A detailed critique of paper III on
3D mapping of HD 24712
submitted by N. Rusomarov, O. Kochukhov and T. Ryabchikova,
but never published by any scientific journal
There are at least 3 major objections against publication of the paper as it stands:
Nobody would deny that the determination of 3D abundances is a truly important topic and it is of course
- Without published extensive tests which show that the new version of INVERS10 is capable of
recovering 3D abundance distributions of various kinds, including those predicted by theory,
there is no way to assess the reliability of the results. In the past, Vogt et al. (1987) and Kochukhov
& Piskunov (2002) have presented tests which demonstrated that under certain conditions, their
codes recovered the 2D input abundances, a basic and vital step in the establishment of (Zeeman)
- The regularisation function used by the authors is entirely ad-hoc, unphysical and solely motivated
by numerical expediency. It disregards everything we know about diffusion in magnetic stars but
also concerning the movement of charged particles in the magnetic field of the sun. In the past
millennium when diffusion theory was less developed than nowadays, the regularisation function
given by eq.(2) might have constituted a legitimate first assumption, but these times have gone,
eq.(2) is not state-of-the-art, and a more physical approach is both warranted and possible.
- In this paper one encounters an abundance of over-optimistic statements, combined with scarcity
of relevant bibliography and lack of vital information in the plots (Stokes I only instead of IQUV),
accompanied by unforgivably incorrect interpretations of theoretical papers. To fix these, to
provide more comprehensive explanations concerning apparent contradictions with previous
studies, to bring forward detailed arguments in favour of choices made in the analysis. and to
discuss the uncannily tight correlation shown in Fig.4 would require a major effort. It certainly
would cost the authors quite some time to carry out this ambitious program, but their results would
become both credible and useful to the scientific community, something that unfortunately cannot
be said at present.
most laudable that the authors have attempted to attack this long-standing, as yet largely unsolved, problem.
Their effort however is flawed mainly by the fact that in their study they have leapfrogged an essential stage
required to make sure that the results truly reflect the intrinsic properties of the star. In addition, one often
gets the impression that the authors are not prepared to provide more than the faintest of glimpses of their
findings, treating their results and the chain of assumptions leading to them as a kind of trade secret that
must not be divulged. Several of the explicit or implicit assumptions underlying the 3D analysis of HD24712
should either be argued more convincingly or else changed altogether. On the whole, it is certain that a lot
of thought has been spent on numerical issues and on numerical convenience, but one dearly wishes that
equal attention would have been paid to theoretical results and to the question of how (if at all) the modified
ZDI code could possibly recover predicted 3D structures that do not conform at all to the arbitrary maximum
smoothness criterion underlying the present approach.
Let us discuss a number of points in more detail:
Abundance mapping in 3 dimensions is needed for a better understanding of magnetic Ap stars and the authors
- When Vogt et al. (1987) presented their Doppler imaging technique they presented tests showing that
the letters on the famous "Vogtstar" could be correctly recovered. Similarly, they demonstrated how a
a star with 7 spots could be reconstructed by means of Doppler imaging. Kochukhov & Piskunov (2002)
presented numerical experiments with their INVERS10 code on a total of 21 pages. One could object
that only 2 cases of horizontal abundance inhomogeneities were considered, based on 1 spot only or
on 3 high-contrast spots, but the tests certainly showed that under such restrictive assumptions, these
spots could be recovered. Nothing of this kind has been done in the present article! The statement
"In this study, we have developed and applied the first method to reconstruct a chemical abundance
distribution in three dimensions in a magnetized stellar atmosphere"
does not speak of tests. This does
not represent sound scientific practice. Unless extensive tests confirm that the modified INVERS10
code is capable of retrieving all kinds of stratification profiles, in particular those predicted by theory,
whether based on equilibrium solutions or on stationary solutions to the time-dependent case, there is
no certainty that the 3D maps derived in this paper correspond even remotely to the intrinsic abundance
distributions in the star.
- It is also sound scientific practice to cite relevant papers and not to give the impression that all the ideas
are copyright of the authors. In their claim
"In this study, we have developed and applied the first method
to reconstruct a chemical abundance distribution in three dimensions in a magnetized stellar atmosphere"
the authors are singularly oblivious of a paper by Lüftinger et al. (2008) to which O.K. and T.R. were co-
authors. It is worthwhile to cite the title of this paper "3D atmospheric structure of the prototypical roAp
star HD 24712 (HR1217)" and also the statement
"For the first time abundance stratification with changing
aspects of the magnetic field could be determined for a star."
The respective Figs. 4 of the 2 papers show
essentially the same result. It would therefore be advisable not only to be more careful with "firsts", but
also to cite a work that predates the present study by 8 years!
