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					                                                   Dr. James R. Watson
                                                   Atmospheric and Oceanic Sciences
                                                   Princeton University
                                                   Princeton, New Jersey, 08544, USA
                                                   E-mail : jrwatson@princeton.edu

                                                   23 January 2012

Dr. Ruth Shaw
The American Naturalist

Dear Dr. Shaw

Thank you very much for coordinating the review of our manuscript “Changing
seascapes, stochastic connectivity and marine metapopulation dynamics” (Manuscript
53367). We found the reviewer's comments extremely helpful and we have incorporated
their points into our paper. We believe the paper is better for it.

The reviewers brought up two main concerns. First, there was confusion over why we
used the fecundity (f) to change the strength of density dependence. We have
addressed this in the paper. Essentially, we did not communicate clearly what we were
doing. When we change f there is a concurrent change in beta (the parameter controlling
the strength of density dependence). This happens because the carrying capacity (K) is
constant across simulations, and beta is solved for analytically as we change f. For
example if we increased f, there would be more dispersing larvae. In order to maintain
the same carrying capacity there needs to be a higher level of density dependence,
which is done by changing beta. We have reworded a large portion of our methods to
make this point clearer.

Second, there was concern over the language we used and the extent to which our
discussion linked our theoretical work with biological situations. Following the reviewer’s
suggestions we have expanded our discussion and added to several other areas. We
did this while maintaining the same page length, managing to do so mostly because we
combined two figures and tightened up the equations.

We found the minor comments that the reviewers’ provided all to be extremely useful
and have incorporated them into our revised manuscript. We have attached detailed
replies to the reviewer’s comments below. Thanks to these we believe that the revised
manuscript is improved and we look forward to your further comments.

                                             Yours sincerely,

                                             James R. Watson
Detailed replies to the reviewer’s comments; the reviewer’s comments are in RED and
our replies are in BLACK.

Replies to the Editor - Ruth Shaw
l.11: growth rates when rare (also, later, 'metapopulation growth rates when rare').
These phrases do not make clear what is rare, the demes? individuals within demes?. At
the cost of a few more words, even if there are many instances throughout the
manuscript, a preferable wording would be something like: growth rate of the
metapopulation when it is sparse.
Thanks for this note and suggestion; it is hard to create a phrase that is at the same time
short and informative. We use rare simply to describe a situation when abundances
across the whole metapopulation are low. Thus, to make things more clear we have
expanded our phrase to “the metapopulation growth rate when a species is rare”.

l.8: create -> reach
l.10: impacts -> affects
l.28: is comprised of -> comprises
l.30: nature, -> nature;
l.33: which -> that
l.35: different, -> different;
l.36: exists -> exist
l.42: landscapes -> landscape
These comments have all been addressed, with changes made – thank you!

l.43: ecological time-scales: meaning?
We have added more detail to this sentence. Ecological time-scales are those that are
demographically relevant, specifically the life span of an individual.
Replies to the Associate Editor – Ben Bolker
I am going to recommend a minor revision, because the basic results are sound and the
paper is generally in good shape, but the authors should definitely think hard about
taking the opportunity to extend the discussion slightly as suggested by reviewer #2 and
generally emphasize the connections between the biology and the model as suggested
by reviewer #1.
We have made efforts to address both these points, see our replies to the reviewers.

… any display equation that is not explicitly referred to later, and that does not absolutely
require display notation, can be put inline (e.g., definitely eqs. 1-2, possibly eq. 3
(referred to once later), possibly eq. 4 (could be compacted by use of Kronecker delta
notation -- see PDF notes--see the links below).
We have shortened the paper by removing and rearranging the figures and tidied up
some of the equations (e.g. Eq 13 is now inline). Because the paper is shorter we don’t
see it necessary to use the Kronecker delta notation for Eq. 4. Thanks for the suggestion

Figure 4 might be dispensable, because Figure 4b appears to replicate Figure 2b and
there is really no difference in geometry across the subfigures -- just a general trend in
the difference between deterministic and stochastic outcomes ("if a picture isn't worth
1000 words, to hell with it").
Thanks, we have tidied up our figures. Figs. 4 and 5 have been combined (only using
one panel from Fig. 4) reducing our number our figures. Further, Figs. 3 and A4 have
been combined, shortening the appendix.

