Review for:

Stalagmite carbon isotopes suggest deglacial increase in soil respiration in Western Europe driven by temperature change

This paper presents a useful modeling approach for reconstructing soil respiration using stalagmite carbon isotopes and proxy constraints on prior calcite precipitation and bedrock dissolution effects. Carbon isotopes have been a particularly messy avenue in speleothem science due to the complex interplay of these effects (and others) and the paper represents an exciting effort toward rigorously disentangling this mess. The model is an important step toward understanding how soil respiration changes with climate and, given the breadth of data available in the SISAL database, could be quickly applied on a large scale (assuming it can be appropriately constrained). But the modeling approach carries some critical (and likely invalid) assumptions that need to be addressed. This paper can be of sufficient interest for Climate of the Past and I think my points can be addressed with major revisions. I commend the authors for their coupled proxy-model approach and hope my feedback is useful as they refine their work.

My expertise most closely aligns with the modeling work, so I focus my feedback on this part of the manuscript. I can’t speak much to the analytical methods. Below, I’ve divided my feedback into points about the main modeling approach (outlining my own confusion) and line-by-line items. My biggest concerns are that the modern calibration of the soil respired end member seems invalid (or at least should use modern CO2 levels), and that it is not a safe assumption that the mixing end members are time-invariant.

Main modeling points

My understanding of the modeling approach involves three steps: (1) use modern data to derive a relationship between atmospheric CO2 and soil-respired end members; (2) assuming this mixing relationship holds through time prescribe the full range of soil CO2 and d13C possibilities to solve for proxy data with CaveCalc; (3) using the model output, select and analyze the combination of input parameters that yield results closely in line with the measured data. Below, I dive into my concerns on steps 1 and 2 in more detail and include one note on step 3.

Step 1: calibrating a soil respiration end member

This calibration exercise (outlined in Figure 2) carries four big assumptions that I think need to be addressed. The biggest has to do with using modern data to calibrate a pre-industrial mixing curve (see point 2).

1. First, cave-monitored CO2 and d13C are used to calibrate a soil CO2 mixing line. This assumes that the mixing of atmosphere and respired CO2 in the cave falls the exact functional form of mixing in the soil (put otherwise, it assumes that the bedrock contribution to cave carbon is the same as soil carbon and that there are no other carbon fluxes distinguishing cave from soil). The authors concede this does not hold true in the winter, but could more be said about this assumption in the months of April-November (when (I think) the monitoring data are used)? Could changes in hydrology, or cave vs soil temperatures, or other things violate this assumption? Is soil CO2 assumed to reflect the soil-column integrated conditions? Is it a problem that this assumption breaks down seasonally if calcite deposition is seasonally biased? I think, at the least, it must be written that this assumption is made (right now the link between cave conditions and soil conditions is a bit vague to me).
2. Second, the model is calibrated to pre-industrial CO2 levels even though the data are taken in modern conditions (when CO2 is very well-constrained and much higher!) I think this is done so the same calibration end members can be applied throughout the Holocene (more on this in the “Step 2” section). The forest data are ignored because they might be influenced by “turbulence and advection effects” (Line 196), but they would probably fit really nicely on a mixing line that reaches to a modern CO2 end member (with higher CO2)! In fact, all of the data would likely fit better on such a line (given that the monitoring data residuals to mixing line 1 are mostly above the line when CO2 > 1,000 ppm). This makes sense, because the monitored data are mixing with the modern atmosphere, not the pre-industrial atmosphere. (Correcting for the Suess effect only corrects for pre-industrial d13C, it does not account for the difference in CO2 between then and now). I highly encourage the authors to use a calibration to a modern end member. Otherwise a much more rigorous justification for the pre-industrial end member is needed.
3. Third, I don’t know how the soil-respired end member is defined as 7800ppm and -22.9‰. I imagine that it’s an extrapolation of mixing line 1, but why not extrapolate some number other than 7800? Is there some assumption that I’m missing?
4. Fourth, I think this modeling approach assumes that boundary layer CO2 concentration and d13C (the stuff that diffuses into the soil) also falls on the same mixing curve. This should be stated since at least two things relevant to this study might violate this assumption. First, a shift from no canopy in the last glacial to a canopy when forests appear might lead to a “canopy effect” whereby d13C gets lower than expected for a given pCO2 due to recycling. Second, “turbulence and advection effects” (line 196) that appear to matter during the daytime (probably when photosynthesis is happening) can overprint the simple mixing relationship and propagate down to the soil respired end member. These effects might well be small, but I think the assumption should at least be recognized. 