Throughout the years theoreticians have pointed out that stratifications depend on the angle of the
magnetic field with respect to the surface normal, implying that ZDI should take this 3D structure into
account. Stift & Alecian (2009) for example wrote "Theoretical arguments are advanced in favor of
abundance profiles that depend on magnetic latitude, even in moderately strong magnetic fields" and
Stift et al. (2011) warned "Keep, however, in mind that this approach is still full of
(it is hoped) acceptable
approximations and that more difficulties are lurking behind the bend: the influence of magnetic fields
on the atmospheric structure, stratification, 2D and 3D stellar atmospheres for latitude- and longitude-
dependent stratifications." When the authors of the present paper say
"For this reason, we decided to
incorporate vertical stratification of chemical elements into our current implementation of magnetic
Doppler imaging" it would only be fair to add the appropriate citation(s).
- The authors appear to be rather reluctant to acknowledge the relevance or even the existence of
theoretical work on diffusion, but they are always ready to ask for more and improved theoretical models.
One finds e.g. the following sentence "A more realistic approach would be to
investigate atomic diffusion
in a time-dependent manner (Alecian et al. 2011)" and wonders why papers by Stift et al. (2013) and in
particular by Stift & Alecian (2016) which present extensive time-dependent diffusion calculations are not
mentioned at all. The latter paper has been available since mid-January 2016, so there is no excuse for
- Under these circumstances it comes as no surprise that theoretical results are incorrectly interpreted.
The following picture given in section 5 does not correspond to the results presented by Alecian (2015):
"The theoretical diffusion models predict an increase of the effective local abundance
(interpreted as a
“spot”) essentially by formation of overabundance clouds in the upper atmospheric layers. These clouds
occur in the regions of horizontal field lines and are superimposed on a constant vertical abundance
step-like profile." High-lying clouds of rare elements like Hg, Nd, Pt, Y etc. are thought to form in HgMn
stars with very weak magnetic fields (< 100G). This
does not apply to magnetic Ap stars with kG fields.
- Not reading and not citing parts of the relevant literature has led to the adoption by the authors of a
regularisation functional that is entirely incompatible with all available theoretical results on diffusion
in magnetic atmospheres. Strangely enough, the authors did not even take the conjectures of Lüftinger
et al. (2008) into consideration (remember that O.K. and T.R. were co-authors to this paper) which read
"High-resolution spectroscopic data enabled us to trace the changing vertical structure
of Fe within the
atmosphere of HD 24712 also with changing aspects of the magnetic field -- either the field strength, or,
more likely -- the magnetic field geometry."
Diffusion theory, whether time-dependent or equilibrium, does not predict smooth solutions, quite on the
contrary stratifications increase strongly for almost horizontal fields as stated repeatedly in the past, e.g.
by Alecian & Stift (2010), and recently by Alecian (2015) and by Stift & Alecian (2016). Had the authors
read the latter paper on "Time-dependent atomic diffusion in magnetic ApBp stars", they would unavoidably
have stumbled upon Fig.5 which shows the abundances at 2 different optical depths as a function of magnetic
field angle relative to the surface normal in a dipole field of 1950G at the magnetic pole. Table 1 allows the
transformation from magnetic field angle to magnetic latitude, revealing a change of about 1.3 dex between
5 and 25 degrees latitude in the higher layer, but of only 0.5 dex between 25 and 90 degrees. In the deeper
layer, the changes go from 1.0 dex to 0.4 dex, making it clear that abundances depend very non-linearly on
the field angle, but also on the optical depth.
It is a deplorable fact that not a single of the terms in equ. (2) takes into account these well-known effects
of the magnetic field, rather this particular regularisation functional attempts to iron out any field angle
dependence by looking for maximum smoothness only. This special regularisation ensures that the chance
of recovering field-dependent stratifications is practically zero. The claim advanced by the authors
"The uniqueness and stability of the inversions is achieved by applying Tikhonov
in the smoothest possible solution that fits the observations" is therefore at the same time formally
correct, profoundly unphysical and completely misleading. The solution is certainly the smoothest
possible and mathematically this adopted particular regularisation functional leads to some kind of
"uniqueness", it does however not reflect the physical reality in the star. Correspondingly, the authors
fail to (cannot) provide physical arguments in favour of equ.(2), something that is intolerable in the context
of a paper that professes the intention to provide "comprehensive and definitive
for the theoretical models of atomic diffusion."
