# Inference in molecular population genetics

**Date**: 03/09/2026
**Domain**: statistics/computational_statistics
**Taxonomy**: academic/research_paper
**Filter**: Active comments

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## Overall Feedback

Here are some overall reactions to the document.

**Finite Variance of IS Weights Is Unproven for the Primary Estimator**

Section 6.4 explicitly acknowledges that the authors could not prove finiteness of the variance of the IS weights for Q_θ^SD except in the special case of the infinite-sites model. This is a foundational gap: the central-limit-theorem justification for the standard errors reported throughout Section 5 (Tables 1, Figs 2–7) rests on finite variance of the importance weights, yet this property is not established for the sequence or microsatellite applications that form the paper's main empirical comparisons. The practical consequence is that the reported standard errors may severely underestimate true Monte Carlo uncertainty — precisely the failure mode documented for Q_θ^GT at θ=15 in Table 1. The claim of 'several orders of magnitude' efficiency improvement is quantified via sample variances that may themselves be unreliable estimators of the true weight variance. It would be helpful to either derive sufficient conditions on the mutation matrix P, sample size n, and θ under which the variance of Q_θ^SD weights is finite, or to implement the generalized Pareto tail-fitting diagnostic described in Section 6.4 and apply it systematically to all reported examples — including the challenging θ=15 case and the NSE microsatellite data — so that the efficiency comparisons rest on diagnostically validated estimates rather than on sample statistics whose reliability is unconfirmed.

**Approximation Quality of π̂ Is Uncharacterized Beyond Two Special Cases**

The proposal Q_θ^SD is constructed by substituting the approximation π̂(·|A_n) for the intractable π(·|A_n) in the optimal backward transition rates (equation 25). Proposition 1 establishes exactness of π̂ only under parent-independent mutation (PIM) and for n=1 with reversible P; for all other cases — including the sequence and microsatellite models that constitute the main empirical comparisons in Sections 5.2–5.4 — no bound or empirical measure of the approximation error ‖π̂(·|A_n) − π(·|A_n)‖ is provided as a function of n, θ, or the spectral properties of P. Appendix A further approximates π̂ via Gaussian quadrature with only s=4 quadrature points, introducing a second layer of approximation whose accuracy is described as 'rather rough' in some cases, yet no error analysis, no justification for the choice s=4, and no sensitivity comparison between s=4 and s=8 or s=16 is provided. The efficiency of Q_θ^SD relative to Q_θ^* depends directly on how well π̂ approximates π, yet the paper offers only intuitive arguments and empirical comparisons as validation. It would be helpful to include at least one example where π can be computed exactly (e.g., small n with a two-allele model) to directly quantify the approximation gap, to report quadrature error as a function of s, and to provide at least an asymptotic analysis of how the approximation error scales as θ increases or as the mutation matrix departs from PIM.

**Driving-Value Sensitivity and Variance Behavior Away from θ₀ Are Incompletely Characterized**

The paper cites Stephens (1999) to establish that the Fluctuate/MCMC-I estimator has infinite variance for θ > 2θ₀, and Section 6.1 acknowledges that any single-driving-value IS scheme shares this undesirable property in principle. However, the analogous question for Q_θ^SD used with a fixed driving value θ₀ is left open: no characterization is provided of the range of θ over which Q_θ₀^SD yields finite-variance estimates, either theoretically or empirically. In the NSE microsatellite example (Section 5.4, Fig. 5), the absolute likelihood curves show substantially larger run-to-run variability than the relative likelihood curves, which is consistent with weight-distribution problems as θ departs from θ₀=8.0. The authors note that driving-value sensitivity 'did not appear to cause major problems in the examples considered here' but attribute this partly to the small problem sizes. It would be helpful to characterize, over a range of θ/θ₀ ratios, how rapidly the variance of Q_θ^SD weights grows as θ departs from θ₀, and to recommend bridge sampling or multiple driving values as part of the standard workflow rather than as a future direction, given that this issue is likely to become more acute for the 'much larger data sets' referenced in the conclusions.

