# Inference in molecular population genetics

**Date**: 03/08/2026
**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 Importance Weights Is Not Established for the General Case**

All three reviewer panels flag this as the most foundational gap in the paper. Section 6.4 explicitly acknowledges that finite variance of the importance weights under Q_θ^SD cannot be proved except for the infinite-sites model, where the history space is finite. Without finite variance, the central limit theorem invoked in Section 5 to justify the standard errors reported in Table 1 and Figures 2–5 does not apply, and those standard errors may be arbitrarily misleading. The paper itself notes that at θ=15 the short-run standard error changes by less than a factor of 2 rather than the expected √500 ≈ 22, a pattern consistent with heavy-tailed weight distributions. It would be helpful to derive sufficient conditions on the mutation matrix P, the sample configuration, and θ under which finite variance is guaranteed, or to provide a systematic empirical characterization of weight-tail behavior using extreme-value diagnostics (e.g., generalized Pareto fits as mentioned in Section 6.4) across all examples. At minimum, Theorem 1 and Proposition 2 should be accompanied by a remark clarifying the variance status of the resulting estimator, so that practitioners can identify regimes in which the reported standard errors are trustworthy.

**Approximation Quality of π̂(·|Aₙ) Is Uncharacterized for Non-PIM Models and Large n or High θ**

The efficiency advantage of Q_θ^SD over Q_θ^GT rests entirely on π̂(·|Aₙ) being a good approximation to the true optimal conditional sampling distribution π(·|Aₙ). Proposition 1 establishes exactness only under parent-independent mutation (property a) and for n=1 with reversible P (property b); for all other cases—including the stepwise microsatellite model and the asymmetric sequence model of equation (28), which are the paper's primary motivating examples—the approximation quality is entirely uncharacterized. No bound on ‖π̂(·|Aₙ) − π(·|Aₙ)‖ is provided as a function of n, θ, or the spectral gap of P, and the qualitative discussion in Remark 1 does not substitute for such a bound. For large n or high θ, the geometric mixture in equation (17) may place insufficient weight on types reachable only via many mutations, causing the proposal to miss important regions of history space. Additionally, the Gaussian quadrature approximation in Appendix A (equations 31–33, using only s=4 points) introduces a further uncontrolled error that propagates directly into the backward transition probabilities q̂_θ, with no convergence analysis as a function of s, θ, or sequence length. It would be helpful to derive an asymptotic or non-asymptotic error bound on ‖π̂ − π‖, to present a numerical comparison of π̂ against Monte Carlo estimates of π for representative configurations, and to report the sensitivity of estimated likelihoods and standard errors to the choice of s in at least one sequence-data example.

**Likelihood Surface Estimation from a Single Driving Value θ₀ Has Unverified Finite-Variance Properties**

The paper's primary mode of likelihood curve estimation uses a single IS function Q_{θ₀}^SD and reweights via equation (12) across a range of θ values. It is established (Stephens 1999, cited in Section 5.3) that the analogous MCMC Method I estimator has infinite variance for θ > 2θ₀, and the authors confirm in their reply to discussants that this result holds regardless of sample size. While the authors conjecture that the missing-data representation of Q_θ^SD partially mitigates this problem, no formal result establishes finite variance of the reweighted estimator for θ substantially different from θ₀. Figure 2(c) demonstrates that single-driving-value MCMC methods produce artificially peaked relative likelihood curves, and the same structural concern applies to IS with a fixed θ₀. The paper recommends bridge sampling as a remedy (Section 6.1) but does not implement or evaluate it in any example. It would be helpful to either prove that the Q_{θ₀}^SD estimator has finite variance for all θ in a neighborhood of θ₀, or to demonstrate empirically—using the NSE or sequence data examples—that bridge sampling or a mixture of driving values materially improves the reliability of the estimated likelihood surface. The main text should also include a clear warning against evaluating the likelihood surface far from θ₀ without combining estimates across multiple driving values.

