be misleading: The manuscript treats the land surface as a horizontally combined two-component radiative mixture of “soil” and “vegetation”, whereas in reality land surfaces are strongly three-dimensional, especially in forested or shaded canopies. The “soil temperature” here is essentially the radiative temperature of the visible background, not including the actual soil thermal state under canopy shading. In other words, this is not always a physically complete “soil temperature” in the ecological or hydrological sense. This conceptual limitation needs to be handled much more carefully throughout the paper, especially in the Introduction, Results, and Discussion.
2. Snow-covered conditions create a serious physical inconsistency in the definition of “soil temperature”: Related to the point above, under snow-covered conditions the retrieved “soil temperature” is effectively much closer to surface snow temperature than actual soil temperature. This issue is already visible in the high-latitude performance patterns and is indirectly acknowledged in the context, but it is not treated as a core limitation. The manuscript only masks permanent snow/ice based on MCD12C1 land cover, but does not account for dynamic seasonal snow cover during retrieval or evaluation. Why not involve snow fraction products to improve the product as this issue is already found in Liu et al. 2025.
3. There is a major inconsistency between the source observations and the validation framework: The FuSVeT/GloSVeT product is driven primarily by monthly MODIS LST observations, which are fundamentally clear-sky constrained. However, the ERA5-Land monthly diurnal cycle used in the model, as well as the flux-tower reference, are constructed by averaging all available instantaneous longwave-derived LST observations regardless of sky conditions. This mismatch is not trivial. It may be less severe for vegetation temperature, but for soil temperature with low heat capacity, which responds much more strongly to radiative forcing and sky conditions, this can introduce systematic inconsistency.
4. Lagged soil temperature–moisture analysis is not convincing: I do not find the lag interpretation in Figure 7 sufficiently credible, especially the implied 1–2 month delayed response of soil temperature to soil moisture in dry regions. In water-limited bare systems, the thermal response of the upper soil surface to changes in soil moisture is usually rapid. Possible lag may occur due to soil watter saturation, whihc may occur over days following rainfall, rather than over one to two months. The explanations currently provided are too speculative and are not well supported by either the figure itself or the cited literature.
5. Vegetation temperature–SIF correlations: The manuscript attributes positive correlations mainly to “reduced radiative or aerodynamic constraints”. I do not think this is the most convincing interpretation. This relationship is more naturally discussed in terms of photosynthetic thermal optimum and growing-season physiological activation, which vary strongly by vegetation type. At present, the manuscript mainly shows latitudinal correlation contrasts, but does not actually demonstrate the physiological mechanism it claims.
6. Figure 3: the claim that “GloSVeT performs best in tropical rainforest regions” is not clearly demonstrated as shown close to the equatorial belt at Figure 3d; More broadly, Figure 3 seems to show that ERA5-Land generally has higher correlation, especially for soil temperature, which weakens the central narrative of GloSVeT superiority. Why ERA-land is still compared considering it is used in soil temperature modeling. Why not use other reanalysis or soil temperature datasets mentioned in the introduction.
7. Figure 4: Some biome-level patterns are difficult to reconcile physically. For example, the very low or inconsistent correlations in Mediterranean and arid systems deserve much more scrutiny, although the soil temperature there should be easier to model.
8. Consistency test: A key missing analysis is to recombine the soil and vegetation temperatures back into a synthetic mixed surface temperature and compare that reconstructed LST against the original MODIS LST. This is a basic closure check for any decomposition framework. Without it, it is difficult to know how much error or structural bias is introduced during the separation process.
9. fixed soil emissivity assumption: The manuscript fixes broadband emissivity to 0.98 for vegetation and 0.95 for soil. This may be acceptable as a simplifying assumption in algorithm development, but for a global product covering deserts, bright soils, drylands, and diverse mineral backgrounds, it becomes a non-trivial source of uncertainty. This assumption deserves much more discussion.
10. The purpose and logic of the second “model calibration” step are not sufficiently clear.
11. Figure 7: The manuscript interprets negative correlations between soil temperature and moisture as expected evaporative cooling, which is reasonable in many regions. However, the broad areas of positive correlations across parts of West Asia, Central Asia, the Sahara, and northwestern China are not trivial and should not be casually explained away.

Other comments

1. Why does the dataset end at 2023 only?
2. In the abstract, I would write out FuSVeT in full rather than using only the acronym.
3. The abstract should clearly state how many flux tower sites were used in the evaluation.
4. In abstract, the sentence reporting warming rates for the two components is not sufficiently clear. It should be clarified whether the warming trends refer to global land mean values, or only to pixels where both soil and vegetation temperatures are simultaneously available.
5. “version 6.1” should be written as Collection 6.1 where MODIS products are referenced.
6. “one retrieved LST” is awkward wording. This should be revised to something like “a single retrieved apparent LST”.
7. The final part of the Introduction contains result-like wording (“these results demonstrate…”), which is not appropriate for an Introduction.
8. The Introduction would benefit from a more systematic overview of existing soil temperature products, related metadata, and accuracy, validation strategy, probably list them in the appendix.
9. MCD12: It is unclear how urban pixels are treated. Is it considered as soil? The physical definition may not be consistent again.
10. In the Methods, it would help to explicitly distinguish temperature-independent and temperature-dependent parameters more clearly when they are first introduced.
11. It is not clear whether the “detrended monthly anomalies” used in the TC analysis is deseasonalized?
12. The flux-tower validation section should include a site distribution map.
13. Figure 2 is not fully intuitive. In particular, the seasonal amplitude and magnitude range of vegetation temperature appear unexpectedly unchanged.
14. Why R in Figure 6c is weaker.
15. delete the space before the 2^nd affiliation.
16. The statement “neither reanalysis nor machine learning products can accurately characterize the spatial pattern of soil thermal conditions in the real world” is very strong and may need to be revised or add direct reference support.

