Early warnings and missed alarms for abrupt monsoon transitions

Thomas, Z. A.; Kwasniok, F.; Boulton, C. A.; Cox, P. M.; Jones, R. T.; Lenton, T. M.; Turney, C. S. M.

doi:https://doi.org/10.5194/cp-11-1621-2015

Articles | Volume 11, issue 12

https://doi.org/10.5194/cp-11-1621-2015

© Author(s) 2015. This work is distributed under
the Creative Commons Attribution 3.0 License.

https://doi.org/10.5194/cp-11-1621-2015

© Author(s) 2015. This work is distributed under
the Creative Commons Attribution 3.0 License.

Articles | Volume 11, issue 12

Research article

|

08 Dec 2015

Research article |

| 08 Dec 2015

Early warnings and missed alarms for abrupt monsoon transitions

Z. A. Thomas, F. Kwasniok, C. A. Boulton, P. M. Cox, R. T. Jones, T. M. Lenton, and C. S. M. Turney

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Final revised paper (published on 08 Dec 2015)
Preprint (discussion started on 13 Apr 2015)

Interactive discussion

Status: closed

AC: Author comment | RC: Referee comment | SC: Short comment | EC: Editor comment

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RC C291: 'Referee comment', Anonymous Referee #1, 28 Apr 2015
- AC C1236: 'Responses to Reviewer #1', Zoe Thomas, 03 Aug 2015
RC C336: 'Review of Thomas et al.', Anonymous Referee #2, 08 May 2015
- AC C1237: 'Responses to Reviewer #2', Zoe Thomas, 03 Aug 2015
RC C444: 'Review of Thomas et al. "early warnings and missed alarms"', Anonymous Referee #3, 21 May 2015
- AC C1238: 'Responses to Reviewer #3', Zoe Thomas, 03 Aug 2015
EC C583: 'Editor comment', Martin Claussen, 09 Jun 2015
AC C1239: 'Response to Editor', Zoe Thomas, 03 Aug 2015

Peer-review completion

AR: Author's response | RR: Referee report | ED: Editor decision

ED: Reconsider after major revisions (03 Aug 2015) by Martin Claussen

AR by Zoe Thomas on behalf of the Authors (03 Aug 2015) Author's response Manuscript

ED: Referee Nomination & Report Request started (03 Aug 2015) by Martin Claussen

RR by Anonymous Referee #3 (18 Aug 2015)

Suggestions for revision or reasons for rejection

2nd Review of "Early warnings and missed alarms for abrupt monsoon transitions" by Z. A. Thomas, F. Kwasniok, C. A. Boulton, P. M. Cox, R. T. Jones, T. M. Lenton, and C. S. M. Turney.

The revised version of the manuscript I find much improved and a lot more convincing. I especially like the revised section two with the separate subsection on assessing significance.

Nonetheless, I still have a few – by now relatively minor – points:

- The discussion of significance of the increases in ACF and VAR for the earlier transitions is much improved, but it still isn't clear immediately why the EWS for all of them are rejected. This would become clearer, if the lines marking the Kendall tau values for the various periods in Fig. 5 were annotated. This way it would become clear, which Kendall tau value is achieved for which transition (though he reader CAN, of course, get this information from Fig. 4), thus making understanding this point more intuitive.

- The discussion of Fig. 9 is still exceedingly brief. Yes, of course it cannot be expected that such a simple model cannot capture the full dynamics of the system, but this is not discussed at all when the figure is discussed (page 18, lines 432 to page 19, line 455). This way the reader is left wondering what conclusions to draw – the simple one being that the potential model is plain wrong. Therefore the figure needs to be better discussed in order to lend credibility to the use of the potential model.

- Line 31: The term “monsoon termination” is highly interesting. Is that standard usage? What is the definition?

- Line 44-46: Future monsoon shifts having societal impacts similar to past monsoon shifts would imply that the vulnerability of society has not changed. There are good reasons for doubting this.

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RR by Anonymous Referee #2 (02 Sep 2015)

Suggestions for revision or reasons for rejection

Review of revised manuscript “Early warnings and missed alarms for abrupt monsoon transitions” by Thomas et al.

Main points of criticism on the first version of this ms concentrated on a lack of critical attitude, lack of explanation on methods, and presentation. All reviewers found the subject matter and analysis interesting. While this revision certainly has improved, I still feel it falls somewhat short of standards for a publication in Climate of the Past. Nevertheless, I still believe the authors should be capable of submitting a version that meets these standards.

