Peer review of: Intradecadal variations in length of day and their correspondence with geomagnetic jerks (2020)

Reviewers' comments: 
 
Reviewer #1 (Remarks to the Author): 
 
This manuscript describes a two-part wavelet based method to distinguish the time varying character 
of intradecadal length-of-day (LOD) variations. The authors propose that LOD variations show the 
superposition of two periodic signals, one of which is well known, and one of which is new. The latter 
signal is suggested to coincide with occurrences of geomagnetic jerks and is suggested to be excited 
by MHD waves in the outer core, which might produce both the angular momentum changes seen in 
LOD and the magnetic signals of jerks. 
 
I find this to be a well-written article, the method appears sound, and the proposed conclusions would 
potentially be a significant and well-cited contribution to the field. Similar work on the ~6yr period in 
LOD and linking this to geomagnetic jerks has been published as a Nature Letter (Holme and De Viron, 
2013), and works on the dynamic origin of jerks have also been published in Nature (Bloxham et al 
2002) and Nature Geoscience (Aubert and Finlay 2019). 
 
Despite this, I do not support publication of this manuscript in the current form; I think the 
manuscript needs a significant revision to consider the major comments below as this would 
potentially alter the significance of the conclusions. I also attach an annotated manuscript and 
supplement with further, minor comments. 
 
1. There is a failure to cite and discuss a range of literature that cover an important feature of 
geomagnetic jerks that is very relevant here. Discussion of this should be included, and the 
conclusions would be much strengthened if the authors could contribute to clarifying this issue. Three 
strands of this discussion are outlined below for clarity. 
Jerks are generally accepted to be localised expressions at the Earth’s surface, occasionally observed 
over large parts of the globe, which nevertheless do not occur at the same time in all regions of the 
globe, if seen at all in a given region. It is notoriously difficult to define a single “jerk time” from 
observations when many local secular accelerations overlap in time and space. Our ability to time 
jerks accurately and therefore our ability to assess correlations with other phenomena is far from 
certain. This is not discussed in this work and I believe it should be explicitly. It does not necessarily 
take away from the association of LOD and jerks to do so, but it may temper the certainty of the 
conclusions reached in this work. 

Uncited works such as Nagao et al 2003 (JGR), Pinheiro et al 2011 (G3) and Brown et al 2013 (PEPI) 
discuss the issues of determining jerk times, uncertainties on those times, delays in observing jerks at 
the Earth’s surface due to mantle conductivity and the difficulty of pinning down a single global epoch 
at which a jerk occurred. In these works, and others, jerks are somewhat confusingly considered as 
secular variation changes that manifest in <1yr in any given place, but also a single jerk “event” may 
also be considered to be distributed over several years when observations from multiple locations are 
considered. A key point with jerks is that the older literature often considered only the East 
component of the field as seen at ground geomagnetic observatories in their analyses (less external 
field contamination than other components), and therefore present an incomplete view of jerks that 
has retrospectively been fleshed out. 

A second branch of work from authors such as the cited Chulliat (et al 2015, GRL) (and e.g. Soloviev 
et al 2017 (PEPI), Finlay et al 2015 (EPS)), relates to the view of jerks being defined not as observed 
surface secular variation expressions, but as pulses of secular acceleration at the CMB. This view also 
presents jerks as being uncertain in their timing. Soloviev et al 2017 (PEPI) note the uncertainty 
relating magnetic observations at the surface to the pulses at the CMB is likely +/-1yr due to filtering 
through a weakly conducting mantle, plus an uncertainty of 1-2yr on the timing of the peaks of their 
secular acceleration pulses. 

I’d also suggest referring to Gillet’s 2019 Chapter 9 in “Geomagnetism, aeronomy and space weather: 
a journey from the Earth's core to the sun” (Cambridge). There it is argued that timing jerks precisely 
is not possible, and that the apparent pulsing behaviour of the secular acceleration is a result of the 
filtered view we observe of a stochastic process within the core. This would negate any physical 
interpretation of the 6-year periodic signal seen in the magnetic field. 
 
2. There are two references to information being provided in the SI that I do not think is either cited, 
or shown, adequately in the SI: 
a. The processing to derive the decadal LOD variation 
b. The inability of TMWT to resolve two periodic trends as close in frequency as 6yr and 8.6yr 
 
Reviewer #2 (Remarks to the Author):

Please find attached my report on the paper entitled "Intradecadal variations in length-of-day and their correspondence 
with geomagnetic jerks", submitted to Nature Communication by P. Duan and C. Huan.

Review on the paper entitled « Intradecadal variations in length-of-day and their 
correspondence with geomagnetic jerks », submitted to Nature Communication by P. Duan and
C. Huan.