Step 2: assuming this holds through time

This analysis assumes that the mixing slope between soil respired d13C and atmospheric d13C is constant through time. This is not a good assumption because a lot of factors that matter on decadal or longer timescales (i.e. factors that are not captured by the short calibration) violate it by changing end member CO2 but not d13C (or vice versa). For example, if CO2 increases (like it did from LG to EH), then the isotopic composition of CO2 must decrease to keep the end member on the curve, but we know very well that this assumption is violated on paleoclimate timescales (e.g. Schmitt et al., 2012; Science; Figure 1). Similarly, if soil respiration decreases (thus decreasing soil-respired CO2) then the d13C of soil respiration must increase to stay on the mixing curve. I’m not sure if there’s a defensible mechanism for this, although it might occur by coincidence if water stress increases vegetation d13C (thus soil-respired d13C) while decreasing soil respiration. Either way, I am not aware of any mechanistic reason why the end members of the mixing relationship should, themselves, vary along a mixing curve. The end-members, just like the average soil CO2 values that reflect their mixing, should vary over time.

I think the modeling can still be performed if some significant changes are made (these are just suggestions and other options can be valid too!).

1. Consider using the actual paleoclimate constraints on pCO2 and d13C of CO2 to parameterize the atmospheric end member.
2. Instead of calibrating the soil-respired end member with modern data, be clear that constraints on this term are not great but define reasonable ranges and run sensitivity tests. Allow the soil respired d13C and CO2 to vary with time. Or consider forcing the model with different scenarios as a sensitivity test (i.e. low vegetation d13C, high vegetation d13C and variable, or decreasing, or increasing d13C). Given the strong evidence for substantial changes in vegetation, it is helpful (maybe necessary) to rule this out as the main factor affecting d13C_spel. Consider holding soil respiration constant while letting d13C-respired vary; one might find that the variability would have to be too high to be explained by changes in C3 vegetation or water stress alone (see Kohn, 2010; PNAS).

Step 3: filtering for best model results

More discussion / sensitivity analysis should be done here. Were other options for finding the “best fit” considered? How does changing the thresholds for carbon and calcium isotope data affect the results? What happens if one uses a broader DCF threshold? If these decisions affect the results (or if they don't) it would be important to know.

Smaller comments and line-by-line

• Please clarify the use of “soil carbon” vs “soil-respired carbon”. For example, line 199 states “The regression points toward a soil carbon end member…”. Is this treated as just “soil carbon” in the modeling? Because the exercise seems to imply that the constraint is a “soil-respired carbon” end member. Line 190 also refers to the “soil carbon end member” but states it was constrained with data, not the modeled regression (which I think is accurate). Since soil respired carbon is defined as a component of soil carbon (line 182) this distinction is super important. It’s still not fully clear to me how soil carbon vs soil respired carbon are treated in the model.
• I imagine that the soil respired end member of the mixing curve changes seasonally. If calcite formation is seasonally biased, could this affect the results? For example, are more model solutions at higher soil CO2 conditions possible when strictly summer-time inputs are used?

Line 36: Check out Bova et al., 2021 (Nature) for updated Holocene climate constraints.

Line 49: I’m not convinced by Figure 1 that these records are “highly consistent in timing, amplitude, and absolute d13C”. I worry that the words “highly consistent” are overstating the data. Consider focusing on the main trends that are clearly robust, like the general shift to lower d13C values from 18ka to 6ka.

Figure 1B: Consider labeling the El Pindal and La Vallina sites.

Figure 1C: Is the straight blue line from ~18ka to 15ka just due to the fact that there are no data? It might be clearer to disconnect the timeseries lines whenever there is a sufficiently long duration of no data (maybe wherever there is ~500 years of no data or something).

Line 129: I don’t know if CP allows citing papers in review, just adding it here as a note (although I assume that the authors have already confirmed that this reference is okay!)

Line 169: Is this really deriving the soil carbon “…response to temperature change”? I think the link to temperature change is solely based on interpretation, not model derivation.  

Line 184: Not a paper strictly on soil CO2, but Slessarev et al., 2016 (Nature) might be useful here for linking parameters of the soil carbonate system to the water balance.

Line 194: “…by linear regression of the summer cave monitoring data”. I assume these are the large-diamond points in Figure 2. But looking at figure 2 I assume that the regression data are spring, summer, and fall (since monitoring is said to be monthly and there is no indication that spring/fall data are removed). Which data are actually used in the regression?