**Empirical Comparisons Are Too Small-Scale and Insufficiently Replicated to Support General Efficiency Claims**

The abstract claims efficiency improvements of 'several orders of magnitude' over existing IS algorithms, but all comparisons in Section 5 use datasets with n ≤ 60 chromosomes and sequences of length ≤ 20 sites—problems the authors themselves acknowledge in Section 6.5 to be 'small.' No simulation study with known ground truth reports bias, mean squared error, or coverage of confidence intervals for θ̂ across repeated datasets; the paper explicitly states that 'we have not performed the larger scale simulation studies that are necessary to obtain accurate estimates of Monte Carlo errors.' The single larger example (NSE microsatellite data, n=60, five loci) actually shows micsat outperforming Q_θ^SD for the absolute likelihood surface. No systematic variation of n, sequence length, or θ is presented to characterize how the efficiency ratio between Q_θ^SD and Q_θ^GT, or between IS and MCMC, scales with problem size. It would be helpful to include at least one scaling experiment—varying n from 10 to 100 with fixed sequence length and θ—reporting effective sample size or coefficient of variation of weights and wall-clock time, and to report empirical bias and variance of the MLE across at least 50–100 simulated replicates per scenario, so that the efficiency claims have a statistically grounded basis and practitioners can assess the method's practical scope.

**MCMC Convergence Assessment for Competing Methods Is Insufficient to Support Comparative Conclusions**

Sections 5.3 and 5.4 compare Q_θ^SD against Fluctuate and micsat, but the MCMC runs are assessed only by visual comparison of likelihood curves across a small number of independent seeds, without formal convergence diagnostics such as Gelman–Rubin R̂ statistics, trace plots of genealogy summary statistics, or effective sample size calculations for the MCMC chains. The paper notes that Fluctuate with 50,000 iterations gives 'very inaccurate estimates' and that 1,000,000-iteration chains 'still tended to underestimate the relative likelihood away from the driving values,' but it is not established whether these failures reflect non-convergence of the Markov chain or the known infinite-variance problem of the IS step in Fluctuate (Stephens 1999). These two failure modes have different remedies and different implications for the comparison. It would be helpful to run the MCMC comparisons with explicit convergence monitoring—multiple overdispersed starting trees, Gelman–Rubin diagnostics on TMRCA or number of mutations—and to separately attribute observed inaccuracies to mixing failure versus IS weight degeneracy, so that the relative merits of IS and MCMC are assessed on a fair and interpretable basis.

**Model Assumptions Are Insufficiently Delimited and Their Violation Is Not Assessed for the Real-Data Example**

The demographic and genetic model of Section 2 assumes a constant-sized, panmictic, neutral population evolving under the Kingman coalescent with no recombination, and Theorem 1's optimality characterization is derived specifically under these conditions via the Fleming–Viot particle representation. However, the NSE dataset analyzed in Section 5.4 consists of 60 males sampled from three geographically distinct populations (Nigeria, Sardinia, East Anglia), for which a single panmictic constant-size model is biologically implausible and likely to bias inference for θ. The paper does not quantify or qualitatively discuss the potential bias introduced by applying this model to structured, potentially non-stationary data, nor does it compare results with a structured-coalescent analysis. More broadly, the framing in Sections 1 and 6.5 presents the method as applicable to 'modern population genetics data' without explicitly stating that all likelihood surfaces in Section 5 are valid only under these restrictive assumptions. It would be helpful to add a clearly demarcated assumptions section to Theorem 1, to discuss how the form of the optimal backward transition rates changes under population growth or subdivision, and to include at least a brief sensitivity analysis or simulation study demonstrating the direction and magnitude of bias expected under common violations such as mild population structure or a twofold change in effective population size.

**Constant-size, panmictic population assumption applied to structured, multi-population real data**

The formal model (Section 2) explicitly assumes a single, randomly mating population of constant size N throughout its history — the standard Kingman coalescent with no population structure or demographic change. However, the most substantive real-data application in the paper is the NSE microsatellite dataset (Section 5.4), which consists of 60 males drawn from three geographically distinct populations: Nigeria, Sardinia, and East Anglia. Sampling from three separate continental populations almost certainly violates the panmixia assumption, because chromosomes within each sub-population share more recent common ancestors than chromosomes across sub-populations, producing a structured coalescent rather than a standard Kingman coalescent. The paper acknowledges in Section 6.2 that extensions to structured populations exist (citing Bahlo and Griffiths, 2000; Beerli and Felsenstein, 1999) but applies the constant-size, unstructured model to these data anyway. The consequence is that the likelihood surface for θ estimated from the NSE data conflates the scaled mutation rate with unmodelled between-population divergence, potentially biasing the location and width of the likelihood peak. It would be helpful to note explicitly that the NSE results should be interpreted as a methodological comparison rather than a substantive estimate of θ, and to flag that the structured-population extension is needed before the absolute likelihood values carry demographic meaning.

