Dear Dr Smith,



thank you very much for your comment, you brought up some good points which are much appreciated. We respond to them point by point below. We hope that all objections can be resolved with this. 

How did the authors add CO2 from the carbon-relevant tipping points to FaIR? There are two categories of CO2 in FaIR: fossil & industrial sources (FFI), and AFOLU. Both CO2 sources add CO2 to the atmosphere in the same way, but CO2 AFOLU emissions are used to derive radiative forcing from land surface albedo change (Smith et al. 2018, https://gmd.copernicus.org/articles/11/2273/2018/). This simple relationship is based on the assumption that most CO2 AFOLU emissions are from deforestation for cropland, and changes the land surface from dark to light resulting in a net negative forcing.

At the moment, incorporating emissions from Earth system feedbacks into FaIR is a bit of a hack*. Maybe AMAZ and PFTP would affect forest cover and in both cases, albedo would reduce if the forest dies, so perhaps they should go into the CO2 AFOLU category and PFAT into FFI. It’s not FFI of course, but that column can be used for CO2 emissions that do not affect surface albedo and hence no impact on the land surface forcing.

In FaIRv2.0.0 by Leach et al. (2021), which is the version FaIR we are using, albedo shifts due to land use change are prescribed externally and are not coupled to AFOLU carbon emissions. To the best of our knowledge, there is no distinction made between FFI and AFOLU carbon emissions in FaIRv2.0.0, hence there is only one stock of CO2 and CH4 emissions, to which we simply add the emissions from the carbon tipping elements. You are right in assuming that Amazon rainforest dieback would probably lead to a higher surface albedo but it is also predicted to reduce cloud cover and this is the greater effect. The total biogeophysical effect of tropical forest loss is estimated to be positive, i.e. forest loss would warm the earth beyond the warming induced by the emitted carbon alone (Lawrence et al. 2022, https://www.frontiersin.org/articles/10.3389/ffgc.2022.756115/full ). There are several mechanisms at play producing this positive feedback, with the main ones being reduced surface cooling by evapotranspiration from forests, which also leads to reduced cloud formation. Permafrost thaw is assumed to promote northward migration of boreal forests, which would decrease the local albedo (Scheffer et al. 2021, https://www.pnas.org/doi/10.1073/pnas.1219844110). However, this albedo change is more related to the northern expansion of boreal forests, which is also assumed to include a tipping point. We do not consider changes in boreal forest cover, since northern expansion and southern dieback are expected to roughly balance out.   

Including biogeophysical effects in our study would require a significant increase in complexity, without necessarily increasing its meaningfulness. Hence, we decided to disregard them and focus on the effects of carbon emissions alone. 

[as an aside I don’t find some of the acronyms for the tipping points very intuitive. I’d almost recommend spelling them out everywhere, if you can stomach it].

We could spell them out in the text, however, we need to use acronyms in the figures. 

*bear with us. We’ll sort it eventually.

Starting from section 3: I’m uncomfortable about applying IPCC calibrated language to the findings made in this paper, since the IPCC statements relate to assessments made with multiple lines of evidence than apply nominal probability ranges to likelihood statements, and this paper presents one study with calculated probabilities of tipping points being breached. Using a different calibration of FaIR would give you different results, as would using different probability distributions for your tipping point threshold crossings (see two comments below on these points). The discomfort comes when translating probabilities from this study back into natural language. One example is given on line 327: “(GRIS, WAIS, REEF and PFAT) become more likely than not to be triggered by 2026”. Is this really true? This seems like a very over-confident statement to make with a very precise timeframe given. In short, the relationship between IPCC calibrated language and probabilities flows in one direction, but not both. 

The calibrated IPCC language is used with the intention to make the text more readable, and we think its use is justified since a fixed translation to probability ranges exists. You are right that our results are sensitive to our model setup, however, this would affect calibrated language statements in the same way as it would affect the actual numbers. In the example you mention, we translate our finding that by 2026 GRIS, WAIS, REEF and PFAT all have a probability of getting triggered above 50% to the statement that they become more likely than not to be triggered. Both are true, given our results, and might change with the model setup. 