Line 196: While I suspect the offset of the forest data may actually be due to mixing with modern pCO2 (not pre-industrial levels), if the authors wish to keep this turbulence/advection effect argument I think it is important that a reasonable hypothesis for the signature of the third, unaccounted for air mass is added. Based on atmos circulation and likely boundary layer d13C in upstream ecosystems, is this mixing trend reasonable?

Line 201: “… but they provide the best available constraints on the end-member”. Wouldn’t directly measuring soil CO2 provide a better constraint? (Although, as stated above, I disagree with using a modern calibration to get a Holocene end member)

Line 217: Why was each simulation for each timeslice repeated twice? Were they varied from one simulation to the other? (Table 1 only gives single values for each timeslice)

Line 221-226: I’m a bit confused. Is there one set of binary filtering for the three mixing line simulations, and a different filtering approach (just selecting the best 5%) for the sensitivity tests?

Figure 4: Are measurement uncertainties considered in these regressions?

Line 293-294: I don’t think that encouraging model results is confirmation that “the estimate of the soil respired end member composition is accurate”. More sensitivity tests are needed to demonstrate that other soil respiration end member compositions lead to problematic results (particularly when the end members are allowed to vary with time, as discussed above).

Line 309-311: This is another instance where I’m tripped up by terminology. I think “initial soil gas” is the same as “soil respired CO2” and not the same as just “soil gas” or “soil CO2”?

Line 310-311: I would like to know more about this. Why does the sensitivity test require such an enriched d13C end member? How is the use of this end member justified over the use of the “calibrated” one? Is it a problem that the -22 per mille value does not yield many positive results?

Line 328: What is meant by “depth” here? I don’t think the Pataki paper actually measures anything over soil depth.

Line 347: This is probably just my own problem, but I’m confused with terminology again. I thought initial soil gas might be the initial CO2 from soil respiration, but this sentence implies initial soil gas and soil respired CO2 are two distinct things.

Line 433: “…best explained by..” my version of the document just says “c.”

References

Bova, Samantha, et al. "Seasonal origin of the thermal maxima at the Holocene and the last interglacial." Nature. 589.7843 (2021): 548-553.

Kohn, Matthew J. "Carbon isotope compositions of terrestrial C3 plants as indicators of (paleo) ecology and (paleo) climate." PNAS. 107.46 (2010): 19691-19695.

McDermott, Frank, et al. "A first evaluation of the spatial gradients in δ18O recorded by European Holocene speleothems." Global and Planetary Change. 79.3-4 (2011): 275-287.

Schmitt, Jochen, et al. "Carbon isotope constraints on the deglacial CO2 rise from ice cores." Science 336.6082 (2012): 711-714.

Slessarev, E. W., et al. "Water balance creates a threshold in soil pH at the global scale." Nature. 540.7634 (2016): 567-569.

Comment on cp-2021-3

Anonymous Referee #2

Referee comment on "Stalagmite carbon isotopes suggest deglacial increase in soil

respiration in Western Europe driven by temperature change" by Franziska A. Lechleitner

et al., Clim. Past Discuss., https://doi.org/10.5194/cp-2021-3-RC2, 2021

General comments

This manuscript combines multi-proxy analyses (δ13C, δ44Ca, paired U-Th and 14C ages) and geochemical modelling of vegetation-soil respiration within the soil-karst-cave system in the northern Iberian Peninsula over the last glacial-to-interglacial transition (ca. from 26 ka to 4 ka).

Authors have irrefutable knowledge on the subject and are familiar with the region, data and tools applied. They have performed comprehensive analytical work on three speleothems from two caves [Candela, El Pindal Cave (Moreno et al., 2010; Rudzka et al., 2011; Stoll et al., 2013; this study); Laura, El Pindal Cave (this study); Galia, La Vallina Cave (Stoll et al., 2013; this study)], including three pieces of the overlying bedrock.

The focus is on the δ13Cspeleo signal (Fohlmeister et al., 2020) to decipher whether it can be a possible paleo-soil respiration proxy (pCO2). CaveCalc (Owen et al., 2018) and ISTAL (Stoll et al., 2012) are used to account for effects of prior calcite precipitation (PCP), mean soil carbon age - dead carbon fraction (DCF), karst hydrology, bedrock dissolution, seepage zone and drip interval length changes. The referential temperature pattern is taken from Iberian Margin marine sediments (Darfeuil et al., 2016), the radiometric chrono-stratigraphy of which is sufficiently robust, and multiproxy studies have been performed on its strata.