**Stationarity assumption for the MRCA type may be violated under the stepwise mutation model with a truncated type space**

The coalescent framework in Section 2 requires that the population be sampled at stationarity, so that the type of the MRCA is drawn from the stationary distribution ψ(·) of the mutation Markov chain P. For the microsatellite application (Section 5.4), the stepwise mutation model on the integers is a symmetric random walk, whose stationary distribution on an infinite state space is improper (uniform). The paper handles this by truncating the type space to E = {0, 1, …, 19} and reflecting boundaries at 0 and 19. This truncation induces a proper stationary distribution, but it is one that depends on the chosen boundaries rather than on any biological property of the locus. The NSE allele lengths range from roughly 8 to 13 repeats (the simulated sample used is {8,11,11,11,11,12,12,12,13}), so the boundaries at 0 and 19 are distant, and the paper notes that 'this truncation will make little difference to the likelihood of samples whose allele lengths are not too close to these boundaries.' This is a reasonable practical defence for the simulated single-locus example. However, for the five-locus NSE dataset the joint type space is {0,…,19}^5, and the stationarity assumption for the MRCA type is now an artefact of five independent truncations whose combined effect on the likelihood surface has not been assessed. Readers might note that a sensitivity analysis varying the truncation boundaries, or reporting how far the observed allele lengths sit from the boundaries at each locus, would strengthen confidence that the stationarity approximation is not distorting the estimated likelihood surface for the real data.

**Status**: [Pending]

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## Detailed Comments (25)

### 1. Efficiency claim 'several orders of magnitude' overstated relative to Table 1 evidence

**Status**: [Pending]

**Quote**:
> Our approach substantially outperforms existing IS algorithms, with efficiency typically improved by several orders of magnitude.

**Feedback**:
The abstract asserts efficiency is 'typically improved by several orders of magnitude,' but Table 1 shows standard-error reduction factors of roughly 21 and 17 for θ=2.0 and θ=10.0 respectively — corresponding to variance reductions of ~440-fold and ~290-fold, i.e. at most two to three orders of magnitude. More critically, at θ=15.0 the paper itself notes the standard error changes by less than a factor of 2 rather than the expected √500 ≈ 22, far below 'several orders of magnitude.' The word 'typically' is doing substantial work: the claim holds only for moderate θ. It would be helpful to rewrite as 'efficiency improved by up to two to three orders of magnitude for moderate mutation rates, with smaller gains at high mutation rates' to accurately reflect the quantitative evidence.

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### 2. Topology count formula counts labeled histories, not topologies

**Status**: [Pending]

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

**Feedback**:
For n=4, the formula gives 4!·3!/2³ = 24·6/8 = 18, whereas the number of distinct rooted labeled tree topologies is (2·4−3)!! = 5!! = 15. The formula n!(n−1)!/2^{n−1} counts labeled histories (ordered sequences of coalescent events), not topologies. For n=3 the formula gives 3, which matches labeled histories but also matches topologies by coincidence. The paper explicitly says 'topologies,' but the formula counts something larger. It would be helpful to rewrite as 'there are $n!(n-1)!/2^{n-1}$ different possible labeled histories (ordered sequences of coalescent events) for the underlying trees.'

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### 3. Stationary distribution assumption for MRCA contradicted by infinite-sites application

**Status**: [Pending]

**Quote**:
> f the sample is well approximated by that of a random tree called the  $n$ -coalescent (Kingman, 1982a, b, c). At stationarity, under the neutrality assumption, the distribution of the type of the MRCA is given by the stationary distribution of the (mutation) Markov chain  $P$ . Conditionally on the genealogical tree and the type of the MRCA, types change along different branches of the tree as independent continuous time Markov chains with rate  $\theta / 2 = N\mu / \nu^2$  and transition matrix  $P$  (see for example Donnelly and Tavaré (1995)). Throughout the paper we shall adopt the coalescent approximation as the model underlying the data.
> 
> Define the typed ancestry  $\mathcal{A}$  of a sample to be its genealogical tree  $\mathcal{G}$ , together with the genetic type of the MRCA, and the

**Feedback**:
The general model statement asserts unconditionally that the MRCA type is drawn from the stationary distribution of P. However, the paper acknowledges in the Algorithm 1 discussion that 'For mutation models such as the infinite sites model (Section 5.5), in which the transition matrix P does not have a stationary distribution, it is usually sufficient to measure types relative to the type of the MRCA.' This creates an internal contradiction: the general model description is formally inapplicable to the infinite-sites model, which is one of the paper's primary applications. It would be helpful to add a parenthetical qualification such as '(or, for mutation models lacking a stationary distribution such as the infinite-sites model, types are measured relative to the MRCA type as described below)' immediately after 'stationary distribution of the (mutation) Markov chain P.'

