Dear editor,

here we submit a revision of our paper "Terrestrial planet formation
by torque-driven convergent migration of planetary embryos."

Let us recall we suggest, based on modeling efforts described
in the paper, that the terrestrial planet system practically
formed by a convergent migration of protoplanets in a gas disk.
To support this new model, we identify example disk conditions
where the convergent migration happens and illustrate how things
could work under these conditions. In fact, there are certainly
allowed ranges of parameters and time dependences of relevant
processes. It is just not possible to investigate all possibilities
(in one paper). Nevertheless, we did our best to address all
referees comments.

.
.
.

> From luca.maltagliati@nature.com Thu Aug  6 12:44:28 2020
> Date: Thu, 6 Aug 2020 06:44:24 -0400
> From: luca.maltagliati@nature.com
> To: mira@sirrah.troja.mff.cuni.cz
> Subject: Decision on Nature Astronomy manuscript NATASTRON-19092655A-Z
> 
> 6th August 2020
> 
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> Dear Dr Brož,
> 
> Your manuscript entitled "Terrestrial planet formation by torque-driven
> convergent migration of planetary embryos" has now been seen by 3 referees,
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Foremost, let us thank all 3 reviewers for both positive and negative
comments. We are sorry for the delay, because some of the comments
required additional time-consuming simulations and analyses. We also
added more references, as requested by the referees. Our answers are
appended below. All changes to the manuscript are typeset in bold.

.
.
.

> Reviewers’ comments:
> 
> Reviewer #1 (Comments for the Author):
> 
> In this paper the authors suggest a new way of forming terrestrial planets.
> It is commonly accepted that terrestrial planets form after the protoplanetary
> disk dispersal. This hypothesis offers many advantages, as for example the
> planetary migration problem. In fact, an Earth mass planet forming at 1AU in a
> MMSN has a migration timescale of only 300000 years. On the other hand, N-body
> simulations trying to form the terrestrial planets after disk dispersal are all
> faced, among others, to the problem of the small Mars's mass. A disk of
> planetesimal with an ad-hoc distribution is required to form the "good" Mars.
> 
> Here the authors have the courage of going against the mainstream
> and make a clever use of all the knowledge that has been cumulated to understand
> the migration problem to develop their thesis promoting the formation of
> terrestrial planets during the disk phase.
> 
> Precisely, in a fully radiative model, small planets may migrate outward due to
> thermal torques effects (like the heating torque or the hot trail effect).
> Thermal torques are effective in specific regions (mainly the inner disk). In
> the outer disk the usual Lindblad torque dominates leading to inward migration.
> 
> Results:
> The result is convergent migration of protoplanets at 0.7-1 AU
> with formation of 3-6 terrestrial planets ending on moderately excited orbits
> like in the Solar System.
> 
> Method:
> In the paper a complex 2D hydrocode is performed on short timescales, the
> migration rates as a function of planet mass and orbits are obtained from the
> hydrocode and used for long terms integrations with the N-body symplectic code
> SyMBA.
> 
> Statistic:
> It is explained that dozen of simulations have been performed to provide a
> statistical caracterization of results, however it is not explained how such
> simulations are prepared in the main body of the text. This discussion appears
> on the SI, however it would be interesting to have few sentences on the paper.

Yes, we added information on the initial conditions of our N-body
simulations. For a distinct set of simulations, we keep the distribution
of m, a, e, and I the same, but the angles Omega, omega, M were
set randomly (in the interval 0 to 360 deg). This is sufficient to
create a random geometry of all close encounters between protoplanets.
Consequently, our results show averages (as well as dispersions)
over these stochastic events.

On the other hand, it is not advisable to vary the mass m or the semimajor
axis a randomly, because we want to test the evolution, e.g., of Mars-size
protoplanets. Also, we should be able to distinguish different source
regions (i.e., ranges of a).


> On the overall the paper is clear, few figures well explained are provided to
> support the results, the discussion about the Moon forming event is very
> important and satisfying. In the supplementar material the discussion on
> implications on the asteroid belt is well described as well as on geochemical
> constraints (on this last point I am personnaly not able to judge)

Thank you; we agree that implications for the Moon-forming impact
are important. (It is one of the stochastic events which has to be
treated carefully, because using fully random collision geometries
cannot always lead to the actual Moon-forming impact and to the
observed epsilon_182W anomaly.)


> My principal point of criticism concerns the choice of the disk and particularly
> the viscosity values. I am convinced that viscosity is one of the key parameters
> for all the thermal effects at the basis of outward migration.
> 
> The authors consider viscous disks and they even do not inform about the
> viscosity values on the main body of the text. On the supplementary material it
> is written that the values of alpha viscosity are in the range 0.001 to 0.005
> and a test with a viscous transition is provided.

This is a good point. Our original decision to put the viscosity in the SI
was motivated by the fact that there are likely more values (prescriptions)
which would yield a convergent migration and we did not want to constrain
the value too much.

In the revised manuscript, we now mention the mass transfer rate Mdot
and nu(r) explicitly in the main text (paragraph 3). We also added
a note on the effective alpha value in the caption of Fig. 1.
We agree it is more clear.


> However, these values are quite high: from observations of Alma disks (Rafikov,
> 2017, Ap.J. 837) for example, alpha values have been found to vary a lot from
> one disk to another and to be mainly correlated to the Star accretion rate
> rather than to global disks parameters. This observation is in favour of non
> viscous transport of angular momentum. Magnetohydrodinamical winds could be
> responsible of angular momentum transport for example. The bulk of the disk
> would be non viscous. McNally et al. (MNRAS 493, 2020) study the migration of
> planet in such non viscous disks and consider 3D effects.

Let us recall here, that according to Rafikov (2017), the range of
alpha = 0.04 to 10^-4 -- as inferred from the continuum sub-mm
dust fluxes (and their Eq. (4)). Usually, these observations are
related to spatial scales 10-100 au. In our case, the region of
increased viscosity occurs on a scale <1 au. Consequently, it is
not guaranteed that a comparison of such alpha's is correct.
Nevertheless, our alpha values are well within Rafikov's range. 

Regarding Mdot, the overall range is 10^-10 to 10^-7 M_S --
as inferred from spectroscopy of the central *. Our Mdot value
is 10^-8 M_S, i.e. within the range. (But again, it's related
to ~1 au scale).

The correlation of Mdot vs. alpha is discussed in Sections 4.2,
4.3, 4.4, and 4.5. Apart from non-viscous transport (4.5),
there are also other possibilities: increasing Sigma(r) (4.2),
gas pressure, ionisation fraction, magnetic field strength,
or geometry (4.3), decoupling, instability, or accumulation (4.4).

Consequently, we think that our parameters (Mdot, nu) are not
unusual -- although it may be difficult to compare local/global
quantities as discussed above. In our original manuscript (SI)
we mentioned the previous work of McNally etal. (2018) as an
alternative explanation for the "inverted" surface density profile
and we agree with a possibility that disks might have been inviscid.
We extended our discussion (in par. 3) and added a citation to
Rafikov (2017).