Only the introduction of physical constraints could possibly remove the indeterminacy of the ill-posed
inverse problem, a kind of approach strongly advocated by Donati in 2001 at the conference on "Magnetic
Fields Across the Hertzsprung-Russell Diagram". Donati surmised that irrespective of the regularisation
function used, data sets with all 4 Stokes parameters did not necessarily contain enough information on
the field to accurately recover the magnetic distribution, even in simple cases. The same must hold true
- The authors claim
"For Fe we discovered a strong correlation between the surface abundance from
2D-MDI and vertical stratification: higher surface abundance corresponds to a wider transition region
that occurs higher in the atmosphere and vice versa." This statement elicits several questions:
- According to which criterion has the handful of stratification profiles plotted in
Fig.4 been chosen?
The authors simply say "We plot a sample of these stratification profiles"
which is not particularly
- Are all stratification profiles for a given "effective local surface abundance"
identical to within
0.01 dex as suggested for the restricted sample plotted in Fig.4, or do they scatter? What is the
scatter for -5.07, -5.19 and -5.32 surface abundance ?
- Can it be excluded that the said correlation is an artefact of the two Tikhonov algorithms used for
the 2D and the 3D analysis respectively? Depending on the choice of the sample taken for Fig.4
and the regularisation functional given by equ.(2) it seems difficult to exclude a priori that such a
spurious correlation should turn up. It must be the relative sizes of the 5 Lambdas in equ.(2) that
determine the 3D solution and it is highly unsatisfactory that the authors simply write
of the regularisation parameters Lambda are determined on the basis of a balance between the
goodness of fit and smoothness of solution".
One is entitled to expect a more physically based
and quantitative approach to this problem, always keeping in mind that a change in the value of
the one single regularisation parameter in the 2D analysis has led to a Ca contrast in 2016 that
is just 16% of the 2015 contrast !
- Let us put it slightly differently. What makes the authors so confident that a
relation on the
0.01 dex level between 3D stratification profiles and 2D abundances assumed to stay constant
throughout the atmosphere reflects the true nature of the atmospheric structure of HD24712?
When a (moderate?) change in the regularisation parameter used in the 2D analysis leads to
completely different Fe and Ca maps (for more questions see below), the correlation shown in
Fig. 4 fills the reader with endless wonder concerning the successful fine tuning of altogether
6 parameters. We are in dire need for a convincing explanation of this phenomenon.
- What is the physical meaning of the assumption of a linear change of abundance with column
mass in the transition zone? Theory does not predict any linear change of abundance with
either column mass, optical depth tau_5000, Rosseland depth tau_R or geometrical height.
If this is just another ad-hoc assumption, it should be openly declared as such.
- The authors certainly cannot be accused of false modesty when they write "This enables
us to study
chemical inhomogeneities in three spatial directions, providing comprehensive and definitive observational
constraints for the theoretical models of atomic diffusion and its interplay with global magnetic fields in
the atmospheres of Ap stars" when at the same time not even the 2D maps for Ca and Fe determined
by Rusomarov et al. (2015) have proved "definitive" and the effect of the magnetic field is not taken into
account in the regularisation function. In a similar vein, the authors claim "In the present
work we perform
the first ever self-consistent reconstructions of the vertical and horizontal abundance inhomogeneities, ..."
although this self-consistency does not go much further than what had been done by Shulyak et al. (2009).
It has to be made clear in the article that as long as any influence of the magnetic field is suppressed in
the ZDI algorithm, one cannot speak of a really self-consistent model.
- Citing a paper by Kochukhov et al. (2006) the authors write "... solving a regularized
problem which recovers the vertical abundance distribution of a chemical element without making any
assumptions about the shape of the vertical distribution ..." which simply is not correct. The assumptions
made in the VIP approach are in effect extremely restrictive and unphysical. Fig. 3a of the 2006 paper and
Fig. 2 of Ryabchikova (2008) clearly show that the profiles converge to the same abundance value deep
in the atmosphere and in the outermost layers, and simply deviate from this value in some intermediate
zone, in complete contradiction with the entire bulk of theoretical results published so far by LeBlanc
and coworkers and by Alecian and coworkers. For these reasons, the said 2006 paper must not be cited.
- The authors claim "The resulting surface abundance map of Fe is shown in Fig. 1a, and
compatible with the abundance map presented in paper II." This statement must remain a puzzle. At
phases 0.80, 0.00 and 0.20 there is not the slightest resemblance between the 2 sets of maps. The
equatorial spot visible at phases 0.40 and 0.60 in paper II splits into 2 quite different structures in
paper III. The conspicuous depletion around the south pole has disappeared.
In addition one reads "Fe shows a relatively simple horizontal structure with a small
gradient over the
surface and the minimum abundance approximately coinciding with the positive magnetic pole of the star".
