Dear Dr Baldini,

Your submission has now been reviewed by 4 selected referees, as well as additional comments provided during open discussion, notably also from Prof Pyle providing insight into volcanic eruptions. The referees, who are all leading experts in their fields, were selected to cover a range of expertise, to ensure a fair review process. There were some severe criticisms of the work, as well as enthusiasm for some aspects. On balance the overall assessment is that this paper needs considerably more thought and work, and thus requires major revision (and will be sent back out to review).

The reviewers have been clear in the issues that need to be dealt with, and in your response you have satisfactorily outlined how this will be dealt with (with some examples of revised text). I urge you to ensure that your revised manuscript comprehensively addresses the points raised. As you have responded, a number of these requests may need to be addressed by future studies.

I would also like to take this opportunity to raise a couple of issues from my own reading of the work (and which resonate with Reviewer 1’s comments), which I hope will improve the paper.

Firstly, a couple of minor points: (a) as pointed out, the existence of MWP-1B is questioned (probably no abrupt jump in sea-level) - Bard et al 2010 Science. (b) Although this may not arise on your revised manuscript, the role of the AMOC in the Little Ice Age (LIA) has been questioned, with the latest reconstructions suggesting that AMOC did not weaken (Rahmstorf et al 2015, Nat. Clim. Change), and the LIA may instead be caused by changes in horizontal subpolar gyre circulation and sea-ice feedbacks (Moreno-Chamarro et al 2017, Clim. Dynamics).

The broader issue with this submission is that it is not providing new data or evidence, but instead is using an updated age model to propose a new hypothesis (albeit one that had been earlier considered and rejected, as discussed). I am not overly concerned about this, since as stated by one of the reviewers, and highlighted by yourself, this is a topic that has perhaps been neglected and it is useful to put this idea out there to be discussed. However, it does mean that the merits of this manuscript depend heavily on it providing an accurate overview of the state of the art regarding the onset of the Younger Dryas (YD). In its current form I do not think the paper does this and there are major omissions in terms of providing the necessary context.

The onset of the YD is associated with the end of the preceding Bolling-Allerod (BA), which is usually considered to be a DO warm event/interstadial. There is a large body of literature that proposes the BA-YD oscillation is simply another DO cycle that occurred as climate passed through an intermediate climate state. Therefore the mechanisms involved for the BA to YD transition may be similar to those acting at the end of earlier DO interstadials. This is consistent with your assertion about the possible role of volcanic eruptions in ending both the BA and earlier DO interstadials. However, the duration of an interstadial has been shown to be dependant on its rate of cooling (ie DO interstadials do not end with random timing, and they occur after a period of gradual cooling). This evidence is difficult to reconcile with the suggestion that a volcanic event triggered the YD/stadial transition, in isolation.

I therefore suggest that you consider a slight modification to your hypothesis, which stresses that climate was probably close to switching back to stadial conditions anyway, and that the occurrence of a volcanic eruption was the (small) trigger that determined the precise timing of the transition (which incidentally may help explain why only some stadials have been linked to volcanic eruptions in your earlier 2015 paper). In the context of the YD, many climate record, especially those around the North Atlantic and linked to the AMOC, show a gradual change (deterioration) in climate through the BA which fits with this generalized evolution of a DO interstadial.

Related to these ideas is the concept that the BA was an overshoot of the AMOC that occurred during termination of the last glacial, such that its demise was inevitable because climate had not yet shifted to an interglacial state where the on mode of AMOC was stable i.e. the BA should be viewed as the event that needs a trigger, and the YD was simply a return to glacial conditions not requiring a trigger (or only a minor one). This framework for the deglaciation is fairly well established, and I think these concepts ought to be included to ensure that the reader has a more complete and accurate context with which to assess the validity of your hypothesis.

Suggested references (by no means an exhaustive list) that deal with these concepts are: Ganopolski and Rahmstorf 2001, Nature; Schulz et al. 2002 GRL, 10.1029/2001GL013277; Sima et al. 2004, EPSL; Knorr & Lohmann 2007 G^3; Liu et al. 2009, Science, DOI: 10.1126/science.1171041; Barker et al. 2010, Nature Geoscience; Thornalley et al. 2011, Science; Buizert & Schmittner 2015 Paleoceanography; Barker et al., 2015, Nature.