The authors present an analysis of subdecadal length-of-day (LOD) series, based on a normal Morlet 
wavelet transform (NMWT) method. They isolate two signals at 6 and 8.6 yrs, and propose a 
correspondance between extrema of the latter signal and the occurrence of geomagnetic jerks. They 
also discuss potentially important consequences of their analysis, regarding for instance the strength 
of the magnetic field deep in the core, or the predictability of jerks. 

I have several major concerns about this work. First I would ask for additional synthetic tests regarding
the analysis of LOD series. Second there are alternative choices possible for the catalogue of jerks, 
which should be considered. This requires a discussion on the current debate about the existence of 
jerks isolated in time. Finally, some geophysical consequences should be revised. I detail these points 
below, and recommend major revisions for a publication to Nature Communication. 

Major remarks : 
1) additional synthetic tests :
I acknowledge the efforts by the authors to perform synthetic tests. Nevertheless, I wonder if the two 
spectral lines found with the wavelet analysis could still be the consequence of too short series. I raise
this question for two reasons. First in Fig. 1b, there seem to be some drift (in period) of the maximum 
of energy between 6 and 8.6 yr (with some signal around 7 yr too !). Second, a modulated 
monochromatic signal naturally tends to show, if analysed on a short series, several spectral bands. 
This is particularly tricky since the LOD spectrum is red. Long periods may pollute the analysis : this 
effect is considered in the supplementary material, but the synthetic trend considered there (saw-
toothed) might be mis-leading. It indeed contains strong hypotheses, as spectral properties of such 
series is specific and well distinct from that of sine curves.
I thus think the authors should make the following test : 
- generate a AR-2 damped oscillator stochastic series (choosing first a single period at 6 yr, and a
realistic quality factor) ;
- add-it to an AR-1 stochastic process of significantly larger r.m.s. amplitude (e.g. x5), with a decay
time long compared with 6 yr ;
- apply their method on series as long as the available LOD series… is there a single or two spectral
lines that show up ? If more than one, the authors results are doubtful, otherwise the test is not
negative.
This way, the author could furthermore test if they recover the decay rate associated with the « true » 
damped oscillator series. Finally the same test could be performed by considering two damped 
oscillators instead of one.
I also ask these questions since SSA on LOD series cleaned from atmospheric winds and solid tides 
contributions clearly show a 6 yr line, but not the one at 8.5 yr.
Finally, why is this new line not apparent in previous studies implying the authors [8,13 ] ? is it only 
because the spectra were cut in Figures at periods shorter than 8 yrs ? 

2) jerks catalogues :
The authors refer to jerks dated from [6, 23, 24]. There exists two systematic studies of such events 
that the authors shall consider : Brown et al (2013) and Soloviev et al (2017). In the former, more 
frequent jerks are found as data become more accurate, almost filling the entire span at recent 
epochs. In the second, SA pulses (in between jerks) are found at preferred epochs, with 
consequences on the dates of jerks (some being less v-shaped than others). Jerks dates from these 
two studies should be considered when building dans discussing Fig. 4.
Furthermore, there is currently a strong debate on the existence of jerks localized in time, which 
should be recalled in this study. The localization of jerks in time could be the effect of considering 
filtered series (because we cannot separate well internal from external sources). It has some 
implications on the spectra of SV series. Indeed, SA pulses seem to occur at preferred epochs (see 
Soloviev et al), but SV series do not show clear isolated spectral lines at subdecadal periods – see for 
instance to Gillet (2019) and to Lesur et al (2017). The sentence « the above phenomenon… » on p. 6
should be modified accordingly.