We do not believe that using the calibrated IPCC language leads to an overstatement of our results simply because we use the translation in reverse to express a probability. If this was true, it would mean that the use of IPCC calibrated language is restricted to the IPCC or similar bodies gathering evidence on a broad basis which informs likelihood statements, which is not an opinion we share. Therefore, we would like to stick to our use of the calibrated IPCC language. 

One thing I am missing a little from this study is the consideration of overshoot. My reading is that once a temperature threshold is crossed, a tipping point will happen with certainty, though it may take hundreds of years to manifest and in the meantime we may have been able to bring temperatures down substantially. Can we tolerate overshooting a threshold, if the overshoot is small and temporary? Are any of the tipping points reversible on the lower branch of the bifurcation if temperatures are reduced?

That is correct, especially tipping elements with long internal timescales are thought to be able to tolerate an overshoot of their threshold temperature for some time before they tip (Richie et al. 2021, https://doi.org/10.1038/s41586-021-03263-2). We do not include this effect in our study, which is something we could mention in the discussion section. Including this effect would potentially cause lower tipping probabilities of ice sheets under SSP1-1.9 and SSP1-2.6.   

Minor comments

9: FaIR is not an intermediate complexity model in the sense of it including a gridded, book-keeping land and ocean carbon cycle module such as in a model like UVic. It’s much simpler; “emulator” or “reduced complexity model” is more appropriate. 

Will be changed in the document, thanks. 

13: “triggering until the year 2500 of 65%”. I’m not sure this statement is well-defined. Triggering which tipping point? All of them? 

This refers to the probability of tipping on average over all tipping elements in the year 2500. We can make this clearer. 

60: under what process do the NH and SH forest dieback balance out in terms of global warming? Is it a carbon cycle feedback, surface albedo feedback, some combination of both?



It is the carbon cycle feedback. This is what the current IPCC report says: “Boreal forest dieback is not expected to change the atmospheric CO2 concentration substantially because forest loss at the south is partly compensated by: (i) temperate forest invasion into previously boreal areas; and (ii) boreal forest gain at the north”  (page 740).  

64-65: difficult to read sentence: would recommend separating list items with semicolons.



Will be added, thanks. 

66: FaIR does not include the deepening of the active layer / gradual permafrost release feedback either, so I assume that this process is not accounted for in your analysis.



Correct, we do not include gradual thaw of permafrost since it is not regarded to be a tipping element (Armstrong McKay et al. 2022) and more sophisticated modelling techniques already exist. 

71: 20% - is this the fraction of SOC released as methane? Please confirm.

Yes

115: best to specify FaIR v2.0.0. Since there is a v2.1 already out. In fact the calibration of the model makes rather a large difference (lines 121-123), as we have a constrained ensemble of FaIR v2.1 which meets all of the IPCC assessed constraints with good precision as well as historical climate observations (https://zenodo.org/record/7694879).



Will be added, thanks. 

Table 1: while a review of Armstrong McKay et al. (2022) and this paper does not provide a new analysis of tipping points, I would think that Sahel greening would constitute some carbon drawdown. 

Armstrong McKay et al. (2022) mention in the supplementary material that some carbon would be sequestered by Sahel greening, but not enough to measurably impact the global climate and land surface albedo would be lowered. 

202-210: the list of distributions to choose from is limited by the software package, which is unfortunate. Any three given percentiles of a distribution can be fit with a three parameter model; a good choice here would be skew-normal, which reduces to a normal if the upper and lower bounds are symmetric.

Thanks for pointing that out. Using a three parameter model would probably improve our methodology, however we are not in a position to redo the whole analysis. Furthermore, the distributions we use are fitting the percentiles sufficiently good. 

Figure 3, 4 (maybe others): using the same y-axis range on each subplot would be more informative.

For Figure 3 we provide a plot with a shared y-axis in the supplementary material. We do not use a shared y-axis in Figure 3 to make the relation between anthropogenic carbon emissions and carbon emissions from carbon tipping elements clear. If we used a shared y-axis, you would only see that emissions are increasing from SSP1-1.9 to SSP-8.5, which is pretty obvious and stated in the text. The same argument holds for Figure 4. Since the difference in warming is so big between the different SSPs, you would not be able to see how carbon emissions from carbon tipping elements shift the temperature distributions for low-emission SSPs if we used a shared y-axis.  