* Like reviewer 1, I was a bit puzzled by the use of fecundity as a control parameter for
density dependence. More generally, the
non-spatial equivalent of the model used here is:

n*(1-m)+f*n*gamma/(1+beta*n) = n+n*(f*gamma/(1+beta*n)-m)

So at least in the deterministic non-spatial case, f and gamma are inseparable. It might
be useful to spend a little bit more time discussing in a general way how the parameters
control the dynamics: (f*gamma-m) is the intrinsic rate of increase, f*gamma/m is the
per-generation rate of increase (which is irrelevant in deterministic models but important
in stochastic ones); a version of this turnover rate, f/m, also controls the fraction of the
population that disperses at each time step. I believe (haven't re-derived it) that the
intrinsic rate of increase also controls the strength of the gradient toward the equilibrium,
but it does seem odd conceptually to control density-dependence via f -- beta (or
beta/gamma, or some other dimensionless analogue) would be more natural, if it turns
out to make any mathematical sense.
We have expanded on why we used fecundity (f) to change the strength of density
dependence (see second to last paragraph of the Metapopulation Dynamics section).
This confusion came about because we did not make it clear how f affects density
dependence. When changing f we solve for beta (the more usual parameter for changing
DD) given a carrying capacity (K). Thus, this answers Bolker’s and reviewer 1’s
comments – we do vary the strength of density dependence by changing beta; we just
do so indirectly through f. This choice was made because it is easy to conceptualize the
effect of changes in f and its effect on density dependence – e.g. increasing fecundity
produces more larvae, which then requires a higher level of DD in order to maintain the
same carrying capacity (K).

* I have a general issue with the summary statistics quoted for (e.g.) Figure 6 -- the null
hypothesis that the simulation results are unrelated to the approximation results is even
less interesting, and even less worthy of formal hypothesis testing, than many trivial null
hypotheses in ecology, in part because the p-value can be made arbitrarily small by
increasing the number of simulations. The R^2 is slightly more relevant, but as implied
by one reviewer (who commented on the bias in the relationship) it could be very high
even when the approximation-simulation relationship has a non-zero intercept and a
slope different from 1 -- it would probably be best to quote the intercept and slope [or
slope-1] values (measures of bias and relationship between bias and simulation value)
as well as the R^2.
In addition to discussing the bias we have added the slope and intercept values. We
have removed the p-values.

* The authors use the terms "deterministic" and "stochastic" to denote constant and time-
varying scenarios. While I can appreciate that in their particular scenarios they are
indeed comparing time-invariant with time-varying stochastic models, I would encourage
them to be more careful in their terminology -- at the very least, they should briefly
discuss the issues of comparing time-invariant with (1) time-varying deterministic vs. (2)
time-varying stochastic scenarios. (I'm not sure of the answer myself, here: given a
deterministic temporal signal with the same second-order statistics
(variance/covariance/power (cross-) spectrum etc.), I think that most of their discussion
and approximation would still hold, but I haven't studied Tuljapurkar's (e.g.) work
carefully, so I don't know whether subtle differences between deterministic and
stochastic temporal drivers would appear at some point).
This is a good point and we have added a section to the discussion describing the
difference between time-varying stochastic models and time-varying deterministic. Also,
following the advice of the other reviewers we have been more explicit about the nature
of stochastic connectivity and we have talked about deterministic periodic environments
and the tools necessary to investigate them (i.e. Floquet theory). Further, we argue that
for our study species, assuming that potential connectivity is time-varying stochastic and
not deterministic is appropriate. This is because our species spawn once a year, and the
year-to-year variability in ocean currents has been shown to create concomitant
stochasticity in connectivity (see Berkley et al. Eco Lett 2009, Siegel et al. PNAS 2009).
If we were studying a species that spawns continually over a single year then yes, this
could be a time-varying deterministic scenario with dispersal patterns having a seasonal

* Appendix B seems largely irrelevant -- the figures (as stated) are exact replicates of
each other, and of Figure 4b. I strongly suspect that there is an analytic argument
(based on algebra, or on nondimensionalization arguments) that shows that the results
are for precisely (up to numeric error) invariant to changes in f (or K).
Are you going to do the mathematical derivation?
Bolker is right; we have removed Appendix B, as it is not necessary to show these
replicates. We have also expanded the description in the main text, outlining why our
model results are insensitive to changes in the carrying capacity (K). However, we do
not develop an analytic argument. We feel that given the page limits, our numerical
exploration of the insensitivity of changes in K is sufficient.
Replies to comments on manuscript:
Thank you for identifying the typos – all corrected now.

