Netzel et al. present a new method for pollen-based quantitative climate reconstructions based on the ‘mutual climate range’ approach. They develop an algorithm using Bayesian statistics to overcome the disadvantages of other methods such as age model uncertainties, criteria for plant taxa inclusion/exclusion, and human-induced impact on natural vegetation. The method is applied on a previously published palynological dataset from Lake Kinneret (Eastern Mediterranean region) that spans the past c. 9 kyrs suggesting a mean winter temperature of c. 10 ^oC throughout this time interval and a mean annual precipitation of about 400–700 mm.

Although I am not an expert on the development of pollen-based climate reconstruction techniques, I have read this manuscript with great interest because of the necessity for robust and precise reconstructions of past climates. This is a well-structured manuscript and generally clearly written. In my view, however, there are several shortcomings that preclude publication in ‘Climate of the Past’ in its current form.

Main concerns:

1. The authors argue that the comparison of the reconstructed climate parameters with those provided by other reconstruction methods will test the reliability of the results (Lines 67-68). I struggle to understand the logic behind this approach. For example, if the here-reconstructed values are comparable with those provided by other methods, the question that arises is why a new method is needed. If the results are not comparable, then the question that arises is how one can test which reconstructed values are more realistic. In my view, independent (i.e., non-pollen-based) climate reconstructions should be used to check the reliability of the here-reconstructed climate parameters. This aspect needs to be elaborated on in a revised manuscript.
2. The authors consider ‘a priori that the climate reconstructions should explain about 50 % of the variance of the respective reference curves’ (Lines 182-183). If I understand correctly, this threshold value of 50 % is regarded as sufficient to address the human influence on vegetation dynamics. In my view, this is an important point that needs to be explained further. How is this ‘about 50 %’ defined? Is it based on statistical analysis or empirical observations? And how would the reconstructions be affected if this threshold value was higher or lower? Clearly, the human influence on natural vegetation has gradually intensified during the Holocene, and the manuscript does not explain how the new method elaborates on this. As such, the statement that the method ‘helps to reduce the human impact on vegetation during the reconstruction process’ (Line 412) is not fully substantiated.
3. The mean winter temperature reconstructed values (Figure 9a) show almost no variability over the past 9 kyrs. Instead, a quasi-stable temperature of about 10 ^oC is suggested to have prevailed for such a long period of time. Arguably, the method is not sensitive enough to capture changes in temperature, despite the fact that the temperature reconstructions are generally easier than e.g. precipitation reconstructions. I suggest the authors to compare their temperature reconstructed values with other temperature records from the region (also non-pollen-based) and discuss vigorously what the limitations of the method are, and why the here-presented results provide meaningful and reliable climate reconstructions.
4. The mean annual precipitation reconstructions (Figure 9b) mirror the variability in the arboreal pollen %, which in turn they predominantly reflect changes in the Olea % (compare Appendix B). As such, the precipitation reconstructions are misleading because Olea  is closely related to agricultural practices in the Eastern Mediterranean region. On this basis, there is a very strong human component in the reconstructed values that appears to obliterate the natural climate variability. This view is also supported by a close look at the timing of the Cichorioideae % peaks (compare Appendix B), which are also considered indicators of human-induced land use changes. Specifically, the precipitation drops at 4 and 3.2 cal. kyrs BP, which the authors attribute to short-term climate changes related to the Bond events (Lines 371-372), conspicuously coincide with Cichorioideae % peaks. As such, the precipitation reconstructed values may also represent a human-induced signal rather than climate variability. As for the temperature, the precipitation reconstructions provided by this new method should be compared with other precipitation records (also non-pollen-based) and vigorously discussed in a revised manuscript.

Other comments:

Line 7: Unclear phrasing ‘…that map climate variable to biome distributions’.

Line 13: Do you refer to arboreal pollen percentages? Please specify here and throughout the text.

Line 23: Add references.

Lines 44-45: It is unclear what the previously application of the BBM approach on the Lake Kinneret dataset has shown. Please expand the text and explain what is the relevance for this study.

Lines 74-76: What is the relevance of the information on the lake’s characteristics for this study. Please explain or delete.

Lines 86 and 92-95: The Kinneret basin cannot be seen in Figure 1, and by extension, the prevalent climate conditions and vegetation biomes in the study area. As such, Figure 1 has to be redrawn.  

Line 94: The vegetation and climate characteristics of the Saharo-Arabian biome are not presented, despite this biome is discussed in both the ‘results’ and ‘discussion’ sections. Please also explain what is the ‘unspecified biome’ and why it is worth mentioning in the text as long as it not found in the catchment area of Lake Kinneret.  

Lines 155-162: I don’t understand how the use of a 50 years grid (which is defined based on the 51 years average temporal resolution of the pollen record) addresses the ‘full age uncertainties’ (see line 50). How does the new method elaborate on the changing sedimentation rates in the lake over the past 9 kyrs?