289: we don’t take credit or blame for the forcing relationship in FaIR; it is derived from Etminan et al. (2016) at https://agupubs.onlinelibrary.wiley.com/doi/full/10.1002/2016GL071930, which is a fit to line-by-line radiative transfer simulations.



Thanks for the hint, we must have missed that. It will be changed in the document.

Table 2: SSP1-19 results have bigger dT in 2300 than 2200 and 2400; what’s going on here?

This can be linked to declining atmospheric methane concentration anomalies due to the comparably short lifetime of methane. We mention this in lines 300 and 301. 

311: The chance of TEs being triggered earlier if carbon emissions are included is surely 100%? Because a carbon TE doesn’t ever remove carbon, and your delta warming will always be positive unless your additional carbon release is zero.

That is correct, we will change this sentence to “Especially TEs within the cryosphere will become more likely than not to be triggered decades earlier, if carbon emissions from carbon TEs are included.”

315: “disproportionately”: not sure about use of term here 

We will change it to “much” to keep it simple.  

We thank the referee for his detailed comments on our manuscript. He raised some valid points that demand revision. The main changes we plan in response to them is to remove SSP1-1.9 from our analysis, since the missing opportunity for overshoot of threshold temperatures results in overestimated risk of triggering under this scenario. Furthermore, we will rephrase our manuscript to better convey the key message that the additional probabilities of triggering from carbon emissions of carbon TEs are small compared to the scenario-dependence of triggering probabilities. We answer the comments in more detail point by point below and hope to resolve them sufficiently. 

The manuscript by Deutloff et al combines assessments of thresholds of tipping elements in the earth system based on a recent paper by Armstrong McKay (expressed in GMST) with the uncertainty of different temperature outcomes under SSP scenarios. This is a relevant and useful idea, as the focus on GMST levels alone misses out on the scenario uncertainty with regard to different warming outcomes. However, it is also not entirely novel as e.g. Kloenne et al (2022) make similar points for irreversible thresholds in the cryosphere.  

However, there are several substantial shortcomings with the analysis in its current form. Some of the results about timing of tipping points I’m not sure are correct. But more importantly, the way tipping is implemented without any considerations of the temporal dynamics of GSMT is too simplistic.



Also, the deterministic nature in which values of an expert assessment in a single study (which is not IPCC) are being implemented requires some reflection.  

We do reflect that our results depend on the findings of Armstrong McKay et al. (2022) in L443. It is our understanding that this study is currently the best summary of the current literature on tipping points, hence it represents a reasonable basis for our analysis. However, you are right in that we cloud make this point more prominent in our manuscript. 

The manuscript has quite some focus on tipping elements with carbon cycle relevance and attempts a coupling between their carbon cycle model and FAIR. I’m not convinced this analysis is robust – first and foremost because the carbon cycle in FAIR is not well constrained and assuming that these dynamics would really be ‘additional’ is an assumption that needs to be justified. However, no analysis of the carbon cycle dynamics in FAIR is presented. I generally think this might not be the right SCM to attempt such a coupling. 

It is correct that we do not justify why FaIR is suited to couple the carbon tipping elements model. We spared this section to keep the paper reasonably short. However, there are good reasons to assume that emissions from the Amazon or permafrost are not included in FaIR which are presented in the thesis the manuscript is based on (https://mpimet.mpg.de/fileadmin/portfolios/127/Masters_Thesis_Jakob_Deutloff.pdf). We will include this section in the supplementary material.  

Secondly, the results are being highlighted quite a bit across the manuscript – whereas in my mind the real finding is that their effects are very small. However, even the title of the manuscript seems to imply that there’s something more to it. I understand that this might have been the hypothesis of the authors when they started their analysis. But their results don’t show it (there are also some issues with how the additional GMST is derived if I understood it correctly). I’d suggest the authors may want to consider removing this part of the analysis, or else substantially repackaging it and underscoring the explorative and illustrative nature of the analysis presented.