L136 – “Dynamics when abundant”. We have added a sentence in the first paragraph to
clarify this part.

L152 – “without loss of generality”. We have added a sentence describing our
assumption that g’’(E[s_x]) > 0 and that there are no Allee effects.

L153 – Jensen’s inequality. We have made a note about Jensen’s inequality and added
Ruel and Ayres 1999 as a reference.

Figure 1c. Stems were drawn instead of lines because our simulated data is discrete
(monthly), rather than continuous. However, we have changed the figure – we agree
and think it looks better without the stems.

Figure 2. I have added labels to the figure.
Replies to Reviewer #1:

1) Lines 102-103: perhaps clarify that the model assumes reproduction before mortality.
Done, thank you. We have added a sentence at line 95 clarifying this point.

2) Line 96: "At low abundances, density dependence is assumed to be negligible".
We have changed this sentence, it now reads “At low larval abundances density
dependence, either negative or positive, is assumed to be negligible”.

a. This seems like a reasonable assumption for negative density dependence, but
positive density dependence in recruitment at low density is not uncommon for
gregarious species. It would be good to specifically exclude this possibility because the
sign of the second derivative depends on the form of density dependence and because
a Type III function would cause the sign of the second derivative to shift with density,
which can lead to poor Taylor approximations.
This was picked up on by Bolker too. We have modified this sentence, stating that we
assume neither positive or negative density dependence when larval abundances are
low/rare, and that our recruitment function is density independent.

b. It's important to clarify that this density dependence is *from other settlers* and not
from resident adults. Similarly, throughout the ms, growth rate when rare refers to growth
rate when there is no density dependence in settlement - for this model, this doesn't
mean that the species has low abundance, but that there are few settlers to a site. This
is an important distinction. Depending on the mortality rate, there may or may not be
much correspondence between settler density and resident density.
We have changed the sentence to highlight this. It now reads “At low larval abundances
density dependence…”. However, we argue that low densities of settlers will occur when
adult abundances are low, and thus the way we have framed our paper is still valid.

3) In Eqn 4, it would be useful to note (in the text in addition to the equation) that the
connectivity in the x=y case includes both self-recruitment and the survival of adults from
one year to the next, such that surviving adults contribute to the connectivity. This is
important because for many species (including, I suspect, kelp bass and sheephead)
adult mortality is relatively low and, therefore, will stabilize year-to-year variability in
connectivity from x to x. These biological details may seem obvious to the authors, but
details like this help a broader audience to follow along.
We have now stated that adult survivors are included in the Cxx case, and mentioned
that it will affect the variances in the cov matrix defined in Eq. 8.

4) For Equation 8, specify that both x,y and k,l are for all possible subpopulations (x,y,k,l
= 1…no of subpopulations)
Thanks, we’ve added this.

5) Lines 126-129:
a. Discuss what kinds of biological situations would cause tau^2 to be positive or
negative. For example, if one of the sensitivities is positive and one negative, what does
this mean biologically? Does this correspond to movement from a larval source to a
larval sink?
Describe when negative (positive) sensitivities, negative (positive) covariances might
b. How would negative covariances arise? Perhaps from eddy structures that promote
recruitment in one area while diminishing it in another?
Describe why negative covariances might arise.

c. Also, it's important to clearly state that positive covariance means synchronous
recruitment between subpopulations and negative covariance means opposing
recruitment between subpopulations, while zero covariance means no relationship. I
know it seems obvious, but help your readers along here.
We have reworked this paragraph, being more explicit about the meaning of positive and
negative covariances.

d. For self-recruitment, the higher variability *always* leads to larger, positive tau2
because Zxy2 is positive.
We have added this comment.

e. In line 128, the authors state that "positive covariances in subpopulation connections
increase tau2", but this is only true if the sensitivities Zxy and Zkl are both positive or
both negative. If the sensitivities have opposite signs, then positive covariance would
decrease the difference between lambda_1 and lambda_s. I don't see any reason why
sensitivities couldn't have opposite signs, but if this not possible, then please clarify.
Are negative sensitivities possible?
Negative sensitivities are definitely a possibility – if a change in a subpopulation
connection (Cxy) results in a decrease in the deterministic metapopulation growth rate
(lambda_1). We have added a sentence here describing that Tau will only certain
combinations of sensitivities and covariances will reduce metapopulation growth rates:
positive (negative) sensitivities and positive (negative) covariances.

