• 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)
  Doppler imaging.


• 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.

1. 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.


2. 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).


3. 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
   this omission.


4. 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.


5. 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 regularisation, resulting
   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 observational constraints
   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
   for stratifications.
   


6. 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
     enlightening.
   • 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 "The values
     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.


7. 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.
   


8. Citing a paper by Kochukhov et al. (2006) the authors write "... solving a regularized vertical stratification
   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.
   


9. The authors claim "The resulting surface abundance map of Fe is shown in Fig. 1a, and is generally
   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.
   


10. Similarly, one finds " The resulting surface abundance map of Ca is shown in Fig. 4.2, and is generally
    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 "The disappearance
    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 and definitive
    observational constraints for the theoretical models of atomic diffusion" ?
    
    Why has the Fe contrast dropped from 0.67 dex to 0.25 dex ?
    


11. 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?


12. 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) would require
    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.


13. Hopefully very minor: Is Psi as defined in equ. (1) based on all 4 Stokes parameters or on Stokes I only?

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