**Scope of Empirical Comparisons Is Too Narrow to Support Broad Efficiency Claims**

The abstract and conclusions assert that Q_θ^SD 'substantially outperforms existing IS algorithms, with efficiency typically improved by several orders of magnitude,' yet the simulation studies in Section 5 are limited to four small examples: n=10 sequences of length 10 (Section 5.2), n=50 sequences of length 20 (Section 5.3), a microsatellite sample of n=9 alleles (Section 5.4, simulated), and n=60 chromosomes at five loci (Section 5.4, NSE data). No systematic variation of sample size n, sequence length, or θ is presented; the 'several orders of magnitude' claim is documented primarily for the GT comparison at θ=15 in Table 1, a single data point. Notably, the one larger real-data example (NSE, Section 5.4) shows micsat outperforming Q_θ^SD in accuracy for the absolute likelihood surface (Fig. 5), which the authors acknowledge but do not fully explain. The history space grows super-exponentially with n, and it is unclear whether the efficiency gains observed for small n persist at the 'much larger data set' scales referenced in the conclusions. It would be helpful to present a factorial simulation study varying n ∈ {10, 50, 200}, θ ∈ {1, 5, 15}, and mutation model, reporting estimator variance, bias, and wall-clock time, to establish the conditions under which the efficiency gains are robust and to identify regimes where Q_θ^SD may not dominate.

**MCMC and IS Convergence Diagnostics Are Insufficient to Validate Reported Comparisons**

The paper's comparative evaluation relies primarily on comparing results across a small number of independent runs (typically five) as its convergence and mixing diagnostic for both IS and MCMC methods. For the MCMC baselines (Fluctuate, micsat), no trace plots, autocorrelation functions, effective sample sizes, or Gelman–Rubin statistics are reported, making it impossible to assess whether the chains had mixed adequately for the specific datasets analyzed. This matters because an unfavorably tuned or unconverged MCMC chain provides an artificially weak baseline: the discussion by Kuhner and Beerli (Fig. 9) demonstrates that combining 10 independent MCMC runs at different driving values recovers a curve consistent with Q_θ^SD, suggesting the original comparison was against a suboptimally run MCMC. For the IS scheme, Section 6.4 discusses monitoring weight mean, variance, effective sample size, and maximum weight, but the authors' reply (Fig. 12) shows that even these diagnostics can be misleading, with large discontinuous jumps in running estimates appearing after locally stable periods. The proposed Pareto tail diagnostic is described as 'promising on initial investigation' but is not implemented in any example. It would be helpful to report, for each method and example, the effective sample size of the IS weights or MCMC chain, the ratio of the maximum weight to the sum of weights, and results from at least 10 independent runs, and to apply the Pareto tail diagnostic to the challenging examples, so that readers can assess the reliability of the reported likelihood surfaces independently of qualitative judgments.

**Model Assumption Violations Are Unassessed Despite Their Relevance to the Real-Data Application**

Section 2 clearly states the constant-population-size, selective-neutrality, and no-recombination assumptions underlying the Kingman coalescent, and Section 6.2 briefly mentions extensions as future work. However, the paper provides no sensitivity analysis or even qualitative discussion of how violations of these assumptions distort the likelihood surface for θ or the resulting MLE. For the NSE Y-chromosome microsatellite data analyzed in Section 5.4, the assumption of a single panmictic population of constant size is almost certainly violated — the data come from three geographically distinct human populations (Nigeria, Sardinia, East Anglia) where population structure, historical bottlenecks, and non-constant effective population size are well-documented. The paper presents likelihood surfaces for these data (Fig. 5) without any caveat about model misspecification, and the discussant D.A. Stephens explicitly raises robustness to mutation-matrix misspecification, with the authors' reply conceding that this 'is likely to be a serious problem.' Readers might note that under population structure or a recent bottleneck, the effective θ estimated by the coalescent can be substantially inflated or deflated relative to the true mutation-rate parameter, in ways that no amount of IS efficiency improvement can correct. It would be helpful to include at least a brief simulation study in which data are generated under a misspecified model (e.g., two-population structure or exponential growth) and the constant-size panmictic likelihood is fitted, to illustrate the magnitude and direction of the resulting bias in θ̂.

**No-recombination assumption applied to multi-locus data with physical linkage**

Assumption: Section 2 explicitly states that the chromosomal region analysed is 'sufficiently small that the possibility of recombination over relevant timescales can be ignored,' so the genealogy is modelled as a single Kingman coalescent tree rather than an ancestral recombination graph.

Data structure: The NSE microsatellite application (Section 5.4) analyses five Y-chromosome loci jointly for 60 males. The paper justifies the no-recombination assumption for Y-chromosome data ('we assume no recombination'), which is biologically reasonable for the non-recombining region of the Y. However, the sequence-data examples (Section 5.2–5.3) use sequences of length 10–20 sites with a non-trivial per-site mutation rate, and the infinite-sites example (Section 5.5) treats the entire sequence as a single non-recombining unit. For nuclear sequence data of even modest length, some recombination within the locus is expected, meaning the true genealogy is a graph rather than a tree.