> This part of literature is not included in the discusssion,
> so that the paper is really new concerning the main idea but remains based on
> "classical" disk structure while this domain is rapidly evolving.
> 
> I suggest the author to better explain the context of nowadays disk models , to
> inform about their choice, and to clearly say in which range of values of
> viscosity their work is valid.

To this point, we performed additional simulations with low|high
viscosity values. We tested a value 0.3|3 times the nominal nu,
while keeping r-dependence the same. Mdot was adjusted also as
0.3|3 times nominal Mdot. The rationale is that we need Sigma(r)
to be similar as before, otherwise we would not test the effect
of viscosity, but also of Sigma. At the same time, our profile
is comparable to the MMSN (in the region r > 1 au). It is then
'believable' there were enough solids to create protoplanets
in the first place.

Our results are summarized in a graphical form here:

http://sirrah.troja.mff.cuni.cz/~mira/tmp/fargo_terrestrial_rv1/rv1.html#viscosity

The convergence zone is present for the viscosity values (at 1 au)
in the range ~0.3e14 to 3.3e14 cm^2 s^-1. For smaller values, its
center is located at 1 au for Mercury- and Mars-mass protoplanets,
but it is shifted outwards for Venus- and Earth-masses, mostly due
to the corotation entropy torque. For larger values of nu, the zone
is preserved, although the migration rate da/dt is ~2 times lower
(and corresponding time scale longer).

Regarding the slope s_1 (in the region r < 1 au), the zone is present
in the range ~-1.3 to -3.0. For s_1 = -1, Mercury- and Mars-mass
protoplanets no longer exhibit a convergence. Nevertheless, their
inward migration is sufficiently slow so that after 2-3 merging
events they eventually start to converge. Of course, s_1 < -3.0
would work too, but nu(r) at the inner edge would be too large.

Overall, there is certainly a range of parameters for which
the convergence zone exists. It is actually not needed that
the range is wide, because solar-system-like systems are not
the only ones (cf. super-Earths, mini Neptunes, hot Jupiters).
Moreover, our approach is similar to a 'reverse engineering'
-- we try to determine parameters which lead to a convergent
migration, because this seems required by the architecture
of the terrestrial system.

We added a brief discussion of parameters (in par. 4).

Alternatively, we used alpha(T) parametrisation of viscosity.
However, disks with Zhu opacity law were often unstable (see
Sec. G in SI). We discussed this possibility also with M. Flock
who informed us about similar instabilities in his 3D simulations.
This is indeed an interesting possibility to create an inverted
Sigma(r) profile by 'temporal averaging', but it is certainly
worth of a separate study.


> A second criticism concerns the discussion about gas dispersal.
> The accelerations on planetesimal comes from hydro simulations on the early disk
> (Sigma0=750 g/cm2) and is used for N-body simulations over 1.e7 years. On this
> timescale the disk evolves.
> Clearly it is difficult to take into account how the acceleration on the
> planetesimal evolves with time. This point is addressed by a simulation with
> Sigma0=75 g/cm2 . It seems that the hot-trail effect is still present with a
> pebble accretion flux up to 1.e-4 Me/y. Is this pebble flux possible at very
> late disk phases?

Well, the referee is right -- it is an 'extreme' pebble flux,
sufficient to heat the protoplanets so that the hot-trail effect
is fully developed within the (limited) time span of our simulations
(see, e.g., Fig. 8 in SI). If the flux is, e.g., 10^-5 M_E/yr,
the hot-trail may also develop, albeit more slowly (and it's not
guaranteed). We think it is also possible that protoplanets were
additionally heated by: (i) differentiation (core formation),
(ii) radioactivity; none of which is included in our model.
If true, the forcing of eccentricity may be more efficient.

In order to demonstrate, why the hot-trail effect is important,
we prepared an N-body simulation with no hot-trail forcing (e_hot = 0.0).
Otherwise, our setup remains the same, so that we can do a 1:1 comparison.
This comparison is shown here:

http://sirrah.troja.mff.cuni.cz/~mira/tmp/fargo_terrestrial_rv1/rv1.html#ehot

In particular, resonant captures are much more common (when e -> 0;
see a(t) plot below, with the resonant order denoted by colour).
Consequently, merging of protoplanets is somewhat delayed,
migration is not always convergent for the pairs of protoplanets
and the resulting number planets is relatively larger (5-8 instead
of 4-6). Given the importance of e_hot, we prefer to keep it as
a free parameter in our N-body model, although it may be difficult
to achieve in full hydrodynamical models.

We already commented that in our model '... migrating planets avoid
capture in orbital resonances.' on p. 6. 


> Moreover disks have been observed to be structured in rings that may be due to
> pressure maxima. This would prevent the global radial drift of the pebbles flux.
> Can the authors comment on this point?

The referee is right. We were also 'afraid' that something (e.g., Jupiter,
gaps, pressure bumps) may prevent pebbles from drifting inwards. Actually,
it was a motivation for us to study a formation of terrestrial planets
'as fast as we possibly can'. Conceptually, it is worth to construct
a simplified local model; otherwise, we cannot conclude, whether such
formation is possible or not. Nevertheless, we definitely agree that
external events can change the evolution of the terrestrial system.

We already mention it in the context of water delivery that '... would diminish
if Jupiter and Saturn block the flux of icy pebbles from > 5 au' on p. 8.

Additionally, pressure maxima lead to an accumulation of solids.
These pressure maxima are associated with opacity transitions,
evaporation lines, active/dead zones (Morbidelli etal. 2008, 2016).
In our case of an inverted Sigma(r) profile, it can also lead to
a locally increased surface density of pebbles Sigma_p(r).
Eventually, if a protoplanet migrates towards/into this region,
pebble accretion/heating would be at least temporarily increased
(cf. e_hot above). Alternatively, if pebbles were accumulated
elsewhere, they can be 'released' if Sigma_p > Sigma_g, or earlier
if the streaming instability occurs, if pebbles are fragmented
(Drazkowska etal. 2019), if the peak is spread due to back-reaction
(cf. Kanagawa 2019). Again, it is probably worth of a separate study.


> To conclude, I suggest the author to more clearly provide the range of validity
> of their model in the context of new disk models mainly provided by disk
> observations. Then I consider that the paper has new very interesting ideas and
> worth publication on Nature Astronomy

Thank you again for your comments.

Let us mention that another supporting reference might be Clement etal.
(2020; PSJ), where authors conclude that another dynamical mechanism
is still needed to explain small Mars. (And they do not account for
the Type-I migration of terrestrial planets.)