Results point to increasing soil pCO2 over the last deglaciation (from late glacial ca. 530-1030 ppmv to ca. early interglacial 1155-5780 ppmv) heavily dependent on temperature (Q10 ~ 2.7-7; i.e., a factor by which soil respiration increases with a 10°C rise in temperature). This is in line with previously documented changes in vegetation cover and substrate from open glacial grassland, steppe taxa and low arboreal percentages to interglacial high arboreal pollen (data compilations in Fletcher et al., 2010 and Moreno et al., 2014; simulations in Scheff et al., 2017).  Authors present and discuss other possible processes which are not found to exert a huge impact on the δ13Cspeleo signal. Their results, interpretations and conclusions are justified by data and are consistent with previous monitoring data that showed seasonal variations in cave pCO2 driven by external temperature variations (Moreno et al., 2010; Stoll et al., 2012).

The science of the manuscript is excellent (significance and quality) and the overall presentation well structured. The organisation and length of the manuscript are good: 1 Table and 6 Figures in main text and 4 appropriate supplementary Figures (see below for specific comments). The title clearly reflects the contents of the paper and the abstract provides a concise and complete summary. The subject addresses relevant scientific questions within the scope of CP. My opinion is that it merits publication with minor changes once few clarifications are added. Please see below for constructive suggestions.

Specific comments and technical corrections

Tables

Suppl. Table 1, Suppl. Table 2

I was unable to find the 2 supplementary Tables mentioned in the text.

Figures

Current Figure 1 (Speleothem δ13C records covering the last deglaciation in temperate Western Europe)

- Remove lines when ‘hiatus’ or ‘no data’ in panels A, C

- Change “El Pindal (study site)” to “El Pindal & La Vallina (this study)” in legend of panel A

- Complete figure caption. Something like: “El Pindal Cave – stalagmite Candela (Moreno et al., 2010, this study), – stalagmite Laura (this study) and La Vallina Cave – stalagmite Galia (Stoll et al., 2013; this study).”

- δ13C Villars (Genty et al., 2006; Wainer et al., 2011) does not appear to be consistent with El Pindal ca. 19 ka. Issue with resolution of the former? Any comment?

-  δ13C Buraca Gloriosa (Denniston et al., 2018) appears opposite to El Pindal (Moreno et al., 2010) ca. 13 ka and around 19 ka. Dating issues? Other reasons?

- δ13C Cova da Arcoia (Railsback et al., 2011, PPP 305) is not included. It seems to have quite different absolute values during the time span Galia grows (ca. 9 ka). Any comment? Could this be relevant to the comparison with temperatures derived from the marine record located further south? Atlantic versus Mediterranean climatic zones? (see for instance Fig. 1 in Denniston et al., 2018)

- In this regard, what about adding d13C La Mine (Genty et al., 2006) as a contrasting environment?

This is important to highlight the “regional” extent of the exercise submitted in the present study.

Additional Figure (new Figure 1? Current numbers would change accordingly up to 7 Figures)

A non-specialist reader would very much appreciate being able to recognise all the variables measured and modelled under discussion. Thus, I earnestly request that authors include an illustrative scheme with the processes and reactions in question. As far as possible, the text must be self-explanatory: labelling the parameters as in the Figures, i.e. d13C, pCO2, specifying sources and including the notion of dead carbon (modern-to-fossil reservoir effect) so the reader can follow the reasoning step by step: (i) atmospheric CO2 and rainwater (highlight seasonal effects in temperature and rainfall density/amount); (ii) biogenic CO2 from vegetation-plant litter-microbial activity-soil respiration (emphasize role of moisture availability, vegetation type and cover in soil gas pCO2); (iii) infiltration through soil water to karst and water flow paths, bedrock dissolution, drip water, CO2 degassing-calcite precipitation to form the speleothem (link to cave air pCO2, cave ventilation dynamics, etc). Perhaps two panels are needed: one for a ‘summer’ scenario (assimilated to interglacial situation?) versus a ‘winter’ one (for the glacial conditions?). Ideally, this must lead the reader through the diverse situations deduced from the results, without digging too much in dispersed literature, which is somewhat scarce for d13C specifically (indeed this is a strong point of the present manuscript value). Consider adding the seasonality of the caves in question with the series of instrumental measures available for the area (see below for additional comments on that).

Figure 3

- Complete figure caption to highlight the paired U-Th and 14C ages shown at the bottom of the figure. Refer to the Suppl. Table 2 (if it exists?)