Yours sincerely,
David Thornalley

Dear Dr Baldini,

Your revised paper has been seen by myself and 3 reviewers. I am grateful for the changes you have made in light of these comments. The overall assessment is supportive of potential publication of these ideas, however there is still considerable concern about the speculative nature of the ideas, and lack of support from model experiments. As it stands the current version cannot be accepted for publication. However the reviewers (and my own opinion) is that a (minor) revised version would be acceptable if the speculative nature of this idea and the strong need for support from future, relevant modelling experiments were stressed and made prominent in the abstract (and towards the end of the introduction). From an editorial perspective, it is important to ensure new ideas are presented to the community, but at the same time it must be ensured that a causal reader does not take away the message that this paper has proved that the YD was caused by the Laacher See eruption.

I therefore request that you make a number of revisions, in light of the reviewers (and my own) comments:

1) Review 2 (Prof. David Pyle) provides some straight-forward additions. Please implement.

2) Review 3 suggests that a condition for publication should be highlighting, in the abstract, that the volcanic trigger hypothesis needs testing and following up with rigorous modelling studies, similar to what was done for the meltwater hypothesis, since, in its current format, this idea is speculative. I agree with this suggestion. Review 1 makes a similar point, but also adds that the claims need to be toned down and the speculative nature made clear i.e. this idea is, as yet, conjecture. I think both these requests can be dealt with adequately by adding a couple of explicit sentences at the end of the abstract (and also the introduction) that clearly state the speculative/conjectural nature of this idea and the urgent need to test it with relevant, specific modelling studies.

I would also add to this, that I strongly suggest towards the end of the introduction you mention something along the lines of: "A number of studies have suggested that the YD, like DO events, may be caused by internal oscillation of the climate system when it is an intermediate glacial state, such as midway through deglaciation. Yet, external forcing may also play an important role in controlling the precise timing of the transition into the YD and, by itself, external forcing has also been proposed as the underlying trigger for the YD. Here, we suggest that a volcanic eruption trigger (in this case the Laacher See eruption) should be considered as a viable hypothesis for triggering the onset of the YD." This would alert the reader to your later text, at the end of the discussion, where you discuss the possibility of the YD not requiring an abrupt external forcing, and it also provides a more complete synthesis of the state of the art (ie plenty of work negates the need for an abrupt external trigger for the YD (and DO events more generally) - as discussed earlier in the review process.

As stated in the earlier review round, I am concerned about the general validity of a concept that calls exclusively upon external triggers for the YD, and DO events more generally (as is implied at times in your text). This is because there is a strong statistical link between the rate of cooling during preceding DO warm periods (for the YD, the BA) and their duration. This means that the approximate timing of the transition from DO interstadial to stadial is predictable. Theoretical concepts have been put forward to explain this relationship (from Schulz et al 2001 up to Buizert & Schmittner 2015, with many in between). It is relatively simple to incorporate a role for a common external forcing, like certain types of volcanic eruption, into these models, such that the general timing of the transition is determined by the evolving state/stability of components of the climate system, but the precise timing (ie why 100 years earlier not later etc) is affected by the occurrence of eg volcanic eruptions. What is difficult to reconcile would be a more dominant controlling role on the timing of DO stadials by volcanic events and a much more extensive theoretical framework would need to be developed to incorporate all the observations and features of DO events and the YD-BA. The problem is perhaps best put as: "The approximate timing of the end of a DO interstadial is predictable once its rate of cooling is established. If the underlying cause for this transition is invoked to be a volcanic eruption, it logically follows that the approximate timing of the eruption can be predicted. Ie during MIS 3 we could use cooling of DO interstadials to predict when the next major eruption will occur....this would certainly need to be explained/discussed, because it is a very provocative inference"

3) I have a number of other minor comments based on your revised text:

L1280 - Please may I suggest that you reword "The most widely accepted explanation for the YD" to "A common explanation for the YD". A minor change but there are many who do not accept freshwater pulses as the YD trigger. Technically fine as you have it though.