6) Eqn 9: Note that g(sx) is, once again in this section, nonlinear.
We have made it more explicit, detailing in this section that we are talking about the non-
linear, density dependent model.

7) Line 176 and Appendix A: Given the exclusion of locations around Pt Conception and
San Diego by a threshold in potential source strength, why were sites on the backside of
San Nicholas of similar source strength still included? Are these considered "genuinely"
low connectivities rather than low connectivities due to boundary effects?
Edge effects are difficult to quantify and deal with in regional oceanographic models. We
used potential source strength to guide the choice of “interior” patches that have less of
an edge effect, but like the reviewer said there are patches in our model with potential
source strength below that of those omitted (e.g. those on the backside of San
Nicholas). However, our choice to omit patches was also guided by our knowledge of the
underlying oceanography. Patches on the back side of San Nicholas are genuinely low
in connectivity, this is known from their situation in the far west of the Santa Barbara
Channel (where offshore equator ward currents leave them unconnected) and from
previous connectivity work we have made (see Mitarai et al. JGR 2009, Watson et al.
MEPS 2010).

8) Eqn 13: This doesn't add anything.
We have removed Eq. 13 from the paper. We agree – it did not add anything.

9) Lines 201-205: k-means clustering algorithm
a. From the description of the methods, it sounds like the number of clusters weren't
really chosen a priori but a range of cluster numbers were investigated and the 5
clusters produced the most geographically interpretable results. This is fine, but it isn't a
Thanks, we have removed the “a priori” bit.

b. Honestly, I'm not sure how useful this analysis is. Perhaps I am misreading, but it is
simply grouping sites by tau^2 value; site location, per se, does not play into this
grouping. Looking at the results, Figures 3a and 3d seem pretty meaningless - these are
just all the connections with little influence on the difference between lambda_1 and
lambda_s. In fact, the most interesting result the authors have relegated to appendix
Figure A4: there are a few sites that have a big influence on the difference between
lambda_1 and lambda_s. What is special about these sites? I suspect they might be
connections from high export to low export sites, but the authors should explore what
makes these sites special.
We have changed the presentation of our results. We agree with the reviewer that Figs.
3a and d have little meaning, so we have replaced them with Figs. A4a and b – the
analysis of the top 1% of connections. We still include the other 4 figures (Figs. 3c-f)
showing the location of two pairs of subgroups – we believe this provides important
spatial information, useful for conservation scientists and spatial fisheries management.
With regards to the importance of certain subpopulations/connections we have
mentioned in the text that our analysis combines subpopulation connection sensitivities
and covariances (i.e. the Tuljapurkar approximation uses a sensitivity weighted
covariance matrix; Eq. 8). As a result we lose information on why certain
subpopulations/connections are important. We state this in the discussion and anticipate
using these quantities to identify key nearshore sites and connections in another paper.

c. Perhaps a better strategy for "grouping" sites is to go further with the analysis they
start in the appendix - where are the top 1% connections w.r.t. deviations of lambda_1
and lambda_s? the top 5%?, etc.
We believe that our analysis identifying the top 1% connections, and the connection
subgroups is sufficient for this paper.

d. The authors do make the point that the connections that contribute to deviations of
lambda_1 and lambda_s are different for different larval life history strategies. This is a
valuable result, but would be more valuable if the authors would discuss how the
connections that are important vary with larval life history in a systematic way or
according to certain oceanographic features. Such general conclusions may be beyond
the scope of this paper, but the authors could include some discussion relevant to kelp
bass and sheephead specifically.
The reviewer is right that a full analysis of the distribution of important connections is
beyond the scope of this paper, but one that is very important. We intend to do this
analysis in a follow up paper. With regards to a comparison of the important connections
for kelp bass and sheephead, we have expanded on this in the discussion.

10) Line 191: "Every modeled species". Just to be clear, modeled "species" vary only in
PLD and spawning time, but are equivalent in mortality rate, fecundity, and density-
independent and density-dependent growth rate parameters. (Or perhaps not because
they are normalized to constant K?). This should be explicitly stated.
Modeled species vary primarily in PLD and spawning period, but also in fecundity (f; in
the density independent simulations) and in beta (in the density dependent simulations).
We have made it more explicit that f and beta values vary between species in each
paragraph detailing their choice (first and second to last paragraphs in the
Metapopulation Dynamics section).