3) geophysical consequences :
- The discussion at the end of p. 6 should be strongly rephrased. I do not see why « Fig. 4 also reveals
that the increasing… these jerks ». This whole paragraph seems highly speculative.
- The authors claim (p. 7) that the 6 yr LOD changes is « most likely » excited by an inner core swing. 
This sentence is not correct. This is one possibility among others. The inner core is only responsible 
for a tiny fraction of the angular momentum budget, and the LOD series alone cannot be considered 
as a proof of inner core oscillations. On the other hand, angular momentum associated with TW alone 
explains subdecadal LOD changes, and there is yet no definitive scenario for their triggerring. It may 
be associated with a swing of the inner core, but alternatively Lorentz torques on the the inner core, or
within the bulk, could equally well generate waves travelling from the inner core (see Teed et al 2014 ; 
Gillet al al, 2017).
- The authors claim (p. 8) that a period of 8.6 yrs for torsional waves (TW), instead of 6 yrs, should 
lead to revise down the strength of the magnetic field deep in the core. This is without considering that
the period is not immediately related to the field intensity. Actually this latter is constrained by the 
slowness (integral, along the cylindrical radius, of the inverse of the Alven speed, see Gillet et al, 
2017). This latter defines the waveform, and it is the waveform that leads to the estimate of the field 
intensity in the core by [1]. As a consequence, one cannot follow the argument on a lower field 
intensity.
- Next the authors mention (still on p. 8) that waves in a stratified layer have been « detected » ; this is
not correct. What Chulliat et al (2015) have shown is that one may possibly interprete subdecadal SV 
changes as the signature of such waves. This paragraph is speculative, especially since in such a 
case, associated surface core flows would not explain directly LOD changes anymore – see also the 
recent work by Gastine et al (2019) that does not favor the presence of a stratified layer at the top of 
the outer core. 
- Alternatively, the authors should discuss further the work by Aubert & Finlay (2019), in particular the 
link these authors see between jerks and the acceleration of zonal motions (and thus possible links to 
LOD variations, as in the study by Holme & de Viron, 2013). 
- Finally, the author mention the « obvious » periodicity in jerk occurrence (see p. 9). This statement 
should be softened (see above point 2). They also speculate on the possibility to predict jerks. This 
idea should be further developed in the light of the results by Aubert & Finlay (2019) ; also a 
discussion of the analysis of dynamo simulations by Gillet et al (2019) would be welcome. These 
authors find that a large fraction of rapid SV changes are due to unmodelled SV associated with 
subgrid-scale induction… how predictable are these, if not correlated with large length-scale 
dynamics ?

Minor points : 
- p. 2 : the last sentence seems rather speculative at this stage. It should be removed. There is no 
definitive evidence of a triggerring of TW by oscillations of the inner core.  
- p. 6 : why refer to [22] here ? There exists more accurate references. 
- p 8 : why refer to [29] for the excitation of torsional waves on the inner core ? There are better 
references (e.g. Mound & Buffett, 2006).
- method section : isn’t it an ambiguity when extending with the symmetric series in a case where 
there are 2 sine functions ? I guess that if one is larger than the other it may work, but what happens 
otherwise ? 

references : 
- Aubert & Finlay, Geomagnetic jerks and rapid hydromagnetic waves focusing at Earth’s core
surface, Nature Geoscience 12, 393-398, 2019
- Brown et al, Jerks abound: An analysis of geomagnetic observatory data from 1957 to 2008, Phys. 
Earth Planet. Int. 223, 62-76, 2013
- Chulliat et al, Fast equatorial waves propagating at the top of the Earth's core. Geophys. Res. Lett. 
42(9), 3321-3329, 2015
- Gastine et al, Dynamo-based limit to the extent of a stable layer atop Earth's core, arXiv preprint 
arXiv:1910.05102, 2019
- Gillet et al, Excitation of travelling torsional normal modes in an Earth’s core model, Geophys. J. Int. 
210(3), 1503-1516, 2017
- Gillet, Spatial and temporal changes of the geomagnetic field: insights from forward and inverse core
field models, in Geomagnetism, Aeronomy and Space Weather: a Journey from the Earth’s Core to 
the Sun, 2019
- Gillet et al, A reduced stochastic model of core surface dynamics based on geodynamo simulations. 
Geophys. J. Int. 219(1), 522-539, 2019
- Holme & de Viron, Characterization and implications of intradecadal variations in length of day,  
Nature 499, 202–204, 2013
- Lesur et al, On the frequency spectra of the core magnetic field Gauss coefficients, Phys. Earth 
Planet. Int. 276, 145-158, 2018
- Teed et al, The dynamics and excitation of torsional waves in geodynamo simulations, Geophys. J. 
Int. 196, 724–735, 2014
- Soloviev et al, Detection of secular acceleration pulses from magnetic observatory data, Phys. Earth 
Planet. Int. 270, 128-142, 2017

 
 
Reviewer #3 (Remarks to the Author): 
 
Review of “Intradecadal variations in LOD….” By Duan and Huang 
Reviewer: Richard Holme 
Recommendation: Not acceptable in current form 
 
Note: this review is phrased in a rather personal way. This is not because I am upset that the authors 
are trying to supersede my work – more power to them! – but because what they are doing is 
antithetical to my approach – I seek simplicity, without relying on a duex ex machina from 
complicated maths – and I would argue that my methods achieve a better fit to data. Fundamentally, 
which is correct may not be answerable, although I suggest a test below. 
 
