Reviewer 1

Verret et al. reports microbial organic matter degradation of a mid-Miocene age permafrost soil column from the McMurdo Dry Valleys (MDV), especially near the surface in the ‘dry permafrost’, which likely occurred during warm periods post-deposition. In addition, the lower ‘icy permafrost’ presents evidence of higher plants from a tundra ecosystem analogous to present-day southern Greenland. In order to study the degradation/preservation of organic matter, the author utilises bulk sediment TOC and δ¹³C, and biomarker distributions. A hierarchical clustering of this dataset highlights three distinct depth intervals that are attributed to increasingly lower levels of organic carbon degradation downcore. Moreover, the author uses two calibrations (i.e. MBT’5ME and BayMBT0) to acquire temperature reconstructions from brGDGTs. Both present a similar range of values and provide insight on the warming required to “unlock” the carbon stored in the permafrost for microbial activity.

Overall, this paper is articulately written with only a few incorrect spelling and/or grammar mistakes. The figures are also very clear and easy to interpret. The Introduction (section 1) and the Study Site (section 2) provide a succinct overview of the locality (i.e. MDV) and the rationale behind the research undertaken. It is nice to see a study that takes advantage of a multi-lipid approach, and not just the compounds most commonly applied (such as n-alkanes and fatty acids). The data also provides insight into high-latitude systems, which are considerably under-studied. The potential impact of carbon released from permafrost, as a response to future warming, is still a major gap in our knowledge, and fingerprinting the biogeochemistry of Antarctic soils would be a crucial step towards developing a better understanding.

Although written eloquently, I believe that the readers would benefit from the author providing geographical context in the introduction (see mostly minor comments for suggestions on improvements). In addition, please find suggestions for how the abstract (see Section 4) and results (see Section 3) could be developed slightly. Finally, there are a few interpretations that I find myself struggling to follow, and believe would benefit from more clarification (see Section 1). In particular, there are major questions pertaining to use of the term “degradation” that a slight reframing of the discussion may solve (see Section 2.1), and potential further exploration of hopanoids (see Section 2.2).

We thank Emily for her detailed insight and useful feedback on our manuscript. It is clear from the comments that she has read our manuscript diligently. We address her comments in the following sections.

Major comments:

1) Interpreting the changes in biomarker distribution

1.1 A new source of organic carbon post-Miocene?

The author suggests that the overall biomarker distribution support a tundra ecosystem that was established during the mid-Miocene (section 5.1). This includes greater values in the SOCd, BIT index, and abundance of high-molecular weight compounds, phytosterols, and phytol. Although the macrofossils further confirm a tundra ecosystem, how confident is the author that the deposits are only composed of mid-Miocene sediments? As described in section 2, the dating relies on magnetostratigraphy constrained by a tie point at much lower depths (tephra layer at 5.13-5.18 m). Is this at a resolution that provides robust ages for the 140 cm section studied? Although the Py-GCMS data provides evidence of plant material, could plants not have grown during warm intervals post-Miocene? Did a tundra ecosystem only exist during the Miocene or is the composition/species of macrofossils specific to the Miocene? If the latter, could the author cite some papers to support this? I ask for clarity on the age model as I wonder how the author ruled out the possibility that the distinct change in the biomarker distribution of unit 1 represent a different time interval with a shift in the depositional environment, and thus lithology. Especially considering the ¹⁴C analyses at ~10 cm yielded an age of ~42 kyrs (even in splits 4 and 5, that supposedly contain the “older material”; line 293), and the TOC is much higher in unit 1.