L1618 - You shouldn't rule out all ocean forcing just because AMOC might not weaken during the LIA (note - in addition to Rahmstorf et al 2015 showing no AMOC weakening during LIA, we have also recently shown no AMOC weakening during the LIA - Thornalley et al 2018, Nature). There are many ways the ocean can influence climate other than the AMOC, such as the horizontal subpolar gyre circulation (as pointed out by the earlier suggested reference to Moreno-Chamarro et al 17, which, if you are discussing the LIA, I would still recommend including).

Therefore change text to something along the lines of "related to sea-ice, atmosphere, or ocean changes other than the AMOC".

L1895 - please alter this text because its underlying inference is incorrect: an abrupt cooling does not require an abrupt forcing. The fact that there is gradual cooling and then a switch to a more abrupt cooling at the onset of the YD does not imply that the gradual cooling had one cause, and then the more abrupt stage, another. As shown by many model studies, climate and the AMOC can display non-linear behaviour and tipping points, for which DO events and the BA-YD have been studied in this context. There can be gradual cooling, and then a threshold is crossed in which the climate can shift to another mode of operation. Ocean convection in the North Atlantic - weakening in the Nordic Seas then switching to south of Iceland - in relation to DO events is often thought of as a classic example of this (eg Ganopolski and Rahmstorf 2001 Nature).

L1903 - Your summary of why some terminations do not have a YD needs revising/updating so that it includes the concept that the anomaly in some terminations is not the YD-like events but rather the BA-type events. As described by Cheng et al 2009 (Science), but also in other earlier studies (see Carlson 2008, QSR, and refs therein), some terminations are characterised by a very long (Heinrich) stadial period, and then transition into interglacial. These terminations have strong insolation forcing that is thought to keep AMOC suppressed throughout the deglacial, possibly due to continued meltwater input. Other terminations (eg T1 and 3), where insolation forcing is weaker, enable a brief recovery of AMOC midway through deglaciation, in the form of a transient BA type event.
Therefore, in addition to your speculation that whether a YD events occurs during a termination or not depends on if a volcanic eruption occurs during an intermediate climate state, you should also discuss the widely supported suggestion that the differing terminations are due to the occurrence (or lack) of a BA-type event interrupting the (Heinrich) stadial event that is thought to be integral to a termination (eg Wolff et al 2009 Nat Geo., Barker et al 2010 and 2011).


I would like to thank you once again for your effort in revising this manuscript in light of the reviewer comments. I look forward to seeing your revised manuscript should you be willing and able to make the suggested changes, which I hope enable you to present to the community your hypothesis regarding the role of the Laacher See event in the onset of the YD, but in such a way that is robust and correctly acknowledges the state of the art and competing hypotheses on the YD and the mechanisms of abrupt climate change.

Yours sincerely,
David Thornalley

Dear Dr Baldini,

Thank you for submitting your revised manuscript, and making the changes requested. You have addressed the comments made. However, before acceptance, please can you address a couple of points in the abstract, to keep the changes in line with the requests (and agreed text) of the reviewers:

Please remove the following text that has been added to the abstract after the review process and that has therefore not been seen and agreed upon by any of the reviewers:
“Furthermore, the eruption itself may have resulted from lithospheric unloading associated with the last deglaciation, and therefore similar volcanic forcings may not be spatiotemporally random, but instead may represent an integral part of deglaciation that often leads to YD-type events.”

I would be grateful if you could also please make a minor amendment to the final line of your abstract, to:
“However, future studies should prioritize climate modelling of high latitude volcanism during deglacial boundary conditions in order to test the hypothesis proposed here.”

Thank you for submitting your work to Climate of the Past.

Best wishes,
David Thornalley

Dear Dr Baldini,
Thank you for submitting your revised version and I am happy to accept this manuscript. I appreciate you sending your work to Climate of the Past and thank you for your co-operation during the review process, which involved a wide range of expert reviewers to ensure a fair hearing for this work.
Yours sincerely
David Thornalley