11) Metapopulation Dynamics section: the organization of this section is a bit confusing
and might be clarified by subheadings specifying where the assumption of low larval
density is being made and where it is not. In particular, line 207 states that "we also
examined the effect of stochastic potential connectivity on equilibrium abundance." To
this reader, this indicates that we are now talking about a density dependent model
because, otherwise, there is no meaningful equilibrium, and this is followed by a
description of the Beverton-Holt model. But then, line 230 states: "We also numerically
simulated stochastic and deterministic metapopulation dynamics when abundances
were not rare." In previous sections, "when abundances are not rare" meant "dynamics
when abundant," i.e., near equilibrium. But perhaps here you mean that you simulated
the full dynamics? Is the difference between these two sections the difference between
an approximation and running the full model? Or is the difference between low density
and near equilibrium?
We have cleared this section up. We have not added subheadings but been more
explicit about which paragraph refers to which scenario: with density dependence and

12) Eqn 14 and Line 212: Typically, gamma is considered the density-independent
growth term and beta is the density-dependent term. If beta=0, the equation reduces to
density-independent growth (as in line 97).
We have added this description of the beta and gamma parameters to our paper.

13) Line 233: unclear where this equation for beta comes from.
We have expanded on this paragraph, making it clear where this equation for beta
comes from (i.e. using a non-spatial version of our model, where there is no dispersal,
this equation is the solution for beta).

14) Line 264-265: "This area corresponds with the spawning periods and PLDs that have
the greatest variability in potential connectivity (Fig 2a)". Yes, but it excludes areas of
high variability that have low PLDs. Why is the variability in potential connectivity
unimportant for low PLDs?
We have added a sentence to our results describing why low PLD species don’t see a
reduction in growth rates when rare. Although there is high variability in potential
connectivity at low PLDs these connections also have low sensitivities (see Tuljapurkar’s
approximation, Eq. 8). They have low sensitivities because there is redundancy in low
PLD connections – dispersal is over shorter distances and there is overlap in the
dispersal kernels of nearby sites. Further, there is little difference in source strength
between sites at low PLDs. This is in contrast to a high PLDs scenario where there are
certain key connections, for example between the mainland and the islands in the
Souhern California Bight. These connections will have large sensitivities as well as large
(co)variances, and hence there are greater reductions in growth rates for these high PLD

15) Line 267: still works pretty well because the nonlinearity isn't too extreme and
doesn't change sign.
We feel that given our description of the Tuljapurkar approximation in the methods,
adding this note is unnecessary.
16) Line 268-9: "We made a further approximation, where off-diagonal elements of the
covariance/variance matrix were set to zero". Give some biological interpretation of this.
This means that there is no synchronicity in connectivity between sites.
We have added a sentence expanding on the biological significance of our “further
approximation”, addressing the removal of synchronicity in connectivity.

17) I'm puzzled by the choice to use f to adjust density dependence. The density
dependence in this model is from settlement to recruitment, therefore, "density
dependence" is the change in the probability of recruitment with increasing settlers. But
by choosing to adjust f, the authors are, essentially, adjusting settlers rather than a
parameter of density dependence. Another way to measure the strength of density
dependence is by the first derivative of the per capita growth rate. In this case, changing
s and changing gamma would have different effects on the strength of density
dependence. It would be helpful to provide the equation you are using for the strength of
We have expanded on why we used fecundity (f) to change the strength of density
dependence (see second to last paragraph of the Metapopulation Dynamics section).
This confusion came about because we did not make it clear how f affects density
dependence. When changing f we solve for beta (the more usual parameter for changing
DD) given a carrying capacity (K). Thus, this answers Bolker’s and reviewer 1’s
comments – we vary the strength of density dependence by changing beta; we just do
so indirectly through f. This choice was made because it is easy to conceptualize the
effect of changes in f and its effect on density dependence – e.g. increasing fecundity
produces more larvae, which then requires a higher level of DD in order to maintain the
same carrying capacity (K).

