[lectures/latex.git] / posic / publications / sic_prec_reply02.txt

Re: BC11912
    Combined ab initio and classical potential simulation study on the
    silicon carbide precipitation in silicon
    by F. Zirkelbach, B. Stritzker, K. Nordlund, et al.

and

Re: BA11443
    First-principles study of defects in carbon-implanted silicon
    by F. Zirkelbach, B. Stritzker, J. K. N. Lindner, et al.



Dear Dr. Dahal,

thank you for the feedback to our submission.

> We look forward to receiving such a comprehensive manuscript. When you
> resubmit, please include a summary of the changes made, and a detailed
> response to all recommendations and criticisms.

We decided to follow your's and the referee's suggestion to merge the
two manuscripts into a single comprehensive manuscript.

Please find below the summary of changes and a detailed response to
the recommendations of the referee.

Most of the criticism is pasted from the previous review justified by
the accusation that we did ignore or not adequatley answered them.
However, we did comment on every single issue and a more adequate
answer is hindered if the referee does not specify the respective
points of criticism. Thus, some responses are identical to these
included of our previous answer.

Sincerely,

Frank Zirkelbach


--------------- Response to recommendations ----------------

> I am not happy with these two papers for a multitude of reasons,
> and I recommend that the authors rewrite them as a single longer
> paper, to eliminate the criticism of serial publication. I do not
> accept the authors argument that they should be two papers ­ they
> address the same issues, using the same methods. If they were to
> be split into two papers, it would be one for the VASP
> calculations, and one for the MD ­ this is not how I suggest you
> do it, though.

We now combined the two manuscripts into a single comprehensive one.

> do it, though. First, though, the following issues should be
> addressed (some are simply pasted from my previous reviews, where
> I feel that the authors have ignored them, or not responded
> adequately).
>
> 1. I feel that the authors are a bit too convinced by their own
> calculations.  They do not state the error bars that would be
> expected for calculations like this +/- 0.2 eV would be a very
> optimistic estimate, I suggest. That being so, many of their
> conclusions on which structure or migration routes are most
> likely start to look rather less certain.

Although differences of 0.2 eV in DFT calculations would generally be
acknowledged to be insignificant when being compared to experimental
results or data of other ab initio studies, these differences are
considered to be reliable when comparing results, i.e. differences in
energy, of a systematic study among each other. This is commonly done
as can be seen in a great deal of literature, some of which is cited
in the section of the present manuscript that investigates defect
structures and formation energies. Very often differences less than
0.2 eV are obtained and conclusions on the stability of a particular
structure are derived.

> 2. Why is 216 atoms a large enough supercell ­ many defect
> properties are known to converge very slowly with supercell size.
> They appear to be separating defects by as large a distance as
> can be accommodated in the supercell to approximate the isolated
> defects, but then they are only separated by a few lattice
> spacings from a whole array of real and image defects ­ how does
> that compare with taking the energies of each defect in a
> supercell.

Choosing a 216 atom supercell constitutes a tradeoff, of course.
However, it is considered the optimal choice with respect to both,
computing time and accuracy of the results.

The convergence of the formation energies of single defects with
respect to the size of the supercell is ensured. For this reason, they
are referred to as single isolated defects.

It is not our purpose to separate defects by a large distance in order
to approximate the situation of isolated defects. However, we find
that for increasing defect distance configurations appear, which
converge to the energetics of two isolated defects. This is indicated
by the (absolute value of the) binding energy, which is approaching
zero with increasing distance. From this, we conclude a decrease in
interaction, which is already observable for defect separation
distances accessible in our simulations. This is stated now more
clearly in section II of the revised manuscript. (-> Change 6)

Nevertheless, the focus is on closely neighbored, interacting defects
(for which an interaction with their own image is, therefore, supposed
to be negligible, too). At no time, our aim was to investigate single
isolated defect structures and their properties by increasing the
separation distance of two defects belonging to a a defect
combination.

A note is added to let the reader know that convergence with respect
to the system size is ensured. (-> Change 2)

> 3. Constant pressure solves some problems, but creates others ­
> is it really a sensible model of implantation? What differences
> are seen for constant volume calculations (on a few simple
> examples, say)?