------------------------------------------------------------------------

> Reviewer #2 (Comments for the Author):
> 
> Review of “Terrestrial planet formation by torque-driven convergent migration of
> planetary embryos” by Broz et al
> 
> 
> This is a really interesting, provocative paper that presents a new model for
> terrestrial planet formation. The code developed by the authors is impressive
> and puts together a lot of different pieces of the puzzle. Their results have
> the potential to explain a number of features of the terrestrial planets and
> inner Solar System.

Thank you.

> I have two significant comments below. If they are addressed clearly then I
> think the paper should be published in Nature Astronomy. I also have a handful
> of more detailed comments.
> 
> 
> Significant comments:
> 
> 1. The general mechanism of concentrating embryos relies on convergent
> migration. This type of convergent migration has been invoked since Lyra et al
> (2010) to attempt to, e.g., accelerate the growth of giant planet cores. Models
> of migrating embryos within evolving disks systematically find that convergence
> zones shift, usually by many au over the course of the disk’s evolution (e.g.,
> Lyra et al 2010, Bitsch et al 2013, 2014, 2015, …). If I understand the authors’
> method correctly (and please correct me if I missed something), their disk does
> not evolve in terms of its surface density. This means that the convergence zone
> for migration in their simulations stays at 1 au, whereas in a true evolving
> disk it should be continually shifting and generally moving inward according to
> the models I’ve seen. This would not be a big problem as long as the convergence
> zone ends up at about 1 au, but it is not at all clear that this should be the
> case. For instance, Izidoro et al (2017) found that even embryos trapped at
> convergence zones ended up migrating inward to become close-in super-Earths
> as the convergence zones shifted inward (and also accounting for corotation
> torque weakening due to planet-planet dynamics -- see Fendyke & Nelson 2013).

Yes, BCs of our 2D hydrodynamic simulations are such that the disk
does not (substantially) evolve. Anyway, the time span (of our s.)
is short compared to the overall disk evolution. We use them to estimate
viable migration rates da/dt and other effects in our N-body simulations. 
Indeed, the convergence zone should end up at ~1 au, otherwise we would
not be able to explain the mass concentration of the terrestrial system.
Using this 'reverse-engineering' argument, we actually admit that
it is not clear, why it should end up right here, but we do not think
it is a problem.

For example, in models of Suzuki etal. (2015), Ogihara etal. (2018),
the evolution is just the opposite -- Sigma(r) is inverted due to
disk winds and its peak (which is close to the convergence radius r_c)
evolves outwards on the time scale of at least several Myr. We think
it is possible that the viscous evolution (as envisaged by Lyra etal.,
Bitsch etal.) occurs together with winds; always depending on the
parameters (e.g., nu, alpha, C_w,0, alpha_phi,z). Consequently,
we do not exclude a possibility that r_c remained around 1 au.
Nevertheless, we admit that r_c was more likely moving somewhere.

We added a note on this issue in paragraph 4 (of the main text).

Let us recall Izidoro et al. (and similar references) use a different
viscous disk model, with the alpha parametrisation and prescribed Mdot
as a function of time, Mdot(t). It also contains a fixed inner cavity,
but at 0.1 au. The problem with this setup might be that it cannot
be straightforwardly applied to the terrestrial system -- it often
leads to an 'overgrowth', i.e., super-Earth planets (see Figs. 2, 5-8
in Izidoro etal. 2019).


> 2. I’m concerned about how the “dissipating disk” setup fits within a broader
> dynamical and cosmochemical context. In simple terms, it seems like water
> accreted from pebbles at this late stage (in a cold disk) would necessarily be
> of non-carbonaceous origin and would therefore not match Earth’s D/H (e.g. Piani
> et al 2015). This is because, without a barrier to the inward drift of
> carbonaceous pebbles (assumed to come from beyond Jupiter; Kruijer et al 2017,
> Desch et al 2018), there should be a range of isotopic characteristics for
> chondrites instead of two distinct classes. This barrier must have been in place
> within ~2 Myr of CAIs, during the window of accretion of chondrite parent
> bodies. I think the issue is how their model can avoid water being accreted
> under these conditions rather than trying to use this as an explanation for the
> origin of such water. As it is, there are a number of other models for water
> delivery (see review by Meech & Raymond 2019) and I don’t see how this
> pebble model can work without resorting to a relatively contrived scenario.

We agree that the D/H constraint is critical. Unfortunately, we do not
have a suitable geochemical model. We do have another one for the
Hf/W system (described in SI Sec. H), but it cannot be easily adapted
to describe D/H, because we do not treat pebbles explicitly (from
their source locations) in our N-body model. Well, in an ideal world,
one should have geochemical models for everything...

Let us recall that typical D/H values of reservoirs are (units 10^-6):

  nebular           20
  SMOW             150
  CC (r > 5 au)    130-180   (Morbidelli etal. 2000)
  NC (r < 5 au)    150-1800  (Piani etal. 2015)
  HTC              300
  JFC              150

where SMOW ... standard mean ocean water, CC ... carbonanceous ch.,
NC ... non-carbonanceous ch., JFC ... Jupiter-family comets (well,
Hartley 2), HTC ... Halley-type comets (a.k.a. Oort-cloud).

The values of D/H reported by Piani etal. for Sermakona ordinary
chondrite (separated to micron-sized pieces) correspond to a mixing
of the CC reservoir (150) with an unidentified D-rich reservoir (1800).
On the other hand, Burkhardt etal. (2019) reports a mixing like:
CC = NC + CAI-like material.

Consequently, we think that's complicated. Of course, one can try
to relate SMOW and one of the reservoirs still existing today, but
what if the D-rich and/or CAI-like reservoirs do not exist anymore?
Nevertheless, we agree with the referee that substantial mixing of
CC and NC reservoirs is 'forbidden' to keep all isotopic anomalies
(Kruijer etal. 2017); although mixing of ~1 %, can be possibly allowed.

--

Let us explain that our order-of-magnitude estimate of water delivery
is not a model; it's only among implications (on p. 8). We included
it because: (i) pebble accretion might have been effective -- or too
effective, exactly as raised by the referee; (ii) disk might have
been cold (T < T_eq), which is not very intuitive. Then depends on
the exact timing/position of the snowline and the barrier(s).

We naively assumed that if the snowline was temporarily below 1 au
and if the barrier is not 100-% effective, even pebbles from the CC
reservoir can be delivered. Even more naively, we envisage that
pebbles may be accumulated beyond Jupiter pressure bump, which
eventually breaks down, when Sigma_p > Sigma_g.

Mixing with the NC reservoir is no longer important, because pebbles
(meteorites) are already solidified, so their isotopic anomalies
remain unaffected. Moreover, the NC reservoir is surely drier than CC
and its contribution to water budget is potentially less important.
Once again, it is probably worth of a separate study.

--

In the original manuscript, we admitted that water delivery by pebbles
was diminished by Jupiter (on p. 8). We added information on the D/H
of SMOW and the respective reservoir.


> Detailed comments
> 
> Ogihara et al (2018, ref 4) is cited as having a different but similar
> mechanism. Their approach is definitely more simplistic and does not include
> pebble accretion or other effects included here. Is it worth a closer comparison
> to determine the key effects?