Line 194: Please explain what do you mean with ‘specific expert knowledge’ and how this can be used in a quantified manner that is required for the climate reconstructions.  

Lines 210-213: I am not sure if I understand this correctly. Do the authors mean that the method cannot be applied for long time periods that would require changes in the taxa weights? Please explain in more detail in order to make clear to non-experts any limitations of the method (e.g., continuous reconstructions for a whole glacial-interglacial cycle).

Line 328: Explain for non-experts what is ‘C++’ and ‘standard CPU’.

Line 364: Higher than what?

Netzel et al consider a series of developments to the Bayesian Biome Model (BBM) of Schoetzel et al (2006), a Bayesian hierarchical paleoclimate reconstruction approach which incorporates a probabilistic interpretation of mutual climatic range which is applied by assigning taxa to biomes and considering the relative influence of two or three biomes in the fossil assemblage. This model has previously been applied to a series of reconstructions, most recently including Lake Kinneret (Thoma, 2017). The authors identify a series of weaknesses in the existing approach (which may apply more generally than to only BBM). These can be summarised as neglect of age uncertainty, neglect of effects of human impacts, assumption of fixed spatiotemporal species-climate relationships and the need for user-defined (subjective) decisions in respect of taxa selection, parameter values and choice of model choice. They address these through a series of modifications to the published method.

My initial reaction was that the approach was rather scattergun, addressing a range of different and unrelated reconstruction issues, and that it might be of limited scientific value because it is unclear what it teaches us is needed to progress. Overarchingly, the paper proposes and implements a series of modifications together with a single reconstruction of Lake Kinneret from this revised model which is compared against a published reconstruction on a core from the Dead Sea (Litt et al 2012). For me, demonstrating that these two reconstructions are consistent is not very convincing because it does little besides suggest that the modifications haven’t made things worse, and in fact have made little material difference?

In part this work is an attempt to automate some ad hoc decisions in the interests of reproducibility and ease of use (and quality of reconstructions). But even for this motivation I think a more complete validation is needed to justify choices and additional complexity.

In my opinion the paper should be restructured and expanded to address the question of which, if any, of these modifications are materially useful and how they influence the reconstruction. Firstly, I think the paper should be more clearly set out to identify which modification relates to which weakness e.g. with clearly headed subsections in both the methods and results that relate back to the weaknesses identified in the introduction. More importantly, each modification should be analysed and discussed in isolation, for instance by starting with the baseline model (of Thoma 2017?) and performing a reconstruction with and without that modification. Something like this is needed to isolate and understand the effects of each modification, not only on the reconstructed value but also on the uncertainty associated with the reconstruction. Note that I am deliberately using ‘modification’ and resisting ‘improvement’ because I am not confident this has been demonstrated yet.

Specific points

Section 3.3.2 discusses the age model and compares pollen percentages due to the revised age model, which has the effect of smoothing the signal. Can this plot instead / in addition plot a comparison of reconstructed climate? I suppose the signal must be smoother, but how much, and what are the effects if any on the uncertainty? Smoothing is only useful to the extent the original variability is spurious, can you justify this - why does “strongly fluctuating behaviour of this AP curve indicates an overfitting result”? Bronk Ramsey developed a Bayesian carbon dating approach OxCal which incorporates the constraint that increasing depth implies increasing age, and which provides useful information through the calibration curve because atmospheric C14 varied over time. Could you comment on this, perhaps only in your response if that’s sufficient, my knowledge of this is rather old and perhaps outdated! I would be interested what effect using the Bronk Ramsey approach might have on your age depth profile.

You “specify a priori that the climate reconstructions should explain about 50 % of the variance of the respective reference curves”. This seems a rather ad hoc assumption, could you e.g. explore the sensitivity of the reconstruction to this assumption, perhaps with two extreme (but justifiable) choices?

What effect does the prior have on your reconstruction? Again, a comparison with and without the CRU prior seems appropriate. This is another modification that will presumably smooth your reconstruction, is this smoothing justified? I don’t really understand why, given that climate change/variability is usually the thing of interest, you would want to inhibit that by applying a prior that assumes no change?

A machine learning competition is used which selects the NNET algorithm as that maximises the ‘balanced accuracy’ under cross validation. I would like to see a comparison of the reconstructions from the four approaches. Are they quantitatively distinguishable, i.e. is the additional complexity of SMOTE justified? Are they qualitatively distinguishable, for instance because they behave differently under extrapolation beyond the training set, so that BA is an insufficient metric to decide the “best” model?

I wasn’t clear, is it intended that the ML competition is run on any new data set, or are you concluding NNET is the best model in general for this problem? i.e. is does your algorithm incorporate the competition or does it apply NNET by default?