In experiment substrate swelling is observed for high-dose carbon
implantation into silicon. Indeed, using the NpT ensemble for
calculations of a single (double) C defect in Si is questionable.
However, only small changes in volume were observed and, thus, it is
assumed that there is no fundamental difference between calculations
in the canonical and isothermal-isobaric ensemble.

Constant volume calculations were not performed and, thus, we cannot
provide concrete differences.

The fact that there are only small changes in volume is added to the
methodology section. (-> Change 3)

> 4. What method do they use to determine migration paths? How can
> they convince us that the calculations cover all possible
> migrations paths ­ that is, the paths they calculate are really
> the lowest energy ones?  This is a major issue ­ there are a
> number of methods used in the literature to address it ­ are the
> authors aware of them? Have they used one of them?

A slightly modified version of the constrained conjugate gradient
relaxation method is used. It is named in the very beginning of the
second part of chapter II and a reference is given. Although, in
general, the method not necessarily unveils the lowest energy
migration path it gives reasonable results for the specific system.
This can be seen for the resulting pathway of C interstitial DB
migration, for which the activation energy perfectly matches
experimental data.

For clarity we added a statement, however, that of course the true
minimum energy path may still be missed. (-> Change 4)

> 5. I have some serious reservations about the methodology
> employed in the MD calculations. The values given for the basic
> stabilities and migration energies in some cases disagree
> radically with those calculated by VASP, which I would argue
> (despite 4 above) to be the more reliable values. The main
> problems is the huge over-estimate of the C interstitial
> migration energy (a process which is at the heart of the
> simulations) using the potential used in the paper. I am not
> convinced that the measures they take to circumvent the problems
> in the method do not introduce further uncertainties, and I would
> need a bit more convincing that the results are actually valid.
> The authors' circumvention of this is to do the simulations at
> much heightened temperatures.  However, this only gives a good
> model of the system if all cohesive and migration energies are
> over-estimated by a similar factor, which is demonstratably
> untrue in this case. For this reason, despite the reputation and
> previous work with Tersoff (and similar) potentials, the results
> need a critical scrutiny, which I am not very convinced by in
> this case.

There is not necessarily a correlation of cohesive energies or defect
formation energies with activation energies for migration. Cohesive
energies are most often well described by the classical potentials
since these are most often used to fit the potential parameters. The
overestimated barriers, however, are due to the short range character
of these potentials, which drop the interaction to zero within the
first and next neighbor distance using a special cut-off function.
Since the total binding energy is 'accommodated' within this short
distance, which according to the universal energy relation would
usually correspond to a much larger distance, unphysical high forces
between two neighbored atoms arise. This is explained in detail in the
study of Mattoni et. al. (Phys. Rev. B 76, 224103 (2007)).

Since most of the defect structures show atomic distances below the
critical distance, for which the cut-off function is taking effect,
the respective formation energies are quite well described, too (at
least they are not necessarily overestimated in the same way).

While the properties of some structures near the equilibrium position
are well described, the above mentioned effects increase for
non-equilibrium structures and dynamics. Thus, for instance, it is not
surprising that short range potentials show overestimated melting
temperatures. This is not only true for the EA but also (to an even
larger extent) for Tersoff potentials, one of the most widely used
classical potentials for the Si/C system. The fact that the melting
temperature is drastically overestimated although the cohesive
energies are nicely reproduced indicates that there is no reason why
the cohesive and formational energies should be overestimated to the
same extent in order to legitimate the increase in temperature to
appropriately consider the overestimated barrier heights for
diffusion.

Indeed, a structural transformation with increasing temperature is
observed, which can be very well explained and correlated to
experimental findings.

The underestimated energy of formation of substitutional C for the EA
potential does not pose a problem in the present context. Since we
deal with a perfect Si crystal and the number of particles is
conserved, the creation of substitutional C is accompanied by the
creation of a Si interstitial.  The formation energies of the
different structures of an additional C atom incorporated into
otherwise perfect Si shows the same ground state, i.e. the C-Si 100 DB
structure, for classical potential as well as ab initio calculations.

The arguments discussed above are now explained in more detail in the
revised version of our work. (-> Change 1, Change 2)