Well, we think it is, but given the strict word limit...

 
> “Computer simulations … are required to match constraints…” -- This sentence is
> the basis of dozens of papers on terrestrial planet formation and should at
> least cite one or two that go into the details of the constraints (e.g.,
> Chambers 2001, Raymond et al 2009, Izidoro et al 2015, Kaib & Cowan 2015,
> Clement et al 2018…).

Yes, we agree. We already mention classical refs. Wetherill and
Chambers & Wetherill. Because we have 35 references on the list,
one reference was added and we opted for the review by Morbidelli etal. (2012).
(The work by Clement etal. is cited later.)


> When discussing the origin of the inner edge of the supposed annulus at 0.7 AU,
> it’s worth mentioning other models (e.g., Morbidelli et al 2016 suggested a
> fossilized condensation front of silicates). In fact, Raymond et al (2016)
> suggested that outward migration of Jupiter’s core would have removed embryos in
> Mercury’s feeding zone, which has some similarities to the idea presented here
> (albeit much more simplistic).

Ditto. We added the ref. Raymond et al.

 
> Do dynamical torques play a role? They seem to be very strong in certain
> circumstances (Paardekooper 2014, Pierens & Raymond 2016).

Yes, we do not use fixed orbits (static torques) in our hydrodynamical
simulations. The torques thus can be considered dynamical, although
we do not see a runaway dependence on da/dt, but rather on e (i.e.,
the hot-trail effect).


> “Wide annulus” from 0.4-1.8 au… This would not count as “wide” in any modern
> study of terrestrial planet formation. I like the proof of concept simulation
> shown in Fig 5 of the supplement, although the initial conditions (with much
> more massive embryos farther out) are suspect.

Yes, this distribution of masses helps the convergence. We removed "wide".

 
> I didn’t see an explanation for the initial conditions in terms of either the
> embryos’ absolute masses or their radial mass gradient. I know that models of
> planetesimal accretion find a very strong radial gradient in timescale for large
> embryos to form (Walsh & Levison 2016, Deienno et al 2019). But pebble accretion
> would naively predict embryos with slightly-increasing masses at larger radii
> (Morbidelli et al 2015) although this depends sensitively on the disk
> properties. I imagine that this mass distribution must be quite important in
> setting the final configurations of systems.

In this sense, our model is simplistic -- we did not test a wide variety
of mass distributions, because we definitely need Mercury and Mars
as left-overs on the inner/outer edge. Of course, we cannot start
with protoplanets larger than this. On the other hand, according to
radiometry (Dauphas & Pourmand 2011), Mars formed early ((1.8 +- 1.0) Myr
after CAIs), which was a motivation for us to start with Mars-size
protoplanets.

Motivated by the referee, we performed additional sets of simulations;
namely with Mercury-mass protoplanets. Of course, their total mass
must be the same (~2 M_E), otherwise we would not test the effect
of mass distribution, but of the total mass. It is shown here:

http://sirrah.troja.mff.cuni.cz/~mira/tmp/fargo_terrestrial_rv1/rv1.html#mercury

The resulting number of planets is larger (6-9 instead of 4-6),
because the evolution is not yet finished, and there are always
some remaining (small) protoplanets. It would take ~15 Myr to
end up with 4-6. In this sense, the ICs are not so favourable
for a fast formation of the terrestrial system. Alternatively,
the migration rates da/dt have to be ~1.5 times faster to achieve
sufficient convergence, which essentially means even steeper
disk profiles.


> Having a migration convergence zone at ~1 au is clearly the main requirement for
> such a model matching the actual terrestrial planets. Given the different inputs
> into the disk model, what is the range in disk parameters that produces a
> convergence zone in this range (and a divergence zone in the asteroid belt)? .
> Is it possible to map out the realm of plausible disk properties in a simple,
> low-effort way? How are we to reconcile the abundant population of super-Earths
> with this type of thinking?

Yes, this is an important point. We addressed the range of viscosity-related
parameters in our answer to referee #1 -- please, see above.

Regarding the super-Earths and their abundance (although Earth-size planets
suffer from observational biases), a simple answer would be a different disk.
I know it's a bit too general, but one can hardly assume all disks are the
same. For example, Izidoro etal. (2017, 2019) used a disk with inner cavity
at 0.1 au, allowing for inward migration and interaction with the edge,
which naturally creates close-by planets. In this sense, our model is logical,
because we try to create terrestrial planets in a similar way as exoplanets,
which are so abundant.

Another key parameters are: metallicity, pebble flux vs. time, relative
importance of planetesimal growth/pebble accretion/protoplanet merging,
existence/timing of giant planets, their migration history, etc. etc.


> “Significantly larger pebble fluxes sustained over millions of years would lead
> to planet overgrowth (i.e., super Earths formation) ….” Cite Lambrechts et al
> (2019)

Sure, we added this ref.


> Regarding the late, cold disk as the origin of the terrestrial planets’
> eccentricities. First, I find this really interesting, especially that the
> planets also avoid resonant capture – the difference must come from the heating
> torque, which wasn’t included in e.g. Pierens et al (2013)’s study of migration
> of embryos at a convergence zone. When looking in detail, I would naively expect
> the planets still to migrate close to resonance – does that happen in the
> simulations, and is it consistent with the spacing of the terrestrial planets?

Yes, we checked for mutual resonances (up to the 9th order), and plotted
planet positions if the ratio of their mean motions were small integers:

http://sirrah.troja.mff.cuni.cz/~mira/tmp/fargo_terrestrial_rv1/symba11b_reductions3/038/reso.png

Planet are so close together that forced eccentricities and mutual
perturbations do not allow long-term resonant captures. On the other
hand, if eccentricities are damped to 0:

http://sirrah.troja.mff.cuni.cz/~mira/tmp/fargo_terrestrial_rv1/symba11b_reductions3_EHOT0.0/038/reso.png

There are numerous captures in low-order resonances which prevent
convergent migration. (Note: These are the same Figs. we used
in our answer to referee #1.)


> In terms of the orbital eccentricities induced by the hot trail effect, I would
> expect that these conditions would be erased by any later instability (e.g. Roig
> & Nesvorny 2015, Kaib & Chambers 2016) – or even by scattering in the context of
> a top-heavy late veneer (Bottke et al 2010) – do you agree?

Yes, we agree that these 'originally-hot-trail' eccentricities could
be (easily) erased, but... it's quite important to know that such
external perturbations are not needed to explain these eccentricities
and 'everything' can be done in-situ. Especially, when e > 0 of the
terrestrial planets are used as a proof that late instabilities occurred
(Brasser etal. 2010).