The age model is robust and is presented/summarized in Chorley at al., 2023 (FHDP-2A shown in Fig. 3b directly overlaps with/correlates to FHDP-2C). The ash date provides absolute constraints for the age at ~5.2 meters below the surface and the most parsimonious solution for the normal chronology above the ash is that it is C5AD (~14.6 to 14.2 Ma). We also note that independent cosmogenic surface exposure age dating (Valletta, R.D., Willenbring, J.K., Lewis, A.R., Ashworth, A.C., and Caffee, M., 2015, Extreme decay of meteoric beryllium-10 as a proxy for persistent aridity: Scientific Reports, v. 5, https://doi .org /10 .1038 /srep17813) indicates that the sediments at Friis Hills are older than 11 Ma (with adjusted/modelled age > than ~14 Ma). Our own cosmogenic study supports that insignificant water has infiltrated the site for 6 Ma (Verret et al., 2023). Biostratigraphic data also suggest a Miocene age for the sediments. The most parsimonious interpretation is that the sediments studied herein are older than 14 Ma and younger than 14.6 Ma (See Chorley et al., 2023, Fig. 11).  Furthermore, the analyzed sediments are from the upper part of sequence 13 from the Friis Hills composite presented in Chorley et al., 2023. This sequence was likely deposited during a single precession cycle between 14.36 and 14.38 Ma (see Fig. 11 Chorley et al., 2023) although we acknowledge that it may have been deposited during alternate precession cycles between ~14.4 and 14.2 Ma. The extinction of tundra in the Dry Valleys is discussed in other papers references in text (e.g. Lewis et al., 2008, Lewis and Ashworth, 2026) and the general consensus is that tundra disappeared from the high elevations of the Dry Valleys during the middle Miocene climate transition. The necessary paleoenvironmental succession at the site is described in lines 96-104 We believe that overall the age constraint is well-discussed in text, although it is not at the center of this paper and is referenced by other studies as well. The young radiocarbon ages represent a mixing signal and were expected to yield an age that includes both Miocene (radiocarbon dead) and “modern” (radiocarbon active).

We added a statement on line 140 to remind the reader of the statements detailed in lines 114-122.

1.2 Microbial organic matter degradation during deposition in the Miocene?

In addition to clarifying why the change in the biomarker distribution of unit 1 does not represent a change in source, and instead is a degradation signal, how did the author determine that microbial organic matter degradation was less severe in the underlying icy permafrost? Besides the abundance of plant-derived degradation products (e.g. pristine and phytane), most of the evidence in the dry permafrost is indicative of a contribution of bacteria-derived organic carbon (e.g. low C:N ratios, high δ 13Corg values, and high relative abundance of iso-FAs, LMW n-alkanes, and hopanoids). I think inferring microbial organic matter degradation from multi-lipid evidence of microbial activity is not a bad assumption, however does this equate to better preservation of lipids in the icy permafrost? (see Section 2.1 for further discussion and a potential solution). It seems unlikely that microbial organic matter degradation did not take place when the permafrost soil was accumulating during the Miocene. Especially considering that there is evidence of higher plants, which implies warmer and wetter conditions that would also favour microbial activity (Chorley et al., 2023). Therefore, is it more nuanced to state that the dry permafrost is influenced by a faster rate of microbial organic matter degradation compared to primary productivity?

As explained in our response to the previous question, we can robustly infer that the organic matter in unit 1 is of Miocene age, derived from plants living during a warmer climate, and can exclude any contributions due to the absence of plant vegetation in later periods. We agree that active microbial degradation would have also occurred during the mid-Miocene, as suggested by the reviewer. Our results even suggest that the differences between units 2 and 3 could represent another paleo-active layer. We know from previous studies that there was an active layer with liquid water incorporating the sections of the sediment core through the late Miocene (Verret et al., 2023). We therefore interpret that the signature found in this section of the core would reflect the most recent active layer, altering the original Miocene signature. Therefore, our explanation regarding higher degradation near the top and lower near the bottom is derived from the fact that there is a gradient of less plant-derived lipids and more bacteria-derived lipid near the surface. Hence, there is a depth-dependent degradation trend where unit 1>unit 2>unit 3.

As suggested by the reviewer, we added a nuance in text in line 537: “These findings imply that rates of microbial organic matter degradation dominated over primary production of organic matter at a point in time following the mid-Miocene climate transition, which could not be precisely dated. The original biomarker signatures would have been preserved throughout the sediment column if the upper part of the permafrost column had remained permanently frozen until present day, preventing extensive bacterial degradation. However, recognizing the increased degradation state of plant-derived organic matter and higher contributions from bacterial lipids in the shallower part of the record suggests overprint of the original lipid distribution during more recent periods when the active layer thawed to that depth.”