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### 4. Index n vs k in mutation probability numerator in Theorem 1 proof

**Status**: [Pending]

**Quote**:
> = \frac {\pi \left(\alpha_ {1} , \dots , \alpha_ {n - 1} , \beta\right) \delta \theta P _ {\beta \alpha} / 2}{\pi \left(\alpha_ {1} , \dots , \alpha_ {n - 1} , \alpha\right)} + o (\delta) \\
> = \delta \frac {\theta}{2} \frac {\pi (\beta | A _ {k} - \alpha)}{\pi (\alpha | A _ {k} - \alpha)} P _ {\beta \alpha} + o (\delta).

**Feedback**:
The proof is working with a configuration of k lineages, so the tuple has k components: (α₁, …, α_{k−1}, α). However, the numerator and denominator of the displayed fraction write π(α₁, …, α_{n−1}, β) and π(α₁, …, α_{n−1}, α), using subscript n−1 instead of k−1. Since k is the running count of lineages (not equal to n in general), this is an index inconsistency. The second displayed line correctly uses A_k, so the error is confined to the intermediate fraction. It would be helpful to rewrite the subscripts from n−1 to k−1 throughout the intermediate fraction.

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### 5. Proof of property (a) of Proposition 1 omits the m=0 term

**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**:
For PIM, P^m = P for m ≥ 1 is correct, but P^0 = I ≠ P in general. The sum in equation (17) starts at m=0, contributing (n_α/n)(n/(n+θ))δ_{αβ}. Substituting P^m = P for m ≥ 1 and P^0 = I for m=0 gives π̂(β|A_n) = n_β/(n+θ) + θP_β/(n+θ), which equals equation (16). The final result is correct, but the stated reason omits the m=0 term. It would be helpful to rewrite the proof as: 'the result follows from the fact that, for PIM, P^m = P for m = 1, 2, …, so the m=0 term in equation (17) contributes n_β/(n+θ) and the remaining terms contribute θP_β/(n+θ), yielding equation (16).'

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### 6. Proof of property (d) concludes π̂ = π̂ instead of π̃ = π̂

**Status**: [Pending]

**Quote**:
> It then follows from equation (23) and mathematical induction that $M^{(n)} = (1 - \lambda_n)(I - \lambda_nP)^{-1}$, and so $\hat{\pi} = \hat{\pi}$.

**Feedback**:
The conclusion of the uniqueness proof is stated as 'π̂ = π̂', which is a tautology. The intended conclusion is that any distribution π̃ of the form (18) satisfying property (b) and the consistency condition (20) must equal π̂, i.e. π̃ = π̂. The induction argument shows that the matrices M^(n) for π̃ are uniquely determined by M^(1), which is fixed by property (b) to equal the M^(1) of π̂. The typographical error 'π̂ = π̂' should read 'π̃ = π̂' to make the uniqueness argument complete.

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### 7. Notation P_θ(H ∩ A_n) in equation (11) conflates set-intersection with joint probability

**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),

**Feedback**:
The third expression P_θ(H ∩ A_n)/P_θ(H|A_n) uses set-intersection notation for two objects from different spaces (H is a history/genealogy, A_n is observed data), which is non-standard and potentially confusing. The correct step is: π_θ(A_n|H)P_θ(H) = P_θ(A_n, H), and then P_θ(A_n, H)/P_θ(H|A_n) = P_θ(A_n) = L(θ). The final answer is correct but the intermediate notation is problematic. It would be helpful to rewrite P_θ(H ∩ A_n) as P_θ(H, A_n) throughout equation (11).