Specific comments:
I am not always convinced by the presentation and (lack of) flow of the narrative. At present methodological details are explained before or after the results/figures they apply to. This gives the ms the appearance of a series of disconnected or separate paragraphs. Top some extent this may be a matter of taste but there are several places where this becomes problematic.

1. Figure 1. What are we seeing here? Delta-O18. But what does it mean? Temperature? Precipitation? There is some discussion on Delta-18 2 pages after introducing Fig. 1, but this is insufficient. If the data represent precipitation, the question is what precip? Annual mean? Summer mean? Extreme values? To know this exactly or as good as possible is important as the authors later on mode these timeseries, a.o. with a model based on a Langevin equation. One cannot judge the validity of the model if one does not know what “x” in this model means.
2. The authors defend the Langevin-model by saying it is just a simple skeleton model. This does not mean that assumptions underlying this model should not be discussed and motivated. One assumption is white noise. If we know what x or x-dot means we can discuss how well this assumption is. If eta reflects some precipitation measure it can be valuated from actuo-observations and actuo (climate model) runs. Same for the linear relation between insolation and x-dot. There is a lot written about the relation between hydrological cycle and radiative forcing.
3. In particular, it seems that the amplitude of the noise is chosen by the model or seen as an arbitrary tuning parameter varied in the discussion. The amplitude of the noise determines whether one finds early warning signals or not. Again, the amplitude should and could be constrained by actuo-obs and modeling time series. See also Fig. 11 and subsequent discussion.
4. The authors introduce Type-I and Type_II errors without explaining what they mean. These terms may be common in a small mathematical-statistical expert-group, but this does not extend to the general Climate of the Past readership.
5. One wonders why both 90% and 95% percentiles are used, seemingly at random, for rejecting hypotheses.
6. In Fig. 5 the authors could explain more how the surrogate time series are obtained, what it means if the Kendall low or high for specific subsections of the timeseries and which bar in panels a and b corresponds to which period.
7. The lack of EWS in other subsections of the timeseries than 150-129 ka BP is attributed to a lack of resolution. The possibility of stochastic resonance or noise-induced transitions is not discussed at all. The authors simply “jump” to a conclusion, or even worse, say “we speculate” without addressing other options or motivating their speculation.
8. Figure 10 shows the potential well flattening over a normal transition cycle and a transition cycle at the termination. The distinction between these two is nowhere explained or illustrated. Which cycles do we see? In what respect are they different? Which time period? Please point to the original data!

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RR by Anonymous Referee #1 (06 Sep 2015)

Suggestions for revision or reasons for rejection

In my opinion, the authors have managed to come up with a much clearer and more transparent manuscript. It is now clear to me what the authors do and why: The fundamental question is whether one can distinguish from the speleothem record if the abrupt monsoon switches are associated with bifurcations or with switches between permanent alternative states. The authors point to this question and show that their potential model is in line with the bifurcation hypothesis. In principle, I think that this result just merits a publication because I see no killing argument against it. However, it still remains unclear to me to what extent the author’s results are any evidence for the bifurcation hypothesis in contrast to a sophisticated speculation. I hope that further research will tackle this question more thoroughly, and that the authors still improve their manuscript, by addressing some of the following points.

The authors state that their potential model should “supplement the analysis of the speleothem records and help interpret the results”. I rather think that this model is at the heart of the analysis and that the message of the paper rests on this model. It is thus important to argue why it is an appropriate model, and why alternative explanations (e.g. nonlinear response to forcing, or stochastic resonance) are less plausible, ideally by using statistical tests to refute some hypothesis. The fact that the authors come up with a model that describes the abrupt changes as bifurcations does not prove that the model is more likely to be true than any other model. Although the way the authors derive the model is now transparent, it is not very transparent to me how sensitive the results are to different choices during the model derivation. The fact that a simpler approach fails due to a negative leading coefficient indicates that the model is not robust. I still wonder how robust the results are to the choices during the model derivation. For example, why is the solar forcing a linear term added to the potential U? Why not say that the four parameters of U all depend on time?
The authors do not find “early warnings” though they would be expected if their bifurcation hypothesis was true, and argue that the time series are too short and the noise level is too large for a detection. Is there any further line of evidence to substantiate this claim? How robust is the noise level estimate?
I think it is sensible in this context to check the dependence of “early warnings” on noise level and resolution, using the potential model, as the authors do. However, it is not clear to me whether the results confirm the claim that most transitions are below detectability, while termination II is above detectability. At which length of the record would the signal become significant? I think this is something else than examining the resolution because of the autocorrelation in the time series (see my point on characteristic timescale below).