18) Figure 4. Lines 302-304
a. First, the sentence "This relationship points to a theoretical high level of density
dependence where, relative to deterministic calculations, the stochasticity of potential
connectivity has no effect" took several reads to decipher - please edit.
This sentence now reads: “Theoretically, this relationship points to a high level of density
dependence where the difference between stochastic and deterministic outcomes is
negligible.” Also, following Bolker’s recommendation we have merged Fig. 4 with Fig. 5,
keeping only results relating to fecundity = 2. We elaborate in the main text that the
difference between stochastic and deterministic outcomes diminishes with increasing
density dependence.

b. Second, consider the biological meaning of this result -- the authors have defined
density-dependence as the compensation ratio and then fixed all sites to the same
carrying capacity. In this context, increasing the "strength of density dependence" by
adjusting fecundity really means throwing more larvae at each site. Given that each site
has the same, fixed carrying capacity, the result is that plenty of settlers arrive to max
out each site and, therefore, all variability in sx above that required to meet carrying
capacity has no effect on the difference between lambda_1 and lambda_s. In other
words, the variation in sx is in a region of the g(sx) where there is no nonlinearity and,
therefore, no effect of variation. Looking at Equation 16, this is expected - if E[sx] in the
denominator of the expression in parentheses is large enough compared to var[sx], then
the expression will be small and have less effect on lambda_1 - lambda_s. The authors
should address more clearly whether this is a biologically realistic scenario - perhaps by
plotting the range of "realistic" compensation ratios on a plot of the BH curve and
comparing this to the variation in sx seen at different sites.
The reviewer’s analysis of Equation 16 is very informative and we have included a
section on it in this paragraph – we outline that increasing density dependence through
modifying the fecundity parameter, increases the expected number of settlers (E[sx]),
and that this should diminish the difference between stochastic and deterministic

Although the reviewer is correct in saying that the level of density dependence is
important, we do not think it is necessary to perform a more detailed analysis of the
relationship between the variance in settlement (sx) and the compensation ratio (the
measure of density dependence). We used realistic compensation ratios (as gauged
from the literature) and as such our results present “biologically realistic” scenarios. This
part of the paper merely states that in the limit of extremely high “unrealistic” density
dependence, our model suggests that the difference between stochastic and
deterministic outcomes becomes negligible. We have highlighted this in the main text.

19) Lines 313-315: The approximation does have a strong correlation with the simulation
results, but it is consistently biased. This bias should be addressed by the authors. I
suspect it is a result of excluding the variation in nx and the cov(nx,sx) that arises
through the simulation.
Indeed there is a clear bias in our settlement approximation to higher expectations and
variances (Fig. A5, dots are mostly above the one-to-one line). The bias comes from our
approximation, which ignores the covariance between adult abundances and settlement
(cov(nx,sx)). Because the bias is to larger values, these statistics must be negative. We
have added a sentence to explain this. Further, following Bolker’s advise we have
included additional information to the figures – the intercept and slope of the
relationships – to quantify the bias.

20) Please clarify the relationship between lines 302-303 (increasing density
dependence decreases differences between lambda_1 and lambda_s) and lines 323-
324 (as the strength of DD increases, the influence of temporal variability increases).
These were badly written sentences and we have reworded both for more clarity. The
first (l302-303) was meant to describe the decrease in difference between stochastic and
deterministic outcomes with increasing density dependence. The second (l323-324) was
meant to describe something different – that the correspondence between simulation
and analytically approximated settlement values strengthened with increasing density
dependence (Fig. A3). Because the analytical approximation depends solely on the
statistics of potential connectivity, we used this increasingly strong relationship to
highlight the importance of potential connectivity. L323-324 now reads “The strength of
these relationships increased with fecundity (Appendix E), indicating that as the strength
of density dependence increases, settlement patterns become increasingly controlled by
potential connectivity.”

21) Lines 375-377: this is a throw-away sentence and needs more careful consideration
to stay in the ms.
Agreed. Although critical nodes and edges in marine connectivity networks play an
important role in the spread of invasive species, the reviewer is right in that this this
sentence would need to be elaborated on if it were to be included in the paper. To save
space we have opted for taking it out.
Replies to Reviewer #2:

My main concerns are related to the interpretation of results and to their discussion. I
think it would be important to provide null expectation and more intuitive interpretation of
the effect of variance and between-site covariance in growth on each population
dynamic metric (growth rate at low abundance and long-term population abundance).
That could then lead to a more in-depth interpretation on the relative importance of
variance and covariance on these metrics.
I don’t understand this comment – didn’t we compare stochastic outcomes with
deterministic ones, isn’t this comparing against a null? What does Rev 2 mean by a null?