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### 8. MCMC ergodic average in equation (7) requires integrability condition not stated

**Status**: [Pending]

**Quote**:
> If $\mathcal{T}^{(1)}, \mathcal{T}^{(2)}, \ldots$ is a sample (after burn-in, and possibly thinning) from a Markov chain with stationary distribution $P_{\theta_0}(\mathcal{T} | A_n)$, then a relative likelihood surface for $\theta$ can be estimated by using

**Feedback**:
The ergodic average in equation (7) converges to L(θ)/L(θ₀) only when E_{P_{θ₀}}[P_θ(A_n,T)/P_{θ₀}(A_n,T)] < ∞, i.e. the ratio is integrable under the driving distribution. The paper's own discussion confirms that for the Fluctuate scheme this condition fails for θ > 2θ₀ (Stephens 1999), regardless of sample size. The section presents the approximation sign '≈' in equation (7) without stating this integrability condition, leaving readers unaware that the convergence claim may fail for θ substantially different from θ₀. It would be helpful to add a remark immediately after equation (7) directing readers to Section 6.1 for the conditions under which this ergodic average is reliable.

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### 9. Sample variance underestimation claim conflates bias with variability

**Status**: [Pending]

**Quote**:
> even assuming finite variance (which is not guaranteed) the distribution of the weights may be so highly skewed that, even for very large $M$, $\sigma^2$ is (with high probability) underestimated by $\hat{\sigma}^2$, and/or the normal asymptotic theory does not apply.

**Feedback**:
The sample variance σ̂² is an unbiased estimator of σ² regardless of skewness, by standard U-statistic theory. The issue with heavy-tailed weight distributions is not that σ̂² is biased downward in expectation, but that (a) σ̂² itself has high variance (requiring finite fourth moment for consistency), and (b) the CLT for the mean converges slowly. The statement conflates two distinct phenomena: variability of σ̂² in a single run versus failure of the CLT. It would be helpful to rewrite as 'the distribution of the weights may be so heavy-tailed that σ̂² has high variance and a single-run estimate of σ² is unreliable, even for large M' because the sample variance is unbiased for σ² under any distribution with finite variance.

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### 10. Standard error reduction factor of 17 at θ=10.0 treated identically to factor of 21 at θ=2.0

**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 theoretical reduction factor is √(10,000,000/20,000) = √500 ≈ 22.36. The observed factor of 21 at θ=2.0 is consistent with this, but the factor of 17 at θ=10.0 represents a ~23% shortfall, suggesting the short-run standard error at θ=10.0 is underestimated by roughly 22% relative to what the long-run ratio implies. The text treats both cases identically as 'reasonably accurate' when the evidence differs substantially. It would be helpful to rewrite as 'suggest that the standard error at θ=2.0 is being estimated reasonably accurately, while the factor of 17 at θ=10.0 indicates a moderate underestimate, consistent with mild skewness in the weight distribution at this value of θ.'

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### 11. Three Q_GT estimates at θ=15.0 span six orders of magnitude without explanation

**Status**: [Pending]

**Quote**:
> in our own implementation of the Griffiths–Tavaré proposal distribution, 1 million samples took 72 h and gave an estimate of the likelihood (dominated by a single large importance weight) of $4.93 \times 10^{-13}$. In contrast, 20000 iterations of a modified Griffiths–Tavaré scheme (implemented in the computer program SEQUENCE, kindly provided by R. C. Griffiths), which includes some of the computational tricks described in Griffiths and Tavaré (1994a), took 23 min and produced an estimate of $4.67 \times 10^{-12}$, with an estimated standard error of $8.72 \times 10^{-13}$.

**Feedback**:
Table 1 reports the Q_θ^GT estimate at θ=15.0 as 2.41×10⁻¹⁹ (20,000 samples), yet the text introduces two additional Q_GT estimates: 4.93×10⁻¹³ (1 million samples, authors' implementation) and 4.67×10⁻¹² (20,000 samples, SEQUENCE). These three estimates span six orders of magnitude (10⁻¹⁹ to 10⁻¹²). No explanation is given for why 1 million samples from the authors' Q_GT implementation yields an estimate an order of magnitude lower than 20,000 samples from SEQUENCE, nor is the relationship between these implementations and the Table 1 entry clarified. It would be helpful to add a sentence explaining the discrepancy between the two Q_GT implementations, because without this the numerical evidence for the 'longer runs are not always a satisfactory replacement' conclusion is internally inconsistent.