By the way, just from looking at the data, the time series from Hulu cave does not occur bimodal to me, and the shifts are less abrupt / less permanent. The authors often refer to “the speleothem data”, but I have the impression it is only the Sanbao record they use for their potential model, while they still analyse early warnings in the Hulu record. This seems to be contradictory.

Further (minor) remarks

Another problem that I think remains in the revised manuscript is the lack of a physical mechanism to explain the relaxation time of the system. The authors correctly point out in line 102 that
“Detecting the phenomenon of critical slowing down relies on a timescale separation, whereby the timescale forcing the system is much slower than the timescale of the system’s internal dynamics, which is in turn much longer than the frequency of data sampling the system (Held and Kleinen, 2004).” However, I missed an explanation why this timescale separation applies to the East Asian monsoon (why should monsoon respond much slower to forcing than the resolution of the record, i.e. ~100 years?). Also, this seems to be at odds to the often cited Zickfeld/Levermann/Schewe model which seems to have a much faster timescale given the rapid processes in the atmosphere. I guess it must be the model’s parameters determined by the ocean that somehow adjust slowly to the change in insolation?

line 97: “While it has been theoretically established that autocorrelation and variance should both increase together (Ditlevsen and Johnsen, 2010; Thompson and Sieber, 2011), there are some factors which can negate this, discussed in detail in Dakos et al. (2012b, 2014).”
I still don’t see clearly why this is noted here. What does it tell about the author’s results? Would they expect an increasing variance in case of the monsoon, and why (not)? As autocorrelation and variance do increase together before termination II, where is the problem?

The test for trends in Kendall’s Tau seem to be done via surrogate time series, which I think is a good idea. But it seems that the surrogate time series have no autocorrelation because it is destroyed by the shuffling. The true data is autocorrelated and thus trends are less robust. Wouldn’t the trend significance then be overestimated? The authors refer to Dakos et al. (2008), and the approach seems to correspond to their H0_1 - one could instead use their Null-hypothesis 2 and/or 3, which take autocorrelation into account.

I have the impression the term “tipping point analysis” has been made up by the authors and is very vague. One could instead refer to particular steps in the statistical analysis by using established conventions. Moreover, “noise-induced transition” is not the right term for a random shift of the system into a different attractor basin. As far as I know the term does not refer to one particular event in a stationary time series but to the sudden change of a system’s long-term statistics when the noise level is changed. For example, see books and articles by Berglund, Gentz, Horsthemke and Lefever on this topic.

I still think that some figures are not required, for example
Fig. 1: c, d;
Fig. 6 and 7: c, d.

Fig. 10: I suggest to use individual potential plots, or arrows between potentials and time periods in the record, or write the letter directly next to the line in the plot.

The caption of Fig. 11 is incomprehensible to me.

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ED: Reconsider after major revisions (08 Sep 2015) by Martin Claussen

AR by Zoe Thomas on behalf of the Authors (20 Oct 2015) Manuscript

ED: Reconsider after major revisions (22 Oct 2015) by Martin Claussen

ED: Referee Nomination & Report Request started (23 Oct 2015) by Martin Claussen

RR by Anonymous Referee #2 (11 Nov 2015)

ED: Publish subject to minor revisions (review by Editor) (12 Nov 2015) by Martin Claussen

AR by Zoe Thomas on behalf of the Authors (15 Nov 2015) Author's response Manuscript

ED: Publish as is (16 Nov 2015) by Martin Claussen

AR by Zoe Thomas on behalf of the Authors (16 Nov 2015)

Short summary

Using a combination of speleothem records and model simulations of the East Asian Monsoon over the penultimate glacial cycle, we search for early warning signals of past tipping points. We detect a characteristic slower response to perturbations prior to an abrupt monsoon shift at the glacial termination; however, we do not detect these signals in the preceding shifts. Our results have important implications for detecting tipping points in palaeoclimate records outside glacial terminations.