2) Gradient of organic carbon degradation that decreases downcore

2.1 Defining “degradation”

Another reason for questioning the statement that there is lower levels of organic carbon degradation downcore, is that, although the Py-GC-MS data presents degraded organic matter in the dry permafrost, there is no Py-GC-MS data from the icy permafrost to compare this to. Potentially, it is actually comparatively much lower in concentration. Moreover, the CPI suggests degradation downcore. Typically, thermally mature organic matter exhibits low CPI values (~1), and high CPI values (>3–30) indicates relatively unaltered organic matter (Diefendorf & Freimuth, 2017). The dry permafrost coincides with CPI values >3. I think the solution here would be to differentiate between microbial degradation and abiotic degradation that has occurred over long timescales to the Miocene deposits. Reframing the paper to fit these definitions would massively help the confusion caused by what comes across as contradictory statements throughout. For example, “Beyond the dry pemafrost, Corg is dominantly ancient and highly degraded” (line 444) and “Overall, the organic matter in the core appears to be compatible with a highly degraded signature of the mid-Miocene paleoenvironment” (line 455). This will improve what appears to be a lack of consistency between the abstract and conclusion (see more recommendations in Section 4).

As part of this recommendation, I would like to suggest that the author focuses on reframing the following section in the Introduction (section 1; line 53):

“Low-molecular weight organic compounds (e.g. sugars and amino acids) and lipids with double bonds or polar functional groups (e.g. fatty acids and alcohols) are typically susceptible to microbial decomposition. However, other lipid biomarkers, such as apolar, saturated hydrocarbons (e.g. alkanes), isoprenoids (e.g. phytane) and cyclic compounds (i.e. hopanes or steranes), are refractory compounds formed during diagenesis (Peters et al., 2007) and may be preserved for long geological timescales (e.g. Eigenbrode, 2008).”

In this section, the definitions can be introduced. Also, as it currently reads, since there is a dominance of easily degradable compounds in the dry permafrost and refractory compounds in the icy permafrost, this suggests lower levels of organic carbon preservation downcore.

We don’t want to overinterpret the biomarker data and split indices into “biotic” and “abiotic”. Since our material is very old, we have long periods with good preservation, interrupted with intervals where we have biotic degradation which could be from long time ago. The bacterial degradation is not exclusively happening during modern times, because the majority of the organic matter at the surface is very old too. However, it should also be noted that the old age would also partially result from the high age of the material that gets degraded, so if bacteria decompose the ancient material, it will also include some of the very old signature into their biomass too, which makes it look older than it may be, so it is quite difficult to be sure when the overprint really happened.

We added a statement in the introduction to resolve the contradiction between abiotic and biotic degradation (line 73): “Over large time-scales, both biotic and abiotic degradation occurred at Friis Hills. Abiotic degradation would result in the organic material near the surface to be better preserved (due to the principle of superposition). However, in a permafrost environment, biotic degradation which is restricted to the active layer (layer that thaws in freezes on an annual basis) during warmer climate intervals would overprint the abiotic degradation and would be more important near the surface, incorporating both contemporary and ancient organic carbon into the system (Kusch et al., 2021) “

2.2 Exploring the hopanoids to determine abiotic degradation This is a recommendation that the author can chose to ignore, however the hopanoid dataset may provide interesting insight into abiotic degradation occurring at this site, further supporting the CPI results. I make this suggestion as the author has already identified and integrated the hopanoids, therefore it is information that would take little work to acquire. If hopanes and their various stereoisomers were discovered, there a multiple ratios that can be used for tracing thermal maturation. For example, the C-17 and C-21 position of hopanes change from a ββ configuration to a more stable βα configuration during early diagenesis (Farrimond et al., 1998).

Thank you for the recommendation. We had actually explored hopane maturation and now include the C₃₀ ab/(ab+ba+bb) index in Fig. 6e. We introduce it in the method (line 257) section, and added it to the results (line 400) and the discussion (line 506).

3) Developing the methods and results section

The comment on the methods section is minor, but some of the indices which are eventually discussed in the results are not introduced in the methods. This includes the cholesterol to plant sterol ratio, 100*C15-17 iso-FA+anteiso-FA/n-FA; Pr:Ph, and C26-28 to C22-24 n-alkanols. It would be useful for the readers to be able to refer back to the methods to understand the ratios and what they represent. Having said this, Pr:Ph (Figure 6 and 8) and C26-28 to C22-24 n-alkanols (Figure 5) are not actually discussed within the text anywhere…is it required in the figures? On the other hand, TN is discussed (line 269 and 298) but is not available in a figure.