Figure 6

This figure seems too compacted. Try to uniform the criteria for all Figures, so the period of interest (from 26 ka to 4 ka?) and the relevant events of the study are clear.

Main text

References are made to the text by giving [line numbers: “text quotes”].

[Line 15 “underwent dramatic climatic and environmental change”]

Please remove “dramatic”. If qualifying the change is needed, any alternatives? “profound” is used for the Introduction, what about “significant” here?

[Lines 17-19 “global carbon cycle” … “on local soil respiration”] 

My recommendation is that neither the word “global” nor the point to “local” fit in here or at least may add confusion. The present work may have “regional” application (and unvaluable as such!)  for similar temperate environments of Western Europe when results are properly reproduced in subsequent studies.

[Lines 21, 73, 88, 92, 325, 336, 337, 349 … “Northern Spain”, “NW Spain”, “northern Spain”…]

Check for consistency and consider changing to geological terms such as “NW Iberian Peninsula”.

[Lines 34-35 “Between 22 and 10 ka BP (ka: thousands of years, BP: “before present”, with the present referring to 1950 CE),”

[Lines 103-104 “Minimum average temperatures are reconstructed for Heinrich event 1 (H1; 18-15 ka BP) and are ~8°C cooler than those of the Holocene Thermal Maximum (~8 ka BP; Darfeuil et al., 2016).”]

[Lines 246, 252, 256, 260, 298, 301, 333, 427 … “LGM (26.8 ka BP)” “the LGM (24 ka BP)” “(LGM, H1, and YD)” “during the LGM and YD” “~530-1030 ppmv during the LGM, and ~1155-5780 ppmv during the EH”]

[Line 316 “for the Early Holocene (EH, post 10 ka BP) and the Late Glacial (LG, pre 10 ka BP and including deglacial)”]

These excerpts use terms and chronostratigraphic units that must be clarified.

For instance, “last glacial maximum” (LGM) is used, though I am afraid I do not find the complete acronym meaning anywhere in the manuscript. In any case, both characterisation and timing of the LGM are complex enough for including the term here (see different approaches and stratigraphy ranging from ca. 33 ka to 26.5 or 23 ka to 19 ka, depending on literature e.g., Peltier & Fairbanks, 2006, QUAT. SCI. REV. 25; Clark et al., 2009, SCIENCE 325; Batchelor et al., 2019, NATURE COMM. 10; Gowan et al., 2021, NATURE COMM. 12; and references therein). Decoupling between temperatures and ice volume is specifically pronounced during deglaciations. Temperature estimations at the Iberian Margin suggest that the LGM was not a real stadial but a kind of weak interstadial. Although undoubtedly cold, it was not the coldest interval. The coldest intervals are observed during Heinrich events. Following the reference used in the manuscript (Lambeck et al., 2014), the main phase of deglaciation occurred from ca. 16.5 ka to 8.2 ka. My advice would be to delete any reference to “the LGM” and stick to two phases Late Glacial (LG) and Early Holocene (EH). Similarly, avoid the reference to a “Holocene Thermal Maximum”, which is an even more diffuse designation. The “Holocene temperature conundrum” debate will likely remain highly contentious over many years to come (Liu et al., 2014, PNAS 111; Bader et al., 2020, NATURE COMM. 11; Martin et al., 2020, QUAT. SCI. REV. 228; and references therein).

Additionally, the base of the Holocene must be placed ca. 11.7 ka, not 10 ka (Walker et al., 2009, J. QUAT. SCI. 24) and the EH spans from 11.7 ka to 8.2 ka (Greenlandian; Walker et al., 2019, J. QUAT. SCI. 34), though technically speaking the present study shows results up to 4 ka in Fig. 3, i.e. the Mid-Holocene (Northgrippian; Walker et al., 2019, J. QUAT. SCI. 34). This does not alter the results of the manuscript but respects the formal definition and dating established, in line with the useful INTIMATE event stratigraphy of Greenland interstadials and stadials (GI and GS, respectively; Lowe et al., 2008, QUAT. SCI. REV. 27; Rasmussen et al., 2014, QUAT. SCI. REV. 106; Mojtabavi et al., 2020, CP 16, 2359). For the LG events, please consider this nomenclature (i.e., use GS-1, not YD; and GS-2.1a, not H1), which implies showing a Greenland d18O profile in the Figures where these intervals are discussed. These are aspects of relevance to the subject because, the manuscript works on and paves the way to well dated speleothem material, with chronologies specifically reviewed within the SISAL database, version 2 (Comas-Bru et al., 2020a,b).