> The setup for the late cold phases of the gas disk confuses me. The authors
> invoke a continuing (albeit reduced) pebble flux in a low surface density, cold
> disk. The part that I don’t understand is related to the origin of water. If
> there was a pebble flux at this late time, it should be of inner Solar System
> origin, because Jupiter would presumably already have formed and cut off the
> flux of pebbles from the outer disk (Kruijer et al 2017, 2020). This pebble flux
> argument should hold even if meteorites’ isotopic dichotomy came from structure
> within the disk rather than Jupiter’s growing to the pebble isolation mass
> (Brasser & Mojzsis 2020). However, the D/H of ordinary chondrites does not match
> that of Earth (e.g., Piani et al 2015; McCubbin & Barnes 2020).
> The only way I can imagine this working is if the water came from secondary
> CC-like dust from planetesimals already implanted into the asteroid belt
> during Jupiter and Saturn’s growth (by the mechanism from Raymond & Izidoro
> 2017, Ronnet et al 2018; Kretke et al also, but paper never published to my
> knowledge).

> The last sentence in the paragraph about water delivery during this phase
> seems to acknowledge the technical difficulty in maintaining a carbonaceous
> pebble flux.

[note: yes, it's true]

> I think this thought could be turned on its head: given that ordinary
> chondrite-like water was not accreted in large amounts by the Earth, what
> conditions would be required to avoid a late flux of water from
> non-carbonaceous pebbles?

This is a very interesting discussion. We already discussed D/H above
-- in our answer to referee #2, point "2.". We think that partly
it's caused by the high water content in CC-like material (up to 20 %).
If NC-like (ordinary; not speaking about enstatite) materials are dry,
their contribution to the D/H of ocean water will be diminished.

We also agree the outer main belt contains CC-like material.
If collisions produced dust (or pebbles), it can drift through
the gas disk inwards (to 1 au). Moreover, if the snowline was
at ~3 au and bodies at >3 au can accrete ice, their population
N(>D) was relatively larger, as well as collisions more frequent.


> How does Jupiter’s growth play into the story? It must have affected the disk
> structure and consequent migration map, at least when it underwent runaway gas
> accretion and carved a gap. This would certainly have affected the temperature
> structure of the disk, with implications for migration (I’ve seen talks at
> conferences and abstracts by H. Jang-Condell but I don’t know of any specific
> published papers on this).

Without doubt! This is related to our conceptual comment to referee #1
-- in this study/model, we purposely avoid modelling of Jupiter.
And it's not only because of simplicity. As pointed out by the referee,
it changes the disk profiles, regulates the pebble flux, even its own
migration history can be complex (e.g., Walsh etal. 2011, 'Grand Tack').
It would be difficult to parametrize all possibilities.

Our model can be regarded as 'just-the-opposite-of-the-Grand-Tack'.
We try to explain everything locally. Otherwise, we cannot decide,
whether formation "... by torque-driven convergent migration of
planetary embryos" is possible (or not).


> Regarding the predictions for observations of planet-forming disks, should Solar
> System-like disks be common or uncommon? It’s clear from exoplanet demographics
> that the Solar System’s orbital architecture is unusual (e.g., Raymond, Izidoro
> & Morbidelli 2020), so it’s not clear that most disks should look like the Sun’s
> did. The key question is simply: Why should super-Earths form so frequently if
> any large embryo should migrate quickly to ~1 au? This is a bit of a
> philosophical point but it’s worth thinking about for the broader context.

It is a tough question. If we look at the biases (Petigura etal. 2013):

http://sirrah.troja.mff.cuni.cz/~mira/tmp/fargo_terrestrial_rv1/rv1.html#bias

it seems, there is still a strong bias of Earth-like and
even Jupiter-like planets, mostly due to periods (>200 d).
If 6+-2 % of Sun-like stars harbours Earth-like planets
(200-400 d), it's not uncommon.

Regarding disks, this can be addressed by direct observations.
We disccussed this with Fedele at the 2019 EPSC-DPS meeting in Geneva.
For example, in his work (Fedele etal. 2010), there is a statistics
of fraction-of-*-w.-infrared-excess vs. age-of-its-cluster:

http://sirrah.troja.mff.cuni.cz/~mira/tmp/fargo_terrestrial_rv1/rv1.html#fedele

The interpretation is not straightforward, though. Sometimes,
this dependence is fitted by an exponential, f = exp(-t/tau),
and tau is interpreted as the 'mean' disk age. However, it
does not mean, that old disks do not exist. There is always
a fraction (on abscissa), which is older. Moreover, there are
at least several outliers (eta Cha, TW Hya, NGC 1960),
containing, e.g., 50 % of disks older than 8 Myr (for eta Cha).
Last but not least, field stars are practically not surveyed
-- although they also harbour disks. Consequently, we think
there is no reason, why Sun's disk cannot be one of the outliers.


Thank you very much for very interesting points.

------------------------------------------------------------------------

> Reviewer #3 (Comments for the Author):
> 
> Here is my review of NATASTRON-19092655A-Z by Broz et al. You may identify me to
> the authors.
> 
> This paper describes numerical simulations designed to test a model for the
> formation of the terrestrial planets in which tidal interactions with solar
> nebula gas tend to drive protoplanets toward 1 AU. This convergent migration
> could explain the fact that 90% of the mass in the inner planetary system is now
> contained in a narrow zone, between 0.7 and 1 AU, in the form of Venus and
> Earth.
> 
> The authors use sophisticated hydrodynamical simulations to model the thermal
> and density structure of the nebula in the presence of protoplanets. They
> estimate the resulting tidal torques on the protoplanet orbits, and model these
> effects in an approximate manner in long-term N-body integrations of systems of
> protoplanets. The integrations follow the orbital and collisional evolution of
> systems of protoplanets between 0.4 and 1.8 AU. They also include a crude model
> for planetary growth due to pebble accretion.
>
> The idea that there are convergent zones in protoplanetary disks, where
> protoplanets will accumulate, has been around for a while, although most work
> using this idea has focussed on explaining the nature of extrasolar systems.

Yes, it's true. We asked a question, what disk would be needed
for the Solar System.

> Here, the authors make a reasonably compelling case that a convergence zone
> could explain the puzzling arrangement of mass in the inner Solar System.
>
> However, it is unclear how robust their model is. I get the sense that the
> authors chose particular model parameters to get the scenario to work, athough
> it is hard to say since the paper doesn't describe a parameter survey. The paper
> is also frustratingly opaque regarding what the authors did in some regards, and
> why they made the choices they did.
> 
> On the plus side, the paper would certainly be of interest to many readers. The
> authors' model is worthy of further study, which this paper would probably spur.
> The scenario has two big advantages. Using the authors' own words (page 5):
> ``This new model offers a notable advantage over the previously suggested
> mechanisms of annulus truncation, because: (i) convergent migration confines the
> annulus from both sides, and (ii) Venus and Earth remain within the convergence
> zone, avoiding problems with the radial mass spreading' (I understand what they
> mean by point (ii), but it would be nice if they explained this in more detail
> since it is an important point - other models such as the Grand Tack model have
> struggled with this issue.)