Also, results provide a number of predictions that are not well connected to the
discussion. For example, the emergence of subgroups with similar impact on the
metapopulations seems very relevant to both validation of predictions, and for the design
of protected areas. These sub-groups are not analyzed in terms of their spatial and
temporal scales, and there is no discussion on this topic except for a brief mention of
heterogeneous contribution of sites to metapopulation dynamics.
We have added a new paragraph in the discussion (second paragraph) expanding on
the scales of the subgroups and their importance with regards to spatial management.

Same thing (or actually the opposite) goes for synchrony and persistence. These
concepts are discussed as an important contribution of the study. I agree with the
authors this is an important contribution of the study. However, the analysis never
explicitly connects between-site covariance to between-site and metapopulation
In this case we have introduced the notion of synchrony earlier in the paper. In the
methods we have explained that synchrony in connectivity is identified by positive
covariances between subpopulation connections (i.e Cxy) used in the Tuljapurkar
approximation (Eq. 7 & 8). We then link to this and expand on it in the discussion (first
and second paragraphs).

Equation 12 - It would be good to take some time to explain how general the prediction
is (expected value decreases with variance), i.e., only depends on the assumption of
equilibrium dynamics and on the nature of stochasticity.
Below Eq. 12 we have added that one assumption of ours is that there are no Allele
effects and that g''(E[s_{x}]) > 0. Later, in the second to last paragraph of the discussion
we have expanded on our assumptions – equilibrium dynamics and the nature of the
stochasticity (i.e. following Bolker’s advice we make a note of the difference between
time-varying deterministic and time-varying stochastic processes).

Maybe explain the relationship of your model to overall stability. You posit equilibrium
population abundance from the outset. It is a common, but not a trivial, assumption given
fluctuations found in natural systems.
Although a stability analysis would be fruitful we feel that this further analysis will not add
to or change our overall result - that stochastic outcomes are different from deterministic
ones. However, this is an important point and we have expanded on this in the
discussion (second to last paragraph). We explain that new theory would have to be
developed to understand other non-equilibrium dynamics such as those resulting from
periodic forcing (e.g. Floquet theory).
The analytical approximations to growth and abundance are compared with seven-year
averages from simulations. However, very often, the assumption of constant connectivity
leads investigators to use single year (or even shorter) data as a good proxy for long-
term connectivity. It could be useful to show how predictions diverge from the long-term
values as one reduces the temporal extent of simulations. Just a thought.
This is a good thought. Using years in solo, rather than the average, will change the
difference between stochastic and deterministic outcomes but not the overall trend. This
will remain the same – stochastic growth rates when rare and equilibrium abundances
will be reduced relative to their deterministic counterparts. We have added a sentence to
the last paragraph of the paper highlighting this.

L201-202 - This sentence is very dense. You should expand and (re)state some
We have reworded this sentence to be clearer.

L246 - Could you provide the criteria for stationarity?
Yes, stationarity was identified by inspecting the variance in the mean of each
subpopulation's trajectory, calculated over a one hundred iteration window, as time
progressed. This is essentially a run-test of stationarity. We have added this description
to the text.

L335 - It would be important at this point to detail the relative importance of variance and
covariance. They have very different implications but are lumped together in the
presentation and discussion of results.
We have expanded this entire first part of the discussion, highlighting the difference
between variances and covariances.

L336 - The subgroup results could be discussed in more detail, especially their scale,
contribution to synchrony, and implication for conservation (MPAs).
We have created a new paragraph on this subject (second paragraph in discussion),
expanding on their scale, contribution to synchrony, and their implications for
conservation. Specifically, we have stated that our subgroups come from analyzing a
quantity that is a combination of subpopulation sensitivities and connection covariances
(i.e. the weighted covariance matrix in Tuljapurkar’s approximation; Eqs. 7 & 8). Thus we
do not single out the sensitivities or covariances alone, but we have discussed how this
could be done. Indeed this is the focus of work we are doing right now.

L341 - This is where the link between synchrony and the results should be explicit. It is
hard to see how this statement is supported by your analysis, especially given the fact
that the distinction between variance and covariances is not emphasized earlier.
Thank you. Our original discussion on this topic was sparse and we have now expanded
it, creating a new paragraph on the subject (second paragraph in discussion).
Importantly we state explicitly that synchrony in larval connections is identified by
positive elements in the covariance/variance matrix used in the Tuljapurkar
approximation (Eqs. 7 & 8). We also state this earlier in the paper, when we introduce
this approximation in the methods (the “Dynamics when rare” section).

Running-head - 'influence'.
Got it, thanks.

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