To streamline the result section and keep the focus on important indices, we removed the cholesterol to plant sterol ratio and C26-28 to C22-22 n-alkanol ratios (in Figure 5).

Pr:Ph is discussed in text in sections 4.2, 4.3, but we added a statement about it in section 5.2.

We added a section “3.4.5. Other indices derived from saturated hydrocarbons, isoprenoids and fatty acids“ to make sure that all the indices are discussed in the method section, where 100*C15-17 iso-FA+anteiso-FA/n-FA, Pr:Ph and C₃₀ ab/(ab+ba+bb) are discussed.

For the results section, although I agree with the author’s choice to first discuss the general background composition of biomarkers, prior to describing the data within each unit in section 4.2 and 4.3, I feel the first sentence is somewhat misleading. The author lists the compounds that show little variation, however then goes on to discuss their differences. For example, n-alkanes are stated as a biomarker that does not vary much, yet the CPI (which compares the odd vs. even n-alkanes) and SC:LC ratio (which compares short- vs. long-chain n-alkanes) is highest in unit 1. As done so for ACL, the author could instead focus on the averages or ranges of values. In addition, I would advise the author to be careful with not interpreting the data too much at this point. The fact that the cholesterol to plant sterol ratio and the BIT index indicates a terrestrial setting and the high-molecular weight compounds further support higher plant input is useful, however to infer that this reflects a “tundra dominated ecosystem” and this agrees with interpretations made from “macrofossils” is something that could be saved for the discussion. Similarly, in section 4.2, I would remove the sentence starting with “Overall…” and maybe expand on what the biomarker indices described in the first paragraph indicate, as done so for HPFA on line 278. This also applies to section 4.3.

Thank you for picking up on this contradiction. We rephrased the first paragraph of section 4.1 to reframe the general trends and avoid over-interpretation. It now currently reads: “We identified the following components within the 1.4m core: n-alkanes (n-C15 to n-C34), isoprenoids, hopanoids, n-fatty acids (n-C12 to n-C30), branched fatty acids with iso- and anteiso- (n-C13 to n-C17) configurations, n-alkanols (n-C12 to n-C28), ketones, and sterols. The distributions of n-alkanes, fatty acids and n-alkanols were dominated by high-molecular weight homologues, with ACL27-33 of n-alkanes, ACL22-32 of n-fatty acids and ACL22-28 of n-alkanols averaging 28.7± 0.5, 24.0 ± 0.3 and 23.3 ±0.4 respectively, and showed little variation in the core (Figs 3d, 4d & 5d). We also identified plant sterols (i.e. C29 sterols most abundant), pristane and phytane along with hopanoids (Fig. 6). The GDGT analysis showed that the distribution of all samples was dominated by brGDGTs. All samples had a BIT index of 1.0, and MBT’5ME index ranged between 0.24 and 0.48 (Supplementary Data). In general, the homogenous distribution of these biomarkers in the core are indicative of a terrestrial environment with higher plant components such as high molecular weight n-alkanes, n-fatty acids and n-alkanols and plant sterols.”

We also removed the sentence in section 4.2: “Overall, these biomarkers reflect the background composition of the tundra-dominated ecosystem of the site during the mid-Miocene as inferred from the macrofossils.”

We removed the sentences in section 4.3: “Overall, these indices display a gradient of organic carbon degradation that decreases downcore through the icy permafrost. The hierarchal clustering analysis suggest higher level of organic carbon degradation in the dry permafrost, intermediate level in unit 2 and lower level in unit 3.”

 4) Consistency between the abstract and conclusion

 In addition to being more cautious with the use of the term “degradation” in the conclusion, to avoid what could be interpreted as contradictory statements between the abstract and conclusion (see Section 2.1), the abstract could also benefit from providing a more ‘complete summary’ of the study.