Yes, we expanded the sentence to be clear.
 
> On balance, I believe the paper could be worth publishing, but only after
> substantial revision. I give more specific comments below:
> 
> Specific comments:
> 
> 1) There are major uncertainties about how robust the model is. For example,
> what range of conditions are required for there to be a convergence zone near 1
> AU? Under what circumstances will this zone apply to protoplanets of the right
> mass range? What disk parameters are needed to give suitable migration rates
> (i.e. too fast could prevent the formation of Mercury and Mars analogues; too
> slow could prevent convergent migration) ?What range of pebble fluxes give
> suitable final masses? What effect do the giant planets have on the evolution,
> especially if they migrate?

We agree these are the key points. We are sorry they were not properly
addressed already in the original manuscript, where we focussed on one
disk model (and mentioned MMSN in SI). In practice, we tested a number
of disk models, but we decided not to discuss them (cf. word limit).

In the revised manuscript, we extended this kind of analysis, which is
now hopefully more systematic. The key parameters mentioned by the
referee are the following:

1. viscosity-related
2. pebble flux 
3. Jupiter-related

Ad 1., we addressed them in our answer to referee #1, please see
our answer above. The migration rate da/dt in our hydrodynamical model
is then dependent on nu(r), which determines disk profiles (slopes
alpha, beta, ...) as explained in the main text, and also on
orbital parameters (due to reductions, dynamical torques, e > 0, etc.).

--

Ad 2., we tested pebble fluxes in the range 2e-5 up to 2e-7 M_E/yr
and protoplanets of various masses/sizes in our N-body simulations.
These results are summarized g. here:

https://sirrah.troja.mff.cuni.cz/~mira/tmp/fargo_terrestrial_rv1/rv1.html#mdotp

Briefly, (i) high pebble flux together with Mercury- to Mars-size
protoplanets do not work, because they overgrow. (ii) Similarly,
low flux and low-mass protoplanets (~<2 M_E in total) do not
grow enough. (iii) Numerous lunar-size protoplanets migrate/merge
too slowly; the resulting number of planets is too large.
(iv) Low number of lunar-size protoplanets (~0.1 M_E in total)
growing by pebble accretion (2e-5 M_E/yr) overgrow too, unless
the evolution spans only ~3 Myr. The caveat might be that the
filtering factor for 0.01 M_E is an extrapolation from >0.1 M_E.
(v) A suitable combination thus seems to be ~1 M_E and 2e-6 M_E/yr
to ~2 M_E and 2e-7 M_E/yr, respectively.

Actually, this is already included in the main text (on p. 5:
"For... 2e-6 M_E/yr, the growth is roughly equally contributed
by pebbles and protoplanet mergers.")

--

Ad 3., we agree with the referee that migrating giant planets
are potentially very important. It would be worth to perform
a throughout testing of 'all' migration scenarios. However, we
think it is practically not possible (within one concise paper).

Please, see also our previous comments to referee #2.

To be sure that our model does not break down when we add
external perturbations, we performed a simple test with Jupiter
on a fixed orbit (see the 2nd column):

https://sirrah.troja.mff.cuni.cz/~mira/tmp/fargo_terrestrial_rv1/rv1.html#jupiter

It is evident that Jupiter on its own is not able to perturb
the terrestrial system -- if the evolution is primarily driven
by gradients within the gas disk. Moreover, if the Type-I migration
of Jupiter's core occurred in yet another convergence zone
(Bitsch etal. 2014, Chrenko etal. 2017) and the Type-II migration
is sufficiently slow, the giant planet(s) can be prevented
to migrate all-the-way-inwards.

On the other hand, if Jupiter (1 M_J) migrates inwards and its migration
is smooth (see the 3rd column), resonance sweeping as well as mutual
captures in mean-motion resonances ('trains') are more common. The resulting
terrestrial system seems to be "squeezed", one bigger planet is often
formed, together with several smaller ones. Of course, one can play
with various migration scenarios (Gomes etal. 2005, Morbidelli etal. 2010,
Walsh etal. 2011, Nesvorny 2011, Nesvorny and Morbidelli 2012,
Raymond and Izidoro 2017, ...).

Let us recall that the 'Grand Tack' model (Walsh etal. 2011) --
in which Jupiter and Saturn migrate inwards && outwards and enter
the terrestrial region -- was partly motivated by small Mars.
On contrary, if we explain small Mars locally (by the gradients),
there is, let me say, no need for the 'Grand Tack'...


> 2) On page 5, the authors say they use an inward pebble flux of 2e-6 Earth
> masses per year for the main integrations. This is very low by comparison to
> other studies (1e-4 is more typical). The paper needs to justify why such a low
> value is plausible. As the authors note, a larger flux could lead to the
> formation of super Earths, which we don't see in the Solar System, but we still
> need a reason for why the flux would be so low. One might appeal to pebble
> isolation - ie. once Jupiter's core reaches a certain mass, it will prevent the
> inward flux of pebbles, but this would stop the flow entirely.

Let us explain that we tested a number of different pebble flux
values. The value explicitly mentioned in the main text was
specific, because it corresponds to a half-and-half growth
by pebbles and merging, respectively.

The referee is right that fluxes 1e-4 M_E/yr are used in
the giant planet zone, but there are at least three reasons
why this cannot be true in the terrestrial zone. (i) It is
below the snowline, so that it is substantially depleted
of ice and only dry pebbles remain. (ii) Pebble filtering
by other protoplanets occurs in the outer parts of the disk
(see Broz etal. 2018, Fig. 21). (iii) Solids may have been
deposited/evaporated/fragmented/transported/reprocessed
sequentially, so that they are not created 'instantly'
and this prolonged flux is actually lower.

We consider the planet overgrowth to be a very strong argument.
If the filtering factors (1-5 %) computed by us are correct,
it is not possible to sustain 1e-4 M_E/yr for a long time
(1-0.2 Myr at most).

Regarding the pebble isolation, Jupiter is possibly not 100-%
efficient in blocking _all_ pebbles. If pebbles accumulate at
the pressure bump (as mentioned above), they can also accrete
and fragment, which creates a size distribution, as well as
velocity distribution among pebbles; a part of them is then
dragged with gas past the planet and is eventually reaccreted
(Drazkowska etal. 2019).

 
> 3) Conversely, the authors use a much higher pebble flux (2e-4 ME/y) for a
> second set of integrations designed to study the late stages of disk evolution,
> when the nebula has almost dissipated. Why is this much higher pebble flux at
> late times justified? Other studies usually find the opposite to be true, i.e.
> the pebble flux is smaller at late times. This suggests some fine tuning is
> required to get the scenario to work.

Again, we tested a values "up to" 2e-4 M_E/yr in our hydrodynamics
simulations, i.e., including lower values.