This paper examines the variation in LOD. It is a development of an earlier paper (by me!) which 
argued that intradecadal variation in LOD could be modelled almost entirely by a 5.8 year period 
signal of constant amplitude. Such a model was not a perfect fit – there were clearly jumps ion the 
LOD which can not be fit by a simple harmonic signal – but nonetheless, it explained most of the 
variance. One additional point in that paper is relevant to this work – the longer period decadal 
variation was removed by a smooth curve fit, and this fit was repeated iteratively after subtracting the 
harmonic variation – the variation requires detrending with the long period signal, while the long 
period signal required detrending the oscillation before it is fit. 
 
This paper instead uses various rather more developed techniques (Morlet wavelets, BEPME (which I 
will not write in long form!) ) to attempt to separate the longer period signal, then shows a good fit to 
the residual with wavelet methods, and then fits the wavelet signals with two different harmonic 
signals – one of about 6 year period and 8.6 year signal, the former decaying, the latter growing. The 
authors argue that this model better fits the data. 
 
First I must say that this problem is strongly non-unique – both the earlier formalism and the work in 
this paper are possible fits to the data, and on some level it is not possible to judge which of the two is 
“better”. Where the two methods differ is the differing reliance on complex methods. This paper relies 
on its methodology, and in particular a spectral separation – the background signal is obtained by a 
low pass filter, defining it in terms of its period. This would work if the signal was longer (so more than 
a few periods) or genuinely appeared stationary, but it does not, either at long periods or short 
periods. The remaining shorter periods are then fit very well by the wavelet transform – but this is 
inevitable, as the wavelets have in effect almost a continuum of free parameters. The final argument 
for the growing and decaying exponentials, leading to a 6 parameter fit – two amplitudes two phases, 
two decay rates) does not fit the data particularly closely (see figure 3, and compare with figure S3 
from my earlier paper for a fit with only a 2 parameter system). 
 
What is the necessity of the two different periods? This relates to the removal of a slowly varying 
trend. This trend has sufficient variation that it can covary with the harmonic components solved for 
here. Thus the problem, even as established, is seriously nonunique. In the original paper, I iterated 
between the long-term trend and the oscillation – I removed the oscillation before detrending again, 
and by doing this got a much better fit for a single constant amplitude component. This is not done 
here – the problem can be seen in 1992 where the background trend shows a peak at exactly the 
same time as the 6 year oscillation. The iterative approach allowed this variation to be adjusted by the 
background trend, the approach in this paper requires a low value of the oscillation at this time, which 
is where the mix of the 6 year and 8 year periods comes in – at this point they are out of phase, and 
so the background trend does not need to be altered. To avoid this cancellation happening at other 
times, the growing and decaying exponentials mean that there is not cancellation apart from at this 
one time. 
 
Both papers fit the data, and therefore on some level it is not possible to argue that one is better than 
the other. However, the simplicity of the first paper (a smooth curve combined with a two parameter 
fit) compared with complexity of the second (highly developed spectral methods for which the time 
series may be too short, with a 6 parameter fit that fits the data less well) suggests to my mind that 
this work does not provide an advance in our understanding. Note also that the fit is not perfect in 
either case – this is because the signal being fit is not stationary, and shows jumps (probably due to 
physical processes) – again see figure S3. So having arguments about including higher complexity of 
statistically stationary elements is a bit futile. This argument would need a discussion of how great an 
improvement in fit the more complex model provides, including allowing time variation of the 
background signal – and I would argue that instead the fit is worse. 
 
The big problem is the apparent belief that complicated modelling methods (such as wavelets) will 
solve this problem. Even simple analysis of splitting different frequencies of signals is not robust – it is 
highly likely that there are components of intervening frequencies in both the background signal and 
the oscillation. The methods rely on a (non-stationary) series of (noisy) data, with insufficient length 
to justify complex analysis – and yet the final fit is not as good as the simpler analysis. There is one 
possible test – I note in figure 3, the data end at 2015, so there should be another 4 years of data by 
now to provide a test of just how good a predictive model is provided by the two models. 
 
The discussion of the physical mechanisms does not bring anything new, or anything robust. The 
problem with such a speculative analysis, as I have found to my cost, is that even if qualified (not 
really done here), once it enters the literature, other workers seem to believe it proven and then 
chase off in unjustified directions of work. There is reference to work of Gilet – again this relies on the 
validity of the transform methods and a clear separation between short and long period signal, so at 
least it is good that the two analyses are in agreement. However, I note that the flow analysis that 
Gilet performs ended up with just a 6 year variation – in fairness, long before I got involved in this 
story. 
 
Minor points – 
Reference 6 talks about intradecadal variation, but does not identify the 6 year period as clearly 
separated. This reference needs to appear, but not at the point in the text where it now does. 
 
What AAM series is used? Is there any smoothing of the data after this removal (a running average or 
a low pass filter?)