We agree that the overall effect of carbon emissions from carbon tipping elements is small compared to anthropogenic emissions. We will make this finding more prominent. 

Other major comments below.

L 61: This strikes me as an argument that’s somewhat incoherent with the rest of the manuscript that (rightly) focusses on uncertainties. Because even if they may cancel out in the central estimate, any deviations from this could still have potentially far reaching implications. Also note my comment on the numbers in Table 1.



It is correct that adding BORF and TUND to our analysis would lead to a larger uncertainty of carbon tipping elements impacts, even if we assume their carbon emissions cancel out, which is not the case in Armstrong McKay et al. (see below). However, we think it is reasonable to exclude BORF and TUND since they are not expected to be major tipping elements within the Earth’s carbon cycle according to the IPCC and their biogeophysical effects (mainly albedo) predominate the impact their carbon emissions would have on global warming.  

L89: This assertion is not correct. A delayed action (past 2030) 1.8°C in 2100 scenario as identified in Meinshausen et al. is quite different from SSP1-2.6 (with emission reductions starting in 2020) – also in the long run which matter a lot for the outcomes here. 

 You are right, the two scenarios are not exactly identical. Since SSP1-1.9 will be removed, we will no longer need to make this comparison. 

L89: I don’t think this paper is the place to speculate what’s political feasible or not. SSP1-1.9 is part of the core set of IPCC WG1 and the WG3 has published a range of IMP scenarios that resemble similar characteristics (1.5 low and no OS). The authors are of course free to choose whichever scenario they like – but to argue SSP1-1.9 was not but SSP1-2.6  is not convincing. Also, it’s long-term outcome emissions and temperature trajectory that matters more than the next decade for the tipping dynamics here I understand. And what’s “feasible” on these scales is not established. 

In this section, we wanted to make the point that SSP1-1.9 is harder to achieve (maybe infeasible according to Jewell and Cerp (2020)) than SSP1-2.6 which allowed us to draw the conclusion that SSP1-2.6 is optimal in the respect that it already reduces the risk of tipping substantially compared to SSP2-4.5 but is more achievable than SSP1-1.9. Since SSP1-1.9 will be removed, this comparison is now redundant. 

Table 1: I’m a bit surprised by the numbers for BORF and TUND. The carbon removal is an order of magnitude different, but the warming effect is very similar. I understand that’s also the case in the original Armstrong-McKay paper. But would be good to verify and explain these findings. I am not across the underlying literature on this – but if the reason was biophysical effects (i.e. warming by increased tree cover), then this would be a local effect rather different from the one on the global carbon cycle. 



Armstrong McKay et al. (2022) argue that changes in evapotranspiration and albedo are counteracting and outperforming the carbon uptake (emissions) from TUND (BORF).

You are correct, these are local biogeophysical effects, however, they affect global temperatures. Since carbon emissions are only of secondary importance to explain this temperature change, we exclude BORF and TUND from our model framework.

L 138: I would like to get some more clarity on why this assumption that PFAT is amplifying PFGT is justified. 

Armstrong McKay et al. (2022) base this assumption on the finding from Turetsky et al. (2020, doi:10.1038/s41561-019-0526-0) that PFAT spreads at similar rates as PFGT in permafrost models. More information can be found in the supplementary material of Armstrong McKay et al. (2022). 

L 175: I’m a bit concerned about this implementation as there’s substantial variability in the carbon cycle response across the full FAIR member ensemble. Some of these carbon cycle ensemble members may actually already reflect (at least conceptually) some high emission outcomes including from those sources assumed (although they’re of course not explicitly modelled in FAIR). So right now it appears to me that some additional emissions are added to ensemble representations that may already, at least by allowing for a wide uncertainty range during constraining, account for some of the effects considered. In other words, I find it very hard to argue that these modelled TE effects are really “additional” when considering the wide range of carbon cycle outcomes under FAIR.

So I’m not sure this approach actually works – or is a bit overly simplistic. Some other simple climate models such as OSCAR have a much more detailed representation of the carbon cycle including also a permafrost module, for example. They might be much better suited for such an application. Else it might be better to remove that part of the analysis.