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### 12. Infinite-variance result scope stated too narrowly — applies to Fluctuate, not Q_θ^SD

**Status**: [Pending]

**Quote**:
> In fact Stephens (1999) has recently shown that for $\theta > 2 \theta_0$ the estimator has infinite variance.

**Feedback**:
The Stephens (1999) result applies specifically to the Fluctuate MCMC estimator (Method I of Kuhner et al.), which uses a Markov chain with stationary distribution P_{θ₀}(G̃|A_n) and reweights via equation (7). The sentence as written appears without specifying which estimator, so a reader could misread it as a general statement about any IS estimator for θ > 2θ₀, including Q_θ^SD. The authors' reply in the discussion confirms the result holds for Fluctuate regardless of sample size, and conjectures that Q_θ^SD partially avoids this problem. It would be helpful to rewrite as 'the Fluctuate estimator (based on sampling from P_{θ₀}(G̃|A_n)) has infinite variance for θ > 2θ₀' to make clear this result applies to the Kuhner et al. scheme and not to Q_θ^SD.

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### 13. Mutation matrix P (eq. 29) is parent-independent; efficiency comparison represents best case, not typical case

**Status**: [Pending]

**Quote**:
> Griffiths and Tavaré (1994a) also used their method to estimate likelihood curves for simulated data, consisting of 50 sequences of length 20, using the same model as above, but with $\theta = 1.0$ and
> 
> $$
> P = \left( \begin{array}{cc} 0.5 & 0.5 \\ 0.5 & 0.5 \end{array} \right). \tag{29}
> $$

**Feedback**:
The mutation matrix in equation (29) has all rows equal to (0.5, 0.5), which is the canonical parent-independent mutation (PIM) model. By Proposition 1(a), under PIM the proposal Q_θ^SD equals the optimal proposal Q_θ^*, so the IS estimator achieves the minimum possible variance. The efficiency comparison in Figs 2(a) and 2(b) therefore demonstrates the best-case advantage of Q_θ^SD over Q_θ^GT, not a typical-case advantage. The paper does not flag this, so a reader might interpret the 'substantially smaller' standard errors as representative of the general non-PIM setting. It would be helpful to add a sentence noting that because equation (29) is a PIM matrix, Proposition 1 guarantees Q_θ^SD is exactly optimal here, so this comparison represents an upper bound on the efficiency gain.

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### 14. Attributed cause of Fluctuate inaccuracy conflates IS-weight degeneracy with MCMC non-convergence

**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.

**Feedback**:
The section attributes underestimation to P_{θ₀}(G̃|A_n) being a poor approximation to P_θ(G̃|A_n), but the immediately following sentence establishes that for θ > 2θ₀ the Fluctuate estimator has infinite variance (Stephens 1999). These are two distinct failure modes: (1) poor mixing of the Markov chain (non-convergence), and (2) infinite variance of the IS weights even with a perfectly mixed chain. The word 'presumably' signals uncertainty, but the text does not distinguish the two mechanisms. It would be helpful to rewrite as 'because P_{θ₀}(G̃|A_n) is a poor IS proposal for P_θ(G̃|A_n) when θ is far from θ₀ — a problem formally confirmed by the infinite-variance result of Stephens (1999) for θ > 2θ₀ — and potentially also because of MCMC mixing failure' to distinguish IS-weight degeneracy from non-convergence.

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### 15. micsat outperforms Q_θ^SD on NSE data but efficiency claim is not revised

**Status**: [Pending]

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

**Feedback**:
The section explicitly states that micsat is more accurate for the NSE dataset, yet the paper's broader narrative frames Q_θ^SD as 'considerably more efficient than micsat.' For the simulated single-locus example Q_θ^SD uses 10,000 samples in ~30 s versus micsat's ~1.5 h, a ~180× speedup. But for the NSE five-locus dataset Q_θ^SD requires 500,000 samples per run at ~18 h each, while micsat requires only 10,000 draws in 4.5 h — and micsat is still more accurate. The efficiency advantage does not hold for the more realistic, higher-dimensional problem. The section does not reconcile this reversal with the earlier efficiency claims, nor does it explain what property of the five-locus problem causes the degradation. It would be helpful to explicitly acknowledge that for the NSE data the IS method does not outperform micsat in accuracy per unit time, and to identify the likely cause (e.g., approximation error from the Gaussian quadrature step in Appendix A).