The abstract appears to focus on the loss of the “legacy” mid-Miocene age carbon in the upper ‘dry permafrost’, however does not delve into the source of carbon that over-prints this signal, as done so in the conclusion on line 443, i.e “Although our study suggests that Holocene organic carbon is being introduced at high elevation sites such as the Friis Hills, modern C_org contributions remain very low (<1%).” This would be useful to include, in addition to a sentence on line 20 that explicitly states what the evidence found within the ‘dry permafrost’ indicates, as done so for the icy permafrost on line 21, i.e. ‘the multiple proxies indicate contribution of bacteria-derived organic carbon, and thus microbial organic matter degradation.’ Moreover, the discussion surrounding the brGDGT results and the significance of temperature on carbon availability / microbial activity is not mentioned in the abstract. However, although I feel the abstract could better expand on the breadth of data and interpretations made, I also acknowledge that there is a word limit. If the addition of the source of carbon and the temperature reconstructions is difficult, I recommend the author prioritises honing the final sentence of the abstract to make it more impactful (line 25). What exactly is the key outcome that is novel to this study that the author would like to highlight here? Is it really that this record provides a nice archive to examine ecological changes in the past? How about the cautionary tale of needing to exclude more recent microbial activity prior to interpreting biomarkers in sedimentary deposits? Or even that these archives are vulnerable to future warming? Alternatively, what we can learn from “present-day organic processes” (line 63)?

We added a statement on line 21: The near-surface (upper 35 cm) dry permafrost has lower C:N ratios, higher δ¹³Corg values, higher proportion of branched fatty acids with an iso- and anteiso- configuration relative to n-fatty acids, lower phytol abundance and higher contributions of low-molecular weight homologues of n-alkanes, than the underlying icy permafrost, indicating higher contributions from bacteria-derived organic matter.

We added the following statement on line 26: “This implies that legacy mid-Miocene age carbon in the near-surface soils (c. 35 cm) has been prone to microbial organic matter degradation during times when the permafrost thawed, likely during relatively warm intervals through the late Neogene (~6.0 Ma) and sporadically during the Holocene (<1%), when ground summer temperatures were ≥+2°C (based on brGDGTs temperature reconstructions).”

We believe that the current last sentences convey our message that ancient organic matter is preserved through large time-scales at Friis Hills, but also vulnerable to past and future climate change. More details are discussed in the conclusion.

Minor comments:

Line 15: “low input rates” of what exactly?

We clarified the sentence, which reads now: “The occurrence of ancient soil organic carbon combined with low accumulation of contemporary material makes it challenging to differentiate between ancient and modern organic processes.”

Line 15: replace “document” with explore or a verb that is more related to the aims of the study rather than results at this stage of the abstract

We changed “document” to “explore”.

Line 17: define ages for mid-Miocene, e.g. ‘(xx–xx Ma)’

Added (∼14.5-14.3 Ma).

Line 18: define FA, e.g. ‘branched fatty acids with an iso- configuration relative to n-fatty acids’ (following how the author defined iso-FAs in line 249).

Changed to “branched fatty acids with an iso- configuration relative to n-fatty acids”.

Line 19: go through the whole manuscript to check whether a hyphen is used or not used between “low/mid/high” and “molecular” and make it consistent

Added hyphen throughout text.

Line 24: define ages for late Neogene, e.g. ‘(xx-xx Ma)’

This is not derived from formal age range, but we added (~6.0 Ma).

Line 24: Since this study specifically focuses on lipids, “Biomolecules” could be replaced with ‘lipid biomarkers’

Done.

Line 27: it may be useful to clarify to the readers that “The hyperarid polar desert” refers to the MDV e.g. ‘The MDV is a hyperarid polar desert, and amongst the coldest and driest environments on Earth (e.g. Horowitz et al., 1972). The MD can be divided into…’

Changed the wording to “This hyperaid polar desert”

Line 40: specify where the “Shackleton Glacier region” is in relation to MDV? e.g. ‘further inland’

Done.

Line 42: could refer to Fig. 1a here, to place University Valley in geographical context

Done.

Line 43: the “3” needs to be in subscript, e.g. “CaCO3”

“CaCO3” as a whole is already in subscript, so we are not able to use an additional level of putting this into subscript. Perhaps this can be done in editing.

Line 45: add r to 152 ky?

Done.

Line 46: Fig. 1a can again be referred to here, after “At Friis Hills…”

Done.

Line 47: the “oldest” what? permafrost?

Yes, we added permafrost again for clarification.

Line 48: define ages for mid-Miocene again in introduction, e.g. ‘(xx–xx Ma)’

Added (~20-14.6 Ma)

Line 56: could be reworded to, e.g. ‘and may be preserved on geological timescales’

Done.