Please see our answer to this point above. 

L195: So to make sure I get this right: Distributions are fitted through 3 data points based on expert assessment, is that correct? It seems to me that pre-industrial = zero risk is also fixed, right? I think it’s fair to say that these distributions are then not very well constrained, also bc. the assumption of taking values for min/max/ best estimate as a given without assuming (allowing for) uncertainties around them. It would be good to see some sensitivity studies of fitting different distributions with different rigidity to assess the effect.

Your interpretation of the probability distributions is correct. We did not include uncertainties of the min/max/best estimate because this range of estimates is already intended to represent the uncertainty in it. Hence, it would not be useful to include an “uncertainty of the uncertainty” by guessing uncertainty ranges of the min/max/best estimate. Adding some sensitivity analysis as you suggested could still be useful to prove the robustness of our approach. 

L230: This part strikes me as crucial and I don’t know if agree with the approach taken here. It is my understanding that the assessment made in Armstrong-McKay relate to stabilization temperatures. But it is not well established for how long these temperature levels would need to be exceeded in order to trigger tipping. If I understand the proposed methodology correctly, this would not be taken into account. If peak warming is above a randomly sampled value, it’s triggered – regardless of the temperature trajectory after. I don’t think that works. As in particular for some of the elements considered, i.e. sea-ice, they would respond quite quickly to a reversal of global temperatures. Similarly, the AMOC for example might show a rapid recovery or even overshoot under reversal of warming (at least in relation to its thermal component – the saline component would probably need to consider a coupling to the Greenland ice sheet). I’d argue that this would also matter for the permafrost dynamics quite a bit, in particular PFAT – that should be stopped once temperatures decline below again 

Other approaches such as by Wunderling et al (2022) explicitly take this time dimension into account and show that long-term stabilization temperatures actually matter quite a bit. So with this current implementation, tipping risks under SSP1-2.6 and SSP1-1.9 are systematically overestimated. As this is also quite apparent in the results (i.e. Fig. 4) I think this should be addressed. I also think it shouldn’t be all too difficult to come up with a temporal distribution for “overshoot” time coupled to peak warming and test the sensitivities of the outcomes towards considering this effect. 

You are right, we do not account for internal timescales of TEs and do therefore not include possible overshoots of the threshold temperature without triggering. We will mention this in our discussion. We agree that this is an important effect and will therefore remove our results for SSP1-1.9 from our manuscript, since this scenario includes a pronounced temperature overshoot. SSP1-2.6 still includes a mild temperature overshoot, but we think it is acceptable to include and mention the missing internal timescales in the discussion. The missing internal timescale will have the biggest effect for TEs with long internal timescales, i.e. cryospheric ones (Ritchie et al., 2021).  Therefore, especially probabilities of  triggering for GRIS, WAIS and BARI might be overestimated under SSP1-2.6. We will add this to our discussion. 



Since the cumulative carbon emissions from PFAT scale linearly with the surface temperature anomaly (eq. 2), the missing internal timescale is not a problem in this case.



To include internal timescales in our analysis would increase the complexity of our approach too much to be feasible for us within this review process. However, it could be an interesting opportunity for future projects building on our work. 

L245: I suggest to not use IPCC calibrated language here (but rather stick to the percentiles). This study is explorative and in this way interesting, but still very far away from the robustness in understanding that would underly any IPCC assessment.



We will follow your suggestion, thanks.  

Figure 3: Strongly suggest to put them all on the same y-axis. (Or at least group together). This way the first visual impression of what this graph is saying is quite misleading.

Grouping them together could indeed be a good solution here. We decided for individual y-axis to make the relative importance of the carbon emissions from carbon TEs to anthropogenic emissions visible. A shared y-axis would have the effect that the difference in anthropogenic emissions is visible. 

L275: This comparison to the median of the ensemble doesn’t make much sense. Clearly, the high end TE feedback outcomes, would be triggered under high warming FAIR realisations. So they wouldn’t materialize compared to the median and their relative contribution would be smaller. I suggest to derive the additional warming relative to each individual realization.