The manuscript presents a potentially valuable global dataset of monthly soil and vegetation component temperatures derived from the FuSVeT framework, with broad spatial coverage and clear relevance for land–atmosphere studies. The study is promising and may make a useful contribution to the remote sensing community. At the same time, several important aspects would benefit from further clarification and strengthening, particularly with respect to methodological novelty, the physical interpretation of the retrieved variables, model applicability across different climatic regimes, parameterization assumptions, validation design, the independence assumption in triple collocation, and uncertainty analysis. Addressing these points would help improve the overall rigor of the study and enhance confidence in the conclusions. For these reasons, I believe the manuscript would benefit from major revision before further consideration:

1. The main retrieval method (FuSVeT) is adopted from a previously published study (Liu et al., 2025, RSE). In its current form, the manuscript appears to primarily extend the application of this existing approach to a longer temporal span, rather than introducing substantial methodological advancements. The authors shouldjustify the novelty and added value of the present study for the remote sensing community.
2. What is the physical definition of the monthly mean soil and vegetation temperatures? The MxD11C3 LST product is derived under clear-sky conditions, whereas ERA5 LST incorporates the effects of cloud cover. It is therefore unclear whether the retrieved component temperatures implicitly include cloud-related information. How are the effects of sunlit and shaded soil surfaces addressed? A simple averaging of clear-sky LST may inevitably mix sunlit and shaded signals, potentially introducing bias.
3. The GOT09 model is employed as the MDC model in this study. However, this model may not be applicable in polar regions, where polar day and night occur. It is unclear how the FuSVeT method is applied in regions above 66.5°N, as shown in Fig. 3. Do these regions exhibit the same monthly diurnal cycle characteristics as lower latitudes? Further clarification is needed.
4. The manuscript states that the number of iterations for Bayesian optimization is empirically set to 2000, but this choice lacks sufficient justification. Does the optimal number of iterations vary with land cover type? In addition, it would be helpful to quantify the computational cost and explain why this approach is preferred over simpler alternatives such as widely used Levenberg–Marquardt minimizationin DTC modeling. The description of “approximating the solution distribution” should also be clarified for better precision.
5. The emissivity in the MxD11C3 product is retrieved using a day/night algorithm, whereas in the FuSVeT method, soil and vegetation emissivities are fixed globally at 0.95 and 0.98 for the entire period (2003–2023). This assumption may not be sufficiently realistic. For example, in bare soil regions (e.g., the Sahara), where vegetation cover is negligible, the emissivity should be consistent with the MxD11C3 product rather than a fixed value. This issue should be revisited and better justified.
6. For in situ validation, sites classified as purely soil- or vegetation-covered based on NDVI are used as references. However, this approach raises concerns. The LST of a pure pixel essentially corresponds to the component temperature itself, meaning that the validation may effectively assess monthly mean LST rather than true component temperatures. In addition, the number of validation samples appears limited (e.g., only 66 points for soil temperature validation in summer during 2003–2023). The authors should justify the dataset used and consider incorporating dedicated LSCT validation sites (e.g., EVO, KAL, and DM).
7. The manuscript employs Triple Collocation (TC) to evaluate consistency among datasets; however, this method relies on the assumption of independent errors. In this study, ERA5 data are used both as input for retrieving soil and vegetation temperatures and as a reference dataset (e.g., ERA5 soil temperature), which may violate the independence assumption and introduce correlated errors. Please clarify how this issue is addressed. Furthermore, the use of subsurface ERA5-Land soil temperature (0–7 cm) may not be consistent with the penetration depth of thermal infrared signals. As noted by the authors, air temperature is also not an ideal proxy for vegetation temperature. These choices require further justification.
8. Reanalysis data are extensively used in the FuSVeT framework, along with MxD11C3 LST. The fusion of multiple datasets may lead to error accumulation; however, uncertainty propagation is not analyzed in the manuscript. Additionally, the reliability of using the MDC model independently should be assessed, as errors introduced during separate fitting may affect the results. For example, the reconstructed 24-hour monthly mean LST could be validated against geostationary LST data at the pixel level.
9. Figures 10–11 indicate that only a subset of pixels passes the statistical significance test (p < 0.05). The authors should report the proportion and spatial distribution of statistically significant pixels and discuss the robustness of their conclusions, given that a considerable fraction of the results may not be significant. Furthermore, the potential impact of non-significant regions on the overall interpretation should be addressed.

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