Consequence: When recombination is present but ignored, the single-tree likelihood is a misspecified approximation. Importance weights computed under the tree model will be systematically biased, and the variance of the IS estimator may be inflated in ways that are not captured by the reported standard errors.

Defense and its adequacy: The authors acknowledge this limitation in Section 6.2, noting that Fearnhead (2000) extended the IS framework to the ancestral recombination graph. This is an honest and constructive acknowledgment, but no sensitivity analysis or recombination-rate bound is provided for the sequence examples actually analysed. It would be helpful to state, even approximately, the recombination rates at which the tree approximation remains adequate for the specific loci used, so readers can assess whether the reported likelihood estimates are materially affected.

**Constant-Ne, panmictic demographic model applied to a geographically structured human sample**

Assumption: The demographic model throughout the paper is a constant-sized, randomly mating Wright–Fisher population of N chromosomes (Section 2). The coalescent approximation adopted is Kingman's n-coalescent, which assumes exchangeable lineages under a single, time-homogeneous effective population size.

Data structure: The NSE data set (Section 5.4) consists of 60 males drawn from three geographically distinct populations — Nigeria, Sardinia, and East Anglia. These populations differ substantially in ancestry, effective size, and history of migration and bottlenecks. Sampling across three continents introduces among-population genealogical structure that is not exchangeable under the panmictic coalescent.

Consequence: Under population structure, coalescence rates differ within and between demes, and the single-Ne Kingman coalescent conflates within-population and between-population coalescence times. The resulting θ estimate is a weighted average that does not correspond to any single population's Ne·μ product, and the shape of the likelihood surface can be distorted. Wilson and Balding (1998), whose micsat results are compared directly, also assume the same single-population stepwise model for these data, so the comparison is internally consistent — but both methods share the same potential misspecification.

Defense and its adequacy: The paper follows Wilson and Balding (1998) in treating the five Y-chromosome loci as evolving under a single panmictic coalescent, and the authors note in Section 6.2 that extensions to structured populations exist (Bahlo and Griffiths, 2000; Beerli and Felsenstein, 1999). No sensitivity analysis for the NSE data is provided. It would be helpful to note explicitly that the θ estimate for the NSE data should be interpreted as a summary statistic across structured populations rather than as a parameter of a single panmictic population, and to indicate whether the structured-coalescent extensions are expected to shift the likelihood peak materially.

**Status**: [Pending]

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## Detailed Comments (22)

### 1. Topology Count Formula Counts Ordered Histories, Not Topologies

**Status**: [Pending]

**Quote**:
> For example, there are $n!(n-1)!/2^{n-1}$ different possible topologies for the underlying trees.

**Feedback**:
It would be helpful to verify what this formula actually counts. For n=3 it gives 3!·2!/4 = 3, which matches the number of labeled unrooted topologies. For n=4 it gives 4!·3!/8 = 18, which equals the number of labeled ordered genealogical histories (ordered topologies) but not the 3 unrooted or 15 rooted labeled topologies. Readers might note that the formula counts labeled genealogical histories rather than topologies in the conventional sense. Rewriting 'different possible topologies' as 'different possible labeled genealogical histories (ordered topologies)' would align the text with what the formula actually enumerates.

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### 2. Equation (1) Mutation Term Ambiguous When P_{αα} > 0

**Status**: [Pending]

**Quote**:
> p _ {\theta} \left(H _ {i} \mid H _ {i - 1}\right) = \left\{ \begin{array}{l l} \frac {n _ {\alpha}}{n} \frac {\theta}{n - 1 + \theta} P _ {\alpha \beta} & \text{if } H _ {i} = H _ {i - 1} - \alpha + \beta , \\ \frac {n _ {\alpha}}{n} \frac {n - 1}{n - 1 + \theta} & \text{if } H _ {i} = H _ {i - 1} + \alpha , \\ 0 & \text{otherwise}, \end{array} \right. \tag {1}

**Feedback**:
When P_{αα} > 0, a self-mutation event leaves H_i = H_{i−1}, which the 'otherwise = 0' branch assigns zero probability. Yet the text later acknowledges this ambiguity ('which may not be uniquely determined by the list of states if P_{αα} > 0'). The transition probability for H_i = H_{i−1} should include contributions from both the split event and any self-mutation event. It would be helpful to add a fourth case for H_i = H_{i−1} that sums both contributions, or to restrict the mutation case explicitly to β ≠ α and note that self-mutations are absorbed into the split case, so that equation (1) is unambiguous for all mutation matrices.