You are right, high-end TE feedback outcomes are more likely to be triggered under high warming FaIR realisations, this is why the 95th percentile rise more than the median of the temperature distributions as shown in Figure 4. However, in Table 2 we show exactly what you propose deriving. Here we calculate the additional warming we get for every individual ensemble member from including carbon TEs and then calculate the percentiles from this additional warming. We should be more clear about this in the caption of Table 2.  

Table 2: Why is there a peak in 2300 despite methane and CO2 emissions staying pretty constant for SSP2-45 and lower scenarios? Is this only because of the PFAT component? I find this a bit strange tbh. And would suggest the authors look into this more to understand what drives this behaviour (might well be an artefact of their method to derive warming relative to the median, also noting that the uncertainty ranges don’t change as much as the median).

The methane and CO2 emissions in Table 2 are cumulative, so after 2300 there are no major additional emissions. The temperature decrease after 2300 can be explained by the declining atmospheric methane concentrations (Fig. S10). 

L300: Not sure I understand what is meant here. Methane concentrations should decrease even faster without those additional emissions. So any additional source should keep the warming up implied by the rate of emissions pretty much. Maybe the authors can help me out here.

We hope this is more clear now, given our elaborations on Table 2 above.  

Fig. 5: This figure illustrates the problems with this approach. Absence of a temporal component makes all tipping elements leaves almost no scenario dependence in the near-term, but the signal is determined by the median warming trajectory. It then also seems to imply that 5 tipping points are breached in 2025 under all scenarios. I’m not convinced this actually represents dynamics of the systems under investigation and that the evidence for such an imminent tipping is sufficient. I’m also a bit confused timing-wise. The threshold for GRIS for example is established as 1.5°C (median estimate) – but the crossing time here is 2023 or 2025. Similar for REEF and WAIS, as well as PFAT. That’s more around 1.3°C and 10 years earlier than when 1.5°C would be crossed in the SSPs in FAIR. I’m not even sure if 1.5°C is exceeded in SSP1-1.9 in FAIR (certainly not by much and for long). I appreciate that there’s some skewness introduced by the fitted distributions, but by eye-inspection this doesn’t look like so much from Fig. 2. So I suspect there’s actually a mistake here – which would need to be corrected.



Thank you for raising this point, there is actually a mistake here. In our code, we forgot to calculate the temperature anomaly relative to the 1850-1900 period before comparing it to the tipping thresholds but used the raw temperature. The raw temperatures produced by FaIR actually cross 1.5°C in the median under SSP1-2.6 in 2025, which explains that our model produces a 50% chance of tipping for TEs with a best estimate of 1.5°C in this year. The temperature anomaly relative to 1850-1900 only crosses 1.5°C in 2027 in the median, so this error leads to crossing of the 50th percentile two years earlier. We will of course correct this, however, it will not change our results dramatically. A warming of over 1.5°C relative to 1850-1900 is still exceeded in the median of SSP1-1.9 (Fig. 10 in Leach et al. (2021) and Fig. 4 in our manuscript).

L367: Small compared to what? And the fact that there’s no scenario dependency in the timing of some of the tipping points is a direct outcome of your assumptions including of not considering temporal dynamics from tipping (and maybe some errors in the GMST estimates from FAIR?).



The reduction of the probability of triggering averaged over all TEs in 2500 (end of the model run) under SSP1-1.9 compared to SSP1-2.6 is only 11.2 pp, which is small compared to the reduction in this number when moving from SSP2-4.5 to SSP1-2.6. We should be more clear here. 

 L378: Agreed re questionable assumption on permafrost. Maybe a good reason to not do it?

Since we use Armstrong McKay et al. (2022) as the foundation of our study, we think it is reasonable to follow their suggestion on how to divide between permafrost components. However, our analysis of additional carbon emissions from carbon TEs must to some degree be seen as hypothetical, given the partly low confidence in their existence. This is the message we want to convey with this paragraph. We will try to make this more clear in the revised version. 

 

L445: See comment above on SSP1-1.9 and feasibility discussion. Please revise



This should be resolved by excluding SSP1-1.9.