Line 59: start new paragraph?

In our version of the manuscript this already is a new paragraph.

Line 59: could remove “diagenetic”

Done.

Line 60: for consistency within the text, use total organic carbon (TOC) rather than “total Corg”. In addition, technically speaking, total N is not part of “bulk organic carbon analysis”.

Changed to TOC. Changed to “bulk carbon and nitrogen analyses”

Line 93: is there a map of Friis Hill with the three sites? Could be added as a supplementary figure?

These three “2” boreholes are few meters apart. A map wouldn’t be useful here. Since we only discuss the 2C borehole here, we think the coordinate is suitable for situating the site.

Line 95: “metre” can be abbreviated

Done.

Line 117: this sentence could be reworded, e.g. ‘The total organic carbon (TOC) and total nitrogen (TN) were measured to determine: i) the soil organic carbon density (SOCd); and ii) if the C:N ratios in the bulk sediments follow the Redfield biological stoichiometry ratio (6:61, Redfield, 1934).’

Done.

Line 162: could a more specific word be used instead of “measurements”? e.g. ‘The concentrations or abundances of lipid biomarkers were used…’

Done.

Line 171: this sentence is repeating what was stated in line 166, and I would also remove “as odd chains get altered into smaller chain lengths” as it may confuse readers considering CPI does not capture changes in chain length. If this sentence is removed, line 169 could be incorporated into the paragraph beginning on line 165.

Sentence line 171 was removed and sentence line 169 was incorporated into line 165.

Line 185: should “i” and “Ci” be in italics to match the Equation 3?

Done.

Line 195: although Strauss et al. (2015) uses the term “chemical degradation”, could the author clarify what this means? Is this an abiotic process not involving microbial activity?

Changed “chemical” to “organic matter”.

Line 198: could reword “Since n-alkanes are typically preserved better…” to, e.g. ‘less labile’ or ‘more stable’ etc.

Changed to more stable.

Line 198: is there a threshold or range for “low HPFA” values that represent “high degrees of organic carbon degradation.” I also wonder if it would be safer to say “relatively high” because a “high degree” could be interpreted as catagenesis or even metagenesis of organic matter, unless this is what the author intended? This also applies to line 278 and 361

It is a relative index, so difficult to set a threshold and there are no absolute thresholds reported in the literature. We changed the wording to “low HPFA are indicative of higher degrees of organic carbon degradation”

Change on line 278 (now 380): “Lower HPFA values are typically indicative of higher degrees”

Changed on line 261 (485): now: “experienced a relatively higher degree of organic carbon degradation by microbes, whereas the underlying icy permafrost (38-71cm) experienced relatively lower levels of degradation”

Line 201: could the author define the BIT index, e.g. ‘branched/isoprenoid tetraether (BIT) index’

Done.

Line 201: is the equal sign most appropriate here? i.e. must the BIT value equal 1 to indicate a terrestrial signal and vice versa for 0 and a marine signal?

Changed to ≈.

Line 210: a space is missing between the subsection 3.5 and paragraph below

Done.

Line 215: RPO is used here and in the captions for Figure 7 and Table 1, without it being defined anywhere in the text

Defined acronym.  

Line 223: define OM, e.g. ‘organic matter’

Removed acronym all together from manuscript.

Reviewer 2

The manuscript by Verret and co-authors examines a Miocene age sediment sequence from the Friis Hills in Antarctica, to explore the potential lipid biomarker and organic carbon evidence for both the original Miocene tundra soils and the subsequent diagenetic impact on the composition of the organic matter. Several techniques and metrics are applied, including a characterisation of a wide range of lipid distributions, carbon and nitrogen content, bulk carbon isotopes, pyrolysis and radiocarbon analysis. The authors argue that they show evidence for the original tundra organic inputs, of Miocene age, and a later diagenetic impact during warmer periods of Antarctica’s past, when the formation of the active layer would likely have enabled microbial activity. The study is an interesting one, which also contains a rich set of data which has been carefully produced and presented.

We would like to thank the reviewer for taking the time to read through our manuscript and provide valuable feedback.  

I have two main concerns.