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### 3. PIM Idempotency Claim P^m = P Stated Without Verification

**Status**: [Pending]

**Quote**:
> Proof of property (a). The conditional probabilities $\pi(\cdot|A_n)$ for PIM are defined at equation (16), and the result follows from the fact that, for PIM, $P^m = P$ for $m = 1, 2, \ldots$

**Feedback**:
Under PIM, P_{αβ} = P_β for all α, so every row of P is the same vector. Then (P²)_{αβ} = Σ_γ P_{αγ}P_{γβ} = Σ_γ P_γ · P_β = P_β = P_{αβ}, giving P² = P, and by induction P^m = P for all m ≥ 1. This one-line verification is omitted, leaving the idempotency claim unsubstantiated for readers unfamiliar with rank-one stochastic matrices. Adding the calculation '$(P^2)_{\alpha\beta} = \sum_\gamma P_\gamma P_\beta = P_\beta$, so $P^2 = P$ and by induction $P^m = P$' immediately after the claim would make the proof self-contained.

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### 4. Induction Step for M^(n) in Proof of Property (d) Is Omitted

**Status**: [Pending]

**Quote**:
> If $\tilde{\pi}$ satisfies property (b) of the proposition, then $M^{(1)} = (1 - \lambda_1)(I - \lambda_1P)^{-1}$. It then follows from equation (23) and mathematical induction that $M^{(n)} = (1 - \lambda_n)(I - \lambda_nP)^{-1}$, and so $\tilde{\pi} = \hat{\pi}$.

**Feedback**:
The induction step — showing that equation (23) with M^(n) = (1−λ_n)(I−λ_nP)^{−1} implies M^(n+1) = (1−λ_{n+1})(I−λ_{n+1}P)^{−1} — is asserted but not carried out. The algebra is non-trivial: substituting M^(n) into the recurrence (n+1)M^(n) = nM^(n+1) + M^(n)M^(n+1) and solving for M^(n+1) requires verifying that (nI + M^(n)) is invertible and that the resulting expression matches the claimed form. Adding the explicit induction step would make the uniqueness claim in property (d) independently verifiable.

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### 5. Support Condition for Single-Driving-Value Estimator (12) Is Unstated

**Status**: [Pending]

**Quote**:
> each value of $\theta$. However, it appears to be more efficient to reuse samples from a single IS function. This is in theory straightforward: for any fixed $\theta_0$ we have
> 
> $$
> L (\theta) \approx \frac {1}{M} \sum_ {i = 1} ^ {M} \pi_ {\theta} \left(A _ {n} \mid \mathcal {H} ^ {(i)}\right) \frac {P _ {\theta} \left(\mathcal {H} ^ {(i)}\right)}{Q _ {\theta_ {0}} \left(\mathcal {H} ^ {(i)}\right)}, \tag {12}
> $$
> 
> where $\mathcal{H}^{(1)}, \ldots, \mathcal{H}^{(M)}$ are independent samples from $Q_{\theta_0}(\cdot)$. This approach is due to Griffiths and Tav

**Feedback**:
Equation (12) is unbiased in expectation only when Q_{θ₀}(H) > 0 whenever π_θ(A_n|H)P_θ(H) > 0 for all θ of interest. This support condition is more demanding than for the per-θ estimator (9) because P_θ(H) changes with θ: histories with positive probability under P_θ but zero under Q_{θ₀} are entirely missed. The text does not state this condition, even though its failure is the root cause of the infinite-variance problem for Fluctuate (θ > 2θ₀) discussed in Section 6.1. Adding a sentence after equation (12) stating the support requirement and noting that it may fail when θ departs substantially from θ₀ would make the validity condition explicit and motivate the subsequent discussion.

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### 6. Asymptotic Normality Invoked for Models Where Finite Variance Is Explicitly Unproven

**Status**: [Pending]

**Quote**:
> For the IS schemes, assuming that the distribution of the weights has finite variance $\sigma^2$, then (by the central limit theorem) the estimator (8) is asymptotically normal with variance $\sigma^2 / M$. A natural measure of the variability is then given by the standard error $\hat{\sigma} / \sqrt{M}$, where $\hat{\sigma}^2$ is the sample variance of the $M$ weights.