Indeed, with 2e-4 M_E/yr, the evolution of the hot-trial effect
is relatively fast (~10 kyr). Lower values are also possible,
although the hot trail takes longer to develop. For example, if we
use 2e-5 M_E/yr in our hydrodynamical model, we obtain:

https://sirrah.troja.mff.cuni.cz/~mira/tmp/fargo_terrestrial_rv1/5planet_1over10_FLUX2e-5/nbody.orbits.et4.png

It confirms our expectation that the evolution of eccentricity
is similar as for 2e-4 M_E/yr although about 3-4 times slower
because the perturbation of density (by heating) is lower;
we expect the asymptotic value (e =~ 0.020) remains the same
because it is essentially determined by the Lindblad torque reversal
which terminates the hot-trail evolution towards even higher e's.

Please, see also related discussion of additional heating (ref. #1).


> 4) I believe the reason the authors want a high pebble flux at late times is to
> activate the ``hot trail effect' in which heating of protoplanets by pebble
> accretion generates a tidal torque from the surrounding disk gas that excites
> the orbital eccentricities somewhat. The paper says this excitation is necessary
> to avoid capturing protoplanets into resonance chains, which is a common outcome
> in other studies of convergent migration. This raises a possible problem: if the
> hot trail effect is the source of Earth and Venus's current non-circular orbits,
> then pebble accretion must continue as long as the gas disk remains. Otherwise,
> subsequent damping would occur after the flux of pebbles ceases. This is at odds
> with recent models in which Jupiter's formation stops the pebble flux before the
> nebula gas dissipates. The paper should discuss this apparent paradox.

Yes, please, see above.

To this point, we extended the text on p. 6, where we explain
the pebble flux can be non-stationary and there are additional
heat sources.


> 5) More generally, why do the authors appeal to pebble accretion rather than
> conventional growth via planetesimals? Convergent migration would operate in
> either case, and planetesimal close encounters could supply the necessary
> eccentricity excitation.

Yes, this is an interesting idea to combine planetesimals
and a low pebble flux. Of course, models should be as complex
as possible. We use planetesimals neither in the hydrodynamical
nor in the N-body model for simplicity, although it can be done
(cf. SI Eq. (8)). Such a model would be more similar to classical
models. In this paper, we prefer to test whether pebble accretion
and convergent migration can work (or not).


> 6) Page 6: ``Additional changes (in e) may have been inflicted in the
> terrestrial planet system by gravitational perturbations during
> migration/instability of the giant planets26' Typically the problem is the
> opposite: giants tend to overexcite the terrestrial planets, especially once the
> gas has gone. The authors need to think more carefully about the evolution after
> the gas dissipates, and discuss how the orbits of the terrestrial planets may
> evolve as a result. Is it really the case that the current orbits of the
> terrestrial planets had to be established before the gas went away?

Well, a short answer to the last question is "not", but regarding
the over-excitation, we agree. It was actually a motivation for us,
why we tried to construct a model, in which the evolution is generally
less violent (possibly including also the giant planet system).

So, the sentence "Additional changes may have been inflicted...
by gravitational perturbations during migration/instability
of the giant planets^30." was included not because these changes
are needed, but because they are often expected (by other authors).

We added a note on over-excitation (on p. 7, at the end of par.).


> 7) Page 6 ``for t_Moon < 10Myr... the tungsten anomaly in the mantle of Earth
> would be generally higher than the observed value... We therefore prefer our
> simulations with SyMBA that ended with five (or more) terrestrial protoplanets,
> thus leaving space for a late Moon-forming impact and ε182W decrease' This is
> too speculative. The authors should integrate their 5-planet systems forward in
> time, without a disk, to see how often the resulting systems resemble the
> terrestrial planets. This would not take much computing effort (sun + 5
> terrestrial planets + Jupiter and Saturn for a few hundred My). The results
> would potentially strengthen or weaken their hypothesis substantially.

The problem here is that the evolution is way too stochastic.
It is impossible to _always_ match 1 case (i.e., the observed
Solar System) when the resulting value (eps_182W) depends on
a single random event. At best, the mean value will be equal,
but a substantial standard deviation is inevitable. This was
nicely demonstrated by Fischer and Nimmo (2017) -- in their
work, they used 100 N-body simulations, obtained eps_182W
in the range 0-48, but for all ages between 10-175 Myr
one can find a suitable Moon-forming impact with eps_182W =
= 1.9 +- 0.1; especially when equilibration is allowed to vary.

We agree with the referee that such integrations can be done.
Given our experience (see, e.g., Nesvorny and Morbidelli 2012),
we are 'a-priori' sure that varying initial conditions, e.g.,
the mean anomaly of Jupiter, one can 'easily' obtain a suitable
timing (a.w.a. eps_182W); especially when late migration/instability
is invoked. We thus believe that geochemical constraints can be
used as in SI Sec. H.

--

We have several sets of simulation with an exponential decay
of gas (torques) and a smooth transition to a gas-free phase
(see the 2nd column):

https://sirrah.troja.mff.cuni.cz/~mira/tmp/fargo_terrestrial_rv1/rv1.html#gasfree

Qualitatively, the evolution and outcomes are similar to our
previous simulations (with constant gas density), when we use
compatible parameters, of course. In this particular case,
the decay time scale was tau = 5 Myr; the systems were integrated
up to 30 Myr. 

Additionally, we computed a long-term evolution, with Jupiter
and Saturn on fixed/current orbits, over additional 300 Myr
(see the 3rd column). Systems end up with 1-6 terrestrial planets.
Statistics of collisions (for the whole set of 100 simulations)
shows they occur anytime between 10 and 310 Myr, but they are
common until ~60 Myr. They are neither 'forbidden' nor 'enforced'
to happen at exactly 45 Myr (cf. eps_182W), but it confirms
our original expectation.

As for complicated giant-planet migration scenarios, this is a work
in progress (Sandro etal.). If one takes 5 planets (2 half-Earths)
and migration scenario "1" from Roig etal. (2016), a typical instability
is like:

https://sirrah.troja.mff.cuni.cz/~mira/tmp/fargo_terrestrial_rv1/sandro1.jpg
https://sirrah.troja.mff.cuni.cz/~mira/tmp/fargo_terrestrial_rv1/sandro2.jpg

It is not a problem to perturb the terrestrial system. The timing is
dependent on "time zero" and it is not a problem to shift it. (In the
classical Nice model of Gomes etal. 2005, it was postponed until ~700 Myr.)

We extended SI Sec. H with information on long-term integrations.


> 8) Page 7 ``..the innermost part of a viscously heated disk can reach the
> evaporation threshold... of many minerals..' This would not be the case for a
> disk where the evolution is mostly driven by a disk wind because viscous heating
> is largely absent in this case. The authors should discuss how much the thermal
> evolution of the disk depends on their assumed disk model.