First, my main concern is about the framing of the temperature story. The authors argue that the soil temperatures that they reconstruct are indicative of “threshold temperatures” required to support microbial activity and thus organic matter degradation (e.g. line 63 and Section 5.4). They use the branched GDGT proxy to calculate the soil temperatures from each of their three sedimentary units. I am unclear why temperatures have to represent post depositional diagenesis, which the authors argue occurs perhaps millions of years after deposition, when branched GDGTs are found with a global distribution today including in the polar regions, and importantly including in tundra settings. Why are the brGDGTs not a contemporary signal of tundra soil temperature during the Miocene, with a potential cooling over time being represented moving upwards from unit 3 to 2 to 1? In line 253-254, for example, the text includes mention of the dominantly terrestrial origin of the brGDGTs in amongst text which refers to the lipid biomarkers being “…indicative of a terrestrial environment “. This is also how we would interpret brGDGTs in more recent sedimentary sequences: as a tool to explore temperature change in the context of co-recorded signals of environmental change. To me, a change in temperature over time (from 7•C deeper in the site to near zero near the top) is more easy to explain than how an activation temperature of 7•C is needed at depth if the surface is only recording 0•C? The authors seem to be suggesting that once the soil hits a single temperature, the microbes record only that temperature, even if it gets warmer than that afterwards?

The climatic transition occurred several million years ago and our dataset seems to point towards a subsequent alteration of the organic material post-deposition, at least in units 1 and 2. This is why we present the temperature reconstructions as threshold temperatures for microbial activity. Had there been no sign of biological overprinting near the surface, the Miocene climatic transition signature recorded in the brGDGT that the reviewer suggest here would have been preferred. However, since the organic material has been altered post-deposition, the brGDGTs would reflect overprinting. In a permafrost context, biological activity is restricted to the active layer that thaws and freeze on an annual basis. The thaw depth is temperature dependant. Therefore, the 7°C required to reactivate activity at depth is simply a function of the surface temperature required to induce a thaw depth of 1m at this site.

We added a statement on line 580 to clarify this: “However, this assumption does not take into account subsequent warm periods (which would result in a re-opening of the system). Therefore, the temperature reconstructions could correspond to either: (1) the temperature at time of enclosement (here the mid-Miocene) or (2) the temperature at time when the active layer last thawed to that depth and thus the threshold temperature to activate bacteria activity at a given depth. Since the previous sections have shown clear signs of overprinting in units 1 and 2, and to some extent in unit 3, the latter assumption is more likely.”

Second, radiocarbon analysis seems under explored. The authors argue that the fraction modern carbon suggests less than 1% input of microbially produce carbon, but how this figure is arrived is unclear, when they only refer to the bulk date (line 378) and do not explore the range of values given by the RPO in figure 7. If microbial activity is using both Miocene (infinite age) and modern (atmospheric) carbon then I would expect a large imprint of the infinite age carbon on this signal, which might mean an underestimate of microbial activity. I think detail is needed here to explain how the authors reach this <1% figure.

We don’t want to overinterpret the radiocarbon data since there is considerable uncertainty of what is considered “modern”. It is important to note that modern biological processes would also incorporate ancient carbon (Kusch et al., 2021). Our aim here was to detect any sort of radiocarbon active contribution. The <1% modern input relates back to a simple two-component mixing model and for F¹⁴C=0.5 (Holocene) and F¹⁴C=0 (ancient) and using the bulk date (F¹⁴C=0.0055). Younger ages yielded from the RPO would include a larger fraction of Holocene carbon, although the selection of F¹⁴C value for this “modern” carbon makes quite a difference.

We added a specification on this on line 504: ¹⁴C of bulk sample indicate active microbial activity is small (<1%; using a simple two-component mixing model and assuming F¹⁴C=0.5 for Holocene carbon, with a half-life of 5730 yrs), but yet it is producing degradation of organic carbon over large time-scales (as shown in the biomarker results).

General comments:

• it’s unclear why only one sample near the surface is analysed for pyrolysis, as repeating these measurements in units 2 and 3 might have shown what a less degraded horizon looked like

With limited resources, we targeted the unit most likely to have modern contributions (largest overprinting), making a sample from unit 1 the most important to run. We agree with the reviewer that running the pyrolysis experiment on one sample from each unit would have been optimal, but we only had the resources to analyse one sample (6 radiocarbon dates in total). However, we wanted the paper to focus mostly on the biomarker distribution, since the timing of activity is difficult to determine. We ran the pyrolysis analysis in parallel, so we thought it was still interesting to present the results here. We acknowledge in the conclusion that the dating should be interpretated with caution and recommend that it should be investigated further.