**Feedback**:
Section 6.4 explicitly states that finite variance of the IS weights for Q_θ^SD could not be proved except for the infinite-sites model. The CLT justification for the standard errors in Tables 1 and Figures 2–7 therefore rests on an unverified precondition for the sequence and microsatellite models. When variance is infinite, σ̂² does not converge to a finite limit and σ̂/√M may not go to zero. It would be helpful to rewrite the passage to note that finite variance is not established for the sequence and microsatellite models, and that the reported standard errors should be interpreted with this caveat in mind — or to cross-reference Section 6.4 explicitly at this point.

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### 7. Factor-of-500 SE Reduction: Observed Factor of 17 Implies Non-Trivial Variance Underestimation

**Status**: [Pending]

**Quote**:
> If they do then the longer run should result in standard errors which are smaller by a factor of $\sqrt{500} \approx 22$. For $\theta = 2.0$ and $\theta = 10.0$ the changes in the estimated standard error (by factors of about 21 and 17 respectively) between the long and short runs for $Q_{\theta}^{\mathrm{SD}}$ suggest that these standard errors are being estimated reasonably accurately.

**Feedback**:
The ratio of sample sizes is 10^7/20,000 = 500, so the expected SE reduction is √500 ≈ 22.4. The observed factor of 17 at θ=10.0 implies the true variance is approximately (22.4/17)² ≈ 1.74 times larger than the sample variance estimate — a roughly 74% underestimation. Describing this as 'reasonably accurate' overstates the agreement. It would be more precise to note that the shortfall implies the sample variance underestimates the true variance by a factor of roughly (22/17)² ≈ 1.7 at θ=10.0, which is a non-trivial discrepancy rather than confirmation of accuracy, and is consistent with the heavy-tail concerns raised in Section 6.4.

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### 8. GT Estimate at θ=15.0 Described as 'Seven Orders of Magnitude' Relative to an Uncertain Reference

**Status**: [Pending]

**Quote**:
> For $\theta = 15.0$, although neither method produces a very accurate estimate of the likelihood using 20000 samples, the samples from $Q_{\theta}^{\mathrm{GT}}$ underestimate the likelihood by seven orders of magnitude.

**Feedback**:
From Table 1, the Q_θ^GT estimate is 2.41×10⁻¹⁹ and the Q_θ^SD long-run estimate is 5.37×10⁻¹², giving a ratio of ~2.2×10⁷ — numerically consistent with 'seven orders of magnitude.' However, the same section acknowledges that the Q_θ^SD long-run SE at θ=15.0 is itself likely underestimated due to skewed weights, so the reference value 5.37×10⁻¹² cannot be treated as a reliable ground truth. Adding a parenthetical such as '(relative to the Q_θ^SD long-run estimate, which is itself subject to substantial uncertainty at this θ value, as discussed in Section 6.4)' would make the reference point and its limitations explicit.

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### 9. Infinite-Variance Claim for Fluctuate Extended to All n Without Proof

**Status**: [Pending]

**Quote**:
> The result of Stephens (1999) can be extended to show that the variance of the IS weights for the Fluctuate scheme (Kuhner et al. 1998) is infinite for $\theta > 2 \theta_0$, regardless of the value of the sample size $n$.

**Feedback**:
Stephens (1999) derived infinite variance for n=2, as Felsenstein explicitly notes in his discussion ('It is important to note that this rule is for n=2'). The extension to arbitrary n is asserted here without derivation, sketch of proof, or citation of a completed result. For general n the IS weight is a product of n−1 ratios whose tail behavior depends on the joint distribution of coalescence times and mutation counts across all lineages — a non-trivial extension. Felsenstein's Fig. 11 (n=50, θ/θ₀≈100, empirically stable) is dismissed without engaging with the possibility that the threshold shifts with n. A citation to a completed proof, or at minimum the key steps of the extension argument, should be added after 'regardless of the value of the sample size n.'

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### 10. √1000 Rounded to 32 Rather Than 31.6, Overstating Theoretical SE Reduction

**Status**: [Pending]

**Quote**:
> the standard errors were smaller by about a factor of 31, suggesting that the standard errors in the smaller sample are accurately reflecting the standard deviation of the weights (they should in theory be reduced by a factor of $\sqrt{1000} \approx 32$).