[Lines 96-99 “(AEMET meteorological stations at Santander and Oviedo, period 1973-2010; AEMET, 2020)” “(AEMET meteorological station at Santander, period 1987-2000; AEMET, 2020)”]

[Lines 469-470 “AEMET, 2020. State Meteorological Agency (AEMET) [WWW Document]. URL http://www.aemet.es/en/portada (accessed 470 10.8.20)”]

Not sure I understand the data source used here. Are the time intervals 1973-2010, 1987-2000 chosen for a particular reason? Is there a gap between 2010 and 2020? Can the series be shown for instance in the new Figure? Something that illustrates the seasonality in the region and explains more clearly the assumptions for the parameters involved in the present study (cave-monitored CO2, d13C, etc).

[Lines 98, 101-102, 106-107, 197-198, 407-409 “winter months (December-February)”, “summer months (June-September)” “estimate of the deglacial temperature change in caves on the coastal plain, as the region’s modern seasonal cycle displays similar amplitude to sea surface temperatures (Stoll et al., 2015).” “caves are well ventilated in the cold season with close to atmospheric pCO2 values, but feature elevated CO2 concentrations during the warm summer season (Stoll et al., 2012).” · “Cave monitoring data from winter months (December-March) were excluded from the regression analysis”; “Two model scenarios mimick full glacial and Holocene conditions, including changes in temperature, cave pCO2, and soil pCO2 for “winter” (i.e., atmospheric) and “summer” (i.e., elevated) cave pCO2 (Suppl. Fig. 4).”]]

Please correct “mimick” to ‘mimic’; or better still, change the word to “simulate”?

Seasonal changes, both in CO2 and temperature, appear crucial for interpretation of the results. Please clarify as much as possible throughout the manuscript. This would improve if illustrated with the new Figure. The reader would appreciate a clearly understandable and comprehensive discussion on that. For calibration purposes, I wonder if databases considering non global atmospheric CO2 values but continuous seasonal CO2 measurements from the ground-based network ICOS may be of some assistance here (Integrated Carbon Observation System, ICOS; Ramonet et al., 2020, Phil. Trans. R. Soc. B 375). Any comments?

[Lines 103-104, 343 “Heinrich event 1 (H1; 18-15 ka BP) and are ~8°C cooler than those of the Holocene Thermal Maximum (~8 ka BP; Darfeuil et al., 2016).” “Assuming a temperature change of roughly 8°C between the LGM and EH (Darfeuil et al., 2016)”]

Please clarify. It seems the 8ºC value accounts for the increase of temperatures between GS-2.1a (H1; ca. 18-15 ka) and the EH (before 8.2 ka). Other alternatives, i.e., from LGM to values after 8.2 ka seem closer to 6ºC, though perhaps I am missing something here. I understand the selection criteria of the site used as a reference for temperature (Iberian Margin site MD95-2042; Darfeuil et al., 2016) is based on its chrono-stratigraphy? I’d suggest authors also highlight the fact that multiproxy studies have been performed on its strata. In Darfeuil et al., 2016, two complementary paleo-thermometers are discussed, the TEX86 and Uk’37 (annual mean sea surface temperatures, a potential shift towards summer production that may occur for glacial times?). Authors refer to the former only and the profile is shown in Fig 3. Any comment here considering seasonality? Please include considerations of the analytical and calibration errors of the estimates. What about alternative documentation provided by pollen transfer functions?  Perhaps it would be preferable to have a sediment core further north, closer to the caves, though to my knowledge this is not available.

[Line 129 “Stoll et al., in review”].

If the paper is not publicly available at the time the present manuscript is published, I would suggest that the authors remove the reference in review and point to a different reference already peer-reviewed or add the information in this study.

[Lines 142.145 “Reimer, 2013”; “Reimer et al., 2013”]

It may be advisable to work on the updated calibration curves, i.e. IntCal20 and Marine20; Reimer et al., 2020, Radiocarbon, 62; Heaton et al., 2020a,b, Radiocarbon, 62. For Marine20, marine reservoir ages are modelled as time-varying, though for IntCal20, speleothem dead carbon fractions are approximately constant over time but with an unknown level. Any comment here?

[Line 360 “vegetation cove”]

Change to “vegetation cover”.

[Line 433 “δ13Cspel over the last deglaciation in Western Europe is best explained by c”]

Please complete the sentence.