Looking however just at phase 0.0, the magnetic
pole lies at 1/4 of the disc from the bottom, the centre of
the minimum abundance region lies slightly above 1/2 of the disc, stretching the meaning of "approximate"
definitely beyond its usual limits.
- Similarly, one finds " The resulting surface abundance map of Ca is shown in Fig. 4.2, and
compatible with the abundance map from paper II." As before, there is little if any resemblance to be
detected between the 2 sets. Isopleths which are horizontal at phases 0.00, 0.40. 0.60 and 0.80 in paper I
suddenly run vertically in paper II, the (marginally) strong spot in paper II infringes substantially on the
depleted spot in paper I.
It is not acceptable that the authors treat the differences in contrast between the 2 sets
of Ca maps,
0.26 dex vs. 1.70 dex (!), in such a nonchalant manner: "The discrepancy between
the lower abundance
limits could be easily explained by our choice of the regularisation parameter" and
of this patch in the current work could be explained by an increased abundance regularisation parameter
and the expanded line list." This is a problem
of the utmost importance that has to be treated in an
orderly, scientifically sound way. If a change in the regularisation parameter (by how much??) can change
the whole map, how can one be
sure to have chosen the correct value and why has this not been achieved
in 2015? If an expanded line list can lead to the disappearance of a spot, what would the necessary number
of lines be that ensures (together with the correct regularisation parameter) "comprehensive
observational constraints for the theoretical models of atomic diffusion" ?
Why has the Fe contrast dropped from 0.67 dex to 0.25 dex ?
- Old (2015) and new (2016) profiles are unnecessarily difficult to compare, Stokes QUV profiles are missing
altogether. In paper II, Stokes IQUV profiles have been shown for all the lines (Na, Fe, Nd) used in the
inversions. Fits to the Stokes Q profiles have been quite poor for a number of lines, in particular the 3 Nd
lines where predicted amplitudes at a given phase might reach 1/2 only of the observed amplitudes. Similarly,
predicted Stokes Q profiles for some Fe lines can range between 50% and 140% of the observed values.
This seems to point at inaccuracies in the magnetic maps. In Fig. 3 of paper III only Stokes I is shown. That
does not allow the reader to judge for himself the quality of the fits to all 4 Stokes parameters and to assess
whether the assumption that the magnetic field determined in paper II can be used for further 3D analysis of
abundances in paper III is indeed justified.
How do the IQUV profiles based on the new 2D maps compare to the IQUV profiles based on the old 2D maps?
This should at least be done for the 6 lines in common. The old profiles of 5198.711, 6137.69, 6336.82 are
(much) better than the new ones, the others of comparable quality. Fig. 8 in paper II is almost optimum, Fig. 3
an unmitigated disaster: bad scale, comparison difficult, lines too thick. This figure should be plotted exactly
as in in paper II. It is disturbing to see 50% of the fits worsen, is there a satisfactory explanation?
- A not so minor point: Figs. 4 and 8 have tau_R as x-axis, although elsewhere in the paper one finds tau_5000
throughout. Comparison with the results of Shulyak et al. (2009) and of Lüftinger et al. (2008)
tau_5000 and so does line synthesis. On the other hand the abundances in the transition regions have been
assumed to change linearly with the log of the column mass. So what do the authors want to convey by using
tau_R ? It simply does not make sense : fellow scientists must have the possibility to carry out independent
checks of scientific results and for this purpose plots should use meaningful units.
- Hopefully very minor: Is Psi as defined in equ. (1) based on all 4 Stokes parameters or on
Stokes I only?
seem to have successfully implemented an algorithm for this purpose. However, there is no physical basis to
the regularisation function used in their algorithm, and without extensive tests of this algorithm similar to what
Vogt et al. did in 1987, and Kochukhov & Piskunov in 2002, the present results are of no value. 3D tests would
have to take into account (among others) the dependence of the stratifications on the magnetic field angle,
for which an entirely new kind of regularisation would have to be formulated, the present one being at variance
with all theoretical work since the 1970s and also with our accumulated knowledge of solar magnetic fields.
At the end of their paper, the authors write: "Based on the methodology presented
in this paper, future Doppler
imaging studies should investigate three-dimensional abundance distribution for a large sample of Ap stars
encompassing a wide range of field geometries and stellar parameters."
The sobering experience of the rejection
of their paper by A&A (and perhaps by other journals too) must however have convinced them not to pursue
this endeavour. Realising finally the starkly unphysical nature of their regularisation functional, they seem to
have quietly closed this chapter of ZDI.
Back to the Ada in Astrophysics