**Feedback**:
√1000 = 31.623…, which rounds to 31.6, not 32. Rounding to 32 makes the observed factor of 31 appear slightly below theory rather than consistent with it: 31 vs. 31.6 is a 2% discrepancy, while 31 vs. 32 is a 3% discrepancy. Rewriting '$\sqrt{1000} \approx 32$' as '$\sqrt{1000} \approx 31.6$' would give a more accurate comparison and strengthen the authors' own argument that the standard errors are reliable.

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### 11. Infinite-Variance Claim for Fluctuate Implies Broader Failure Than Text Acknowledges

**Status**: [Pending]

**Quote**:
> the surfaces obtained still tended to underestimate the relative likelihood away from the driving values used, thus giving a false impression of the tightness and/or position of the peak of the likelihood surface, presumably because $P_{\theta_0}(\tilde{\mathcal{G}}|A_n)$ is a poor approximation to $P_{\theta}(\tilde{\mathcal{G}}|A_n)$ in this range. (In fact Stephens (1999) has recently shown that for $\theta > 2 \theta_0$ the estimator has infinite variance.)

**Feedback**:
The parenthetical cites infinite variance as supporting evidence for underestimation across the full range away from θ₀, but infinite variance only applies for θ > 2θ₀. In Fig. 2(c) the driving values were near 0.6 and 1.0, and underestimation is visible on both sides of the peak, including for θ < θ₀ where the infinite-variance argument does not apply. For θ < θ₀ the underestimation must be explained by the approximation-quality argument alone. It would be helpful to rewrite the parenthetical to clarify that infinite variance explains the particularly severe underestimation on the right tail (θ > 2θ₀), while the underestimation for θ < θ₀ is attributable to the approximation-quality argument stated in the preceding sentence.

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### 12. Inconsistent Driving-Value Notation π₀ vs. θ₀ in NSE Description

**Status**: [Pending]

**Quote**:
> Five different estimated likelihood and relative likelihood curves were found by using our method, each based on half a million samples from $Q_{\pi_0=8.0}^{\mathrm{SD}}$.

**Feedback**:
Throughout the paper the driving value is denoted θ₀ (e.g., Q_{θ₀=10.0}^{SD} in the same section, and Q_{θ₀=8.0}^{SD} in the Fig. 5 caption). Here the subscript is written as π₀=8.0, which conflicts with the use of π for the stationary distribution and the conditional sampling distribution elsewhere. The Fig. 5 caption correctly uses θ₀=8.0, confirming this is a typographical inconsistency. Rewriting '$Q_{\pi_0=8.0}^{\mathrm{SD}}$' as '$Q_{\theta_0=8.0}^{\mathrm{SD}}$' would restore notational consistency.

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### 13. Claim That micsat Is More Accurate for NSE Data Lacks Quantitative Support

**Status**: [Pending]

**Quote**:
> Further investigation (more runs of each method) suggested that the curve obtained by using micsat is more accurate.

**Feedback**:
This is the section's most consequential empirical claim — that the MCMC competitor outperforms the proposed IS method for the NSE real-data example — yet no numerical evidence is presented: no additional figure, no table of run-to-run variability, no effective sample size comparison, and no statement of how many additional runs were performed. The 'accurate' reference curve in Fig. 5(c) is itself produced by the proposed IS method (2.5 million samples), so it is not an independent ground truth. If the IS weights have heavy tails for this dataset, the reference curve may itself be biased. It would be helpful to include the number of additional runs, the criterion used to assess accuracy, and a caveat that the reference curve is an IS estimate whose reliability for this dataset has not been independently validated.

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### 14. Root Count S+1 for Infinite-Sites Rooted Gene Trees Is Incorrect for General Topologies

**Status**: [Pending]

**Quote**:
> There are $S + 1$ such rooted gene trees, where $S$ is the number of mutations in the data.

**Feedback**:
The number of distinct rootings of an unrooted tree equals the number of edges in that tree. For a binary unrooted tree with n leaves and S mutations, the total number of edges is (n−1) + S (coalescent edges plus mutation edges), not S+1. For the Fig. 6 example with n=5 types and S=5 mutations, the unrooted tree has 4+5=9 edges, giving 9 possible rootings, not S+1=6. The formula S+1 holds only for a path-graph (caterpillar) topology where all coalescent edges lie on a single path. It would be helpful to either rewrite 'There are $S+1$ such rooted gene trees' as 'There are $(n-1)+S$ such rooted gene trees (one per edge of the unrooted gene tree)' or state explicitly the topological restriction under which S+1 is correct.