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### 16. Shift-invariance claim under stepwise model does not hold for truncated type space

**Status**: [Pending]

**Quote**:
> Under this mutation model the joint distribution of sample configurations is invariant under the addition of any fixed number of repeats to each sampled allele (Moran, 1975).

**Feedback**:
The shift-invariance result of Moran (1975) holds for the stepwise mutation model on the full integer line. However, the very next paragraph introduces a truncated type space E = {0, 1, …, 19} with reflecting boundaries. On a truncated state space, the boundary rows have asymmetric transition probabilities, so the stationary distribution and likelihood are not invariant under an arbitrary shift. The paper uses this shift-invariance to justify centring the sample near 10 repeats, but this operation is valid only when shifted alleles remain far from the boundaries — a condition satisfied here but not stated as a prerequisite. It would be helpful to qualify the invariance claim as applying only on the infinite state space, with an explicit note that the truncation breaks this invariance and that the centring step is valid only when all allele lengths remain well interior to the truncated range.

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### 17. Causal claim about peaked curves conflates skewness with infinite-variance bias

**Status**: [Pending]

**Quote**:
> Since the IS function which these MCMC methods use is most efficient (in fact optimal) at $\theta_{0}$, and tends to become less efficient for $\theta$ away from $\theta_{0}$, 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 (which we believe helps to explain the overly peaked curves in Fig. 2(c) for example).

**Feedback**:
Increased skewness alone (finite but large variance) produces random errors, not systematic downward bias. It is specifically the infinite-variance / heavy-tail property that causes systematic underestimation, because the sample mean of an infinite-variance estimator is biased downward in finite samples. The text presents the skewness argument as if it logically entails the underestimation conclusion ('As a result such methods will tend to underestimate'), but this inference is only valid under the infinite-variance regime established by Stephens (1999). It would be helpful to rewrite as 'the distribution of the importance weights tends to become heavier-tailed for θ away from θ₀; in the extreme case where the variance of the weights is infinite (as established in Stephens (1999) for θ > 2θ₀ under the Fluctuate scheme), the sample mean of the weights is a downward-biased estimator of the true likelihood.'

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### 18. IS weight index collision in ancestral inference formula

**Status**: [Pending]

**Quote**:
> it follows from standard IS theory that the distribution with atoms of size $w_{i} / \sum_{i} w_{j}$ on histories $\mathcal{H}^{(i)}$ ($i = 1, \ldots, M$) is an approximation to the conditional distribution of $\mathcal{H}$ given $A_{n}$.

**Feedback**:
The expression uses i as both the free index in the numerator w_i and as the summation index in the denominator Σ_i w_j, while simultaneously using j as the summand. This creates an index collision: i appears as a free variable (selecting history H^(i)) and as a bound summation variable in the same expression. A reader could interpret Σ_i w_j as a sum over i of the constant w_j, which equals M·w_j, giving a nonsensical formula. The standard IS normalization formula is w_i / Σ_{j=1}^{M} w_j. It would be helpful to rewrite '$w_{i} / \sum_{i} w_{j}$' as '$w_{i} / \sum_{j=1}^{M} w_{j}$.'

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### 19. Markov structure loss claim should specify time-homogeneity, not Markov property

**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**:
Under a varying population size N(t), the coalescent retains a Markov structure — it is still a continuous-time Markov chain on sample configurations — but loses time-homogeneity: transition rates depend on the current backward time t as well as the current state. The Markov property itself is not lost; what is lost is the time-homogeneity that allows the process to be summarized without tracking elapsed time. The statement 'the simple Markov structure is lost' conflates time-homogeneity with the Markov property. It would be helpful to rewrite as 'the time-homogeneity of the underlying Markov processes is lost' because this distinction clarifies precisely why time information must be included in the missing data.

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### 20. Rejection control analogy incorrectly characterizes Griffiths–Tavaré discarding as a special case

**Status**: [Pending]

**Quote**:
> It may then be fruitful to apply the rejection control ideas of Liu et al. (1999), in which unpromising trees would be discarded before reaching the MRCA, with appropriate modifications of the weights of the undiscarded trees. (This is a more sophisticated version of the strategy of discarding trees with too many mutations which was used by Griffiths and Tavaré (1994a) and Nielsen (1997).)

**Feedback**:
Griffiths–Tavaré (1994a) and Nielsen (1997) discard trees unconditionally