• I suggest that the authors think carefully about which graphs to include or on which order. Figure 2 is presented within the text early on, but the results section lists figures 3-5 before then, and the latter graphics contain a lot of detail which is confusing because the opening section says many of the lipids don’t show any change, so I’m unclear why all of these results are displayed in the main text.

We think it is important to showcase Figure 2 first as it presents the stratigraphic units in relation to the 3 units presented in this paper. We added a reference to it earlier in the results on line 322.

Minor clarifications:

• line 113: there is a risk of organic matter degradation if samples are warmed up, so I’m not clear why the authors would not freeze dry these samples rather than exposing them to water and air at elevated temperatures?

Unfortunately, this was a requirement by the importing authorities in New Zealand. We acknowledge that freeze-drying would have been optimal since it is the standard method for lipid biomarker extractions and that heating at higher temperature has been shown to potentially impact biomarker distributions. However, we look at predominantly ancient organic matter where initial diagenesis should also have had an impact on biomarker distributions, so we would expect only limited impact on the biomarker distributions from the drying procedure. According to the biomarker guide by Peters et al, for instance, the n-C12 alkane has a boiling point of 216°C, so we would not expect major differences due to the drying of the samples at 80°C. Also, we still detect ancient, intact plant sterols among other more labile biomarker suggesting that degradation by sample drying cannot have had a major impact on the robustness of our dataset. Indeed, a bulk of literature shows that oven-drying does not alter significantly plant biomarkers (Suh & Diefendorf, 2020 and references therein). Therefore, we are confident that the drying process had limited impacts on the biomarker distribution and stable isotope composition.

• Also line 113: what is the evidence that this drying procedure didn’t introduce contamination? Were blanks included?

We did not include blanks during the drying procedure, but we did comprehensive blank control during all steps of the biomarker extraction, processing and analysis, where we used large volumes of material. We did not find any plastic or any other contamination in our samples, so our samples and results are robust, with no evidence of being compromised in any way.  

• Line 137: indicates that the polar fractions were derivatised with BSTFA, but later (line 158) the ions selected for the brGDGT analysis are given. Would they not have been impacted by the derivatisation?

Different aliquots were used. We made the clarification on lines 174 and 185.

• Line 170: this implies that odd numbered C chains are only created by diagenesis, but they are also found in plant waxes (as noted for section 3.4.2). Care needed here with phrasing.

Thank you for noting this. We changed it according to the recommendation made by reviewer 1: “Natural distributions or well-preserved n-alkane signatures are expected to show a predominance of odd-numbered carbon chains because of decarboxylation of fatty acids that show characteristic even carbon number predominance.”

• Section 3.6: there is no mention of the RPO experiments (figure 7 shows them), so these need to be included.

We have merged sections 3.5 and 3.6 together and added details on the RPO experiments.

• Section 3.7: please check the readme file for chcluster, but I thought that this method explicitly included an acknowledgment of the ordering of the samples, so that the suggestion in line 240 that the statistics did the grouping (and found an anomalous sample) seems incorrect. Is the anomalous sample flagged as a 4th cluster, and was it statistically significant? The anomalous sample only stands out as being anomalous on figure 2.

The anomalous sample was part of a 4^th cluster and therefore we removed it all together for ease of grouping. This sample had particularly low C content (within error range) to which all biomarker indices were normalized, making it plot as an outlier in all the graphs that are normalized to C_org. Therefore, it was excluded from the interpretation.

• Line 243 flags two additional statistical tests which were performed but I have struggled to find where the results of this analysis are presented or used to inform the interpretations.

Thank you for picking-up on this. We did these tests for initial screening. Since we do not present the results from these tests we removed the following statement: “An ANOVA within subjects and post hoc Tukey HSD tests were then conducted on the results to determine whether the means of each variable in the three units were statistically different.”

• Line 251 is the only time that the cholesterol / plant wax ratio is referred to. What is this showing, and what is the reason for the peak in unit 2?

We removed this ratio based on a comment from reviewer 1.