Yes, we agree with the referee. Our statement was 'carefully weighed',
so that it is valid for disks which are heated enough. Even so called
'wind-driven' disks (Suzuki etal. 2015, Ogihara etal. 2018) may exhibit
an MRI-active region, which means an increased viscosity. Although
Ogihara's model has a simplified treatment of radiative transfer,
it does contain viscous heating term and the temperature at ~0.4 au
reaches 500-2000 K, depending on parameters.


> 9) Page 7 ``As the temperature decreases in a low-mass, late-stage disk (Figure
> 4), Mercury’s surface could have been enriched in volatiles (e.g., Na, S, K, Cl;
> delivered by pebbles), as needed to explain its large volatile.' I leave
> detailed comments about cosmochemistry to other reviewers, but I have a couple
> of comments here: (i) This scenario doesn't explain why Earth is strongly
> depleted in K for example; and (ii) Why is Mercury apparently enriched in Fe
> overall compared to the other inner planets?

Regarding potassium, let us recall that according to Nittler etal. (2018),
Fig. 2.3, the values of K/Th are as follows:

  Mercury  8000
  Venus    3500
  Earth    2500
  Moon      300
  Mars     5500

We think that a standard explanation for the depletion of Earth (and Moon)
is the giant impact(s), which is compatible with our model, because it can
occur later (after gas dissipation).

We can address the 2nd point, because we already have some preliminary
computations of the deposition sequence with the ArCCoS code (Unterborn
and Panero 2017):

https://sirrah.troja.mff.cuni.cz/~mira/tmp/fargo_terrestrial_rv1/rv1.html#condensation

Assuming the solar composition, Fe 'rains-out' at about 1450 K,
just after CAIs. If pebbles drift towards this evaporation front,
they will be already depleted in other elements. If they evaporate,
Fe vapour will enrich the chemical composition and in turn change
the sequence. According to our tests with an increased Fe abundance,
the Fe/Si ratio is increased substantially, as well as the respective
range of T(r) or r. Finally, if Mercury accreted from material
formed in this region, its Fe/Si is large.

Actually, this is the topic of the 2nd paper (in preparation).


> 10) Pages 9-11 or the supplement: Somewhere, the paper needs to include more
> information about the N-body integrations, e.g how many protoplanets were used
> initially, what were their initial orbits, how did the pebble flux vary as a
> function of time, how were planet-planet collisions modelled. Also, did the
> authors model the transition between the high and low gas-surface-density
> scenarios, or just consider the two cases seoarately with a constant disk in
> each case?

Sorry for being so brief. The number and initial positions of protoplanets
are visible in Figs. 2 and 3 (in the main text). The pebble flux was constant.
Collisions were treated in Symba by monitoring positions and perihelia for
pairs of bodies; if q < R1+R2, they were merged. It is a simplified treatment,
but we are not interested in details (moons formation, ejecta, hit-and-run, ...).

We extended SI Sec. F.

Regarding smooth transitions, there were not treated in the N-body models
presented in the main text. We also used an exponential decay (see above).
Our hydrodynamical models with different Sigma(r) profiles shall be treated
as a sequence of constant disks.


> 11) Supplement, pages 6-7: the turbulent alpha_P parameter used to calculate the
> pebble scale height should be related to the viscosity that causes the disk
> heating. The very low value of alpha_p used here (1e-4) cannot generate the high
> disk temperatures found in this study. This suggests the authors are treating
> these viscosities as separate effects. Please explain why this is justified.
> This problem exists independently of whether or not viscosity is the main driver
> of disk evolution.

Yes, it is true. In our description, alpha_p is an independent parameter.
We do not think it is an a-priori bad thing. It determines the scale height H_p
of the pebble disk and therefore affects the accretion. By definition, H_p <= H.
And usually, H_p << H (Youdin and Lithwick 2007; Fig. 4).

In our disk models, H(r) = 0.010-0.072 au. For comparison, the Hill radius
is r_Hill = 0.004-0.018 au for an 1M_E planet. When H_p < r_Hill, the whole
thickness of the pebble disk contributes to the accretion, which is our case.
Even increasing alpha_p does not decrease \dot M. Consequently, our results
are not very sensitive to this parameter.


> 12) Supplement page 16 and eqn 10: how much do e_hot and i_hot depend on the
> accretion rate of the pebbles? How do they depend on the opacity, temperature
> and density of the disk, or the planet mass etc?

Very interesting possible dependencies, indeed. Surprisingly, e_hot and i_hot
values are likely related to the Lindblad torque reversal (as discussed above),
which scales similarly as the Hill sphere, r_Hill = a (m/(3M))^(1/3). Of course,
if the pebble flux is too low, if the surface density is too low (or too high),
perturbations will be negligible and the hot-trail effect won't develop.
Using our hydrodynamical model, we verified (numerically) that the hot trail
operates at least for 0.5 M_E to Venus-size planets (embedded in disks
assumed in this work).

 
> 13) Supplement page 16, after eqn 10. Why do the authors use the overly
> simplified model for pebble accretion in which all planets grow at the same
> rate? Is this justified? Better models for pebble accretion rates exist and are
> widely used.

In our simplified description, the filtering factor f(M) is different
for individual planets. First, we computed f values for Mercury-,
Mars-, 0.5Earth- and Venus-size planets using our hydrodynamical
model, which contains both Bondi and Hill regimes of accretion
(Chrenko etal. 2017; Eqs. (27)-(34)). Because pebbles are treated
as a continuous fluid (in HD), this way we actually account also
for a slightly decreased pebble flux filtered-out by 'outer'
terrestrial planets.

Anyway, we are interested in 0.05 to 1.0 M_E planets -- for this
narrow range of M our N-body description by means of the f(M)
dependence is sufficient.


> 14) Supplement, page 23, on the depleted asteroid belt. The authors calculate
> that objects in the asteroid belt typically move outwards, away from the
> terrestrial planet region. How robust is this conclusion? Under what
> circumstances would protoplanets in the asteroid belt move into the terrestrial
> planet region, potentially nullifying the scenario presented here?

In SI, we cite Bitsch etal. (2014), who considered the snowline
and its vicinity to be a divergence zone. Its former position
might be somehow reflected in the distribution of S- and C-type
asteroids, but it is uncertain (2-3 au) and it was moving.

Our statement that '... out of 20 protoplanets most of them migrate away,'
does not mean they migrate outwards. It is very well possible that half
migrates inwards. It is not in contradiction with our model. Even though
we assumed the initial positions of protoplanets in the range 0.4-1.8 au,
alternatively, the range could have been 0.4-2.5 au. Of course, the total
mass should not be exceed ~2 M_E.

Regarding the robustness, we think an independent parametric study
would be helpful, but if we use one convergence zone for the
terrestrial planets and another one for the giant planets, as Bitsch etal.,
Pierens etal. (2013) and many other authors, it is inevitable there is
a divergence zone in between them. In this sense, the implication
is very robust.


Thank you very much for numerous very interesting points.

With kind regards, Miroslav Broz, Ondrej Chrenko, David Nesvorny
and Nicolas Dauphas

 
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