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### 15. Finite-Variance Admission Creates Logical Tension with CLT-Based Standard Errors Throughout

**Status**: [Pending]

**Quote**:
> we could not prove finiteness of the variance of our weights, except in the special case of the infinite sites model where the number of possible histories is finite.

**Feedback**:
This admission creates a direct logical tension with the standard errors in Tables 1 and Figures 2–7, which are justified by the CLT for IS estimators — a justification that requires finite variance of the importance weights. The authors acknowledge the risk ('all these methods will suffer if the sample variance substantially underestimates the variance') but do not connect this back to the standard errors already reported for the sequence and microsatellite models. Adding a sentence explicitly stating that the standard errors in Section 5 for sequence and microsatellite models are contingent on the unproven finite-variance condition, and that the Pareto diagnostic proposed here should be applied to validate them, would close this logical gap.

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### 16. Causal Claim About Underestimation Conflates Skewness with Infinite Variance

**Status**: [Pending]

**Quote**:
> the distribution of the importance weights tends to be more skewed for $\theta$ away from the $\theta_{0}$. As a result such methods will tend to underestimate the relative likelihood away from $\theta_{0}$, leading to an estimated curve which is artificially peaked about this driving value

**Feedback**:
An IS estimator with fixed θ₀ is unbiased for any θ provided the weights have finite mean — skewness alone does not cause systematic underestimation. What causes the artificially peaked curve is infinite variance (for θ > 2θ₀ in the Fluctuate case), which makes the sample mean an inconsistent estimator in finite samples. It would be helpful to distinguish between (a) the finite-variance regime where skewness causes high Monte Carlo error but not systematic bias, and (b) the infinite-variance regime where the estimator genuinely underestimates. Rewriting 'the distribution of the importance weights tends to be more skewed … As a result such methods will tend to underestimate' as 'the variance of the importance weights tends to grow, and may become infinite, for θ away from θ₀. In the infinite-variance regime the sample mean is not a consistent estimator and will tend to underestimate the true likelihood ratio in finite samples' would make the causal mechanism precise.

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### 17. Choice of s=4 Quadrature Points Is Unjustified Given Acknowledged Roughness

**Status**: [Pending]

**Quote**:
> We used $s = 4$ quadrature points. Although in some cases the approximation to $\hat{\pi}(\cdot|\cdot)$ obtained through this procedure is rather rough, we note that in any case the IS function defined by this approximation to $\hat{\pi}(\cdot|\cdot)$ is a valid IS function in its own right, and so leads to an estimator (9) which is consistent.

**Feedback**:
The authors choose s=4 without any error analysis, convergence study, or comparison with larger s. For large l or large θ, the integrand in equation (31) — a product of l factors F_{αβ}^{(θ,t,n)} — can vary sharply with t, and four-point Gauss-Laguerre quadrature may be inadequate. The acknowledged 'rather rough' approximation in some cases is precisely the regime where the choice of s matters most for IS efficiency. Since quadrature error feeds directly into the approximation of π̂, and the efficiency of Q_θ^SD depends on how well π̂ approximates π, this introduces an unquantified second layer of approximation. Adding a sentence reporting the quadrature error for at least one representative (θ, n, l) combination by comparing s=4 against s=8 or s=16 would allow readers to assess whether the roughness materially degrades the efficiency gains reported in Section 5.

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### 18. Markov Structure Loss Under Varying Population Size Imprecisely Described

**Status**: [Pending]

**Quote**:
> In the case of a varying population size, the simple Markov structure of the underlying processes is lost, and it seems necessary to include time information in the missing data (as in Griffiths and Tavaré (1994c)).

**Feedback**:
The Kingman coalescent with deterministic time-varying Ne(t) retains the Markov property in the joint state (configuration, time) — what is lost is time-homogeneity of the coalescence rates, not the Markov property itself. The process is still Markov when time is included in the state, which is exactly why including time in the missing data restores tractability. Rewriting 'the simple Markov structure of the underlying processes is lost' as 'the time-homogeneity of the coalescence rates is lost, since they become functions of t under varying Ne(t), so the configuration-only Markov property no longer holds' would accurately characterize the technical obstacle and motivate the time-augmentation step.

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### 19. Intermediate Notation P_θ(H ∩ A_n) in Equation (11) Obscures the Bayes-Rule Step

**Status**: [Pending]

**Quote**:
> \pi_ {\theta} \left(A _ {n} | \mathcal {H}\right) \frac {P _ {\theta} (\mathcal {H})}{Q _ {\theta} ^ {*} (\mathcal {H})} = \pi_ {\theta} \left(A _ {n} | \mathcal {H}\right) \frac {P _ {\theta} (\mathcal {H})}{P _ {\theta} (\mathcal {H} \mid A _ {n})} = \frac {P _ {\theta} (\mathcal {H} \cap A _ {n})}{P _ {\theta} (\mathcal {H} \mid A _ {n})} = \pi_ {\theta} \left(A _ {n}\right) = L (\theta), \tag {11}

**Feedback**:
The third expression writes the numerator as P_θ(H ∩ A_n), but the denominator P_θ(H|A_n) is a conditional probability. Dividing a joint probability by a conditional probability does not simplify to a marginal without invoking Bayes' rule explicitly. The cleaner derivation is: π_θ(A_n|H)·P_θ(H) = P_θ(A_n, H), and P_θ(A_n, H)/P_θ(H|A_n) = P_θ(A_n) = L(θ). Rewriting the intermediate step as $P_\theta(A_n, \mathcal{H}) / P_\theta(\mathcal{H} \mid A_n)$ rather than using intersection notation would make the Bayes-rule step explicit and avoid conflating event intersection with joint density notation.

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### 20. Geometric-to-Poisson Equivalence in Appendix A: Rate Parameter Choice Deserves Explicit Derivation

**Status**: [Pending]

**Quote**:
> It follows from elementary properties of Poisson processes that this is equivalent to drawing a time $t$ from an exponential distribution with rate parameter 1, and then applying $m_i$ mutations to locus $i$ ($i = 1, \ldots, l$), where the $m_i$ are independent and Poisson distributed with mean $\theta t / n$, and the mutations at each locus are governed by transition matrix $P$.

**Feedback**:
Readers might note that the choice of rate parameter 1 for the exponential mixing distribution is not the obvious choice from the geometric parameter alone, and the equivalence is described as following from 'elementary properties' without derivation. The marginal distribution of m = Σ m_i under Exp(1) mixing with per-locus Poisson mean θt/n is Geometric with stopping probability n/(n+lθ), which is consistent with the text — but the derivation should be made explicit. Adding a one- or two-line verification showing that the PGF of the Poisson(lθt/n) mixture against Exp(1) yields the correct geometric distribution would allow readers to confirm the equivalence without consulting external references.

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### 21. No-Recombination Assumption Applied to Sequence Data Without Recombination-Rate Bound

**Status**: [Pending]

**Quote**:
> we assume no recombination

**Feedback**:
The paper justifies the no-recombination assumption for Y-chromosome microsatellite data on biological grounds, but the sequence-data examples (Sections 5.2–5.3) use sequences of length 10–20 sites with non-trivial per-site mutation rates, and the infinite-sites example (Section 5.5) treats the entire sequence as a single non-recombining unit. For nuclear sequence data of even modest length, some recombination within the locus is expected, meaning the true genealogy is an ancestral recombination graph rather than a tree. When recombination is present but ignored, the single-tree likelihood is a misspecified approximation and IS weights computed under the tree model may be systematically biased. The authors acknowledge in Section 6.2 that Fearnhead (2000) extended the IS framework to the ancestral recombination graph, but no sensitivity analysis or recombination-rate bound is provided for the sequence examples actually analysed. It would be helpful to state, even approximately, the recombination rates at which the tree approximation remains adequate for the specific loci used, so readers can assess whether the reported likelihood estimates are materially affected.

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### 22. Constant-Ne Panmictic Model Applied to Geographically Structured NSE Sample Without Caveat

**Status**: [Pending]

**Quote**:
> Further investigation (more runs of each method) suggested that the curve obtained by using micsat is more accurate.

**Feedback**:
The NSE data set consists of 60 males drawn from three geographically distinct populations — Nigeria, Sardinia, and East Anglia — yet the likelihood surface is estimated under a constant-sized, randomly mating Kingman coalescent. Under population structure, coalescence rates differ within and between demes, and the single-Ne model conflates within-population and between-population coalescence times. The resulting θ estimate is a weighted average that does not correspond to any single population's Ne·μ product, and the shape of the likelihood surface can be distorted. The paper follows Wilson and Balding (1998) in this choice, making the comparison internally consistent, but no caveat is provided for readers interpreting the θ estimate. It would be helpful to note explicitly that the θ estimate for the NSE data should be interpreted as a summary statistic across structured populations rather than as a parameter of a single panmictic population, and to indicate whether the structured-coalescent extensions cited in Section 6.2 are expected to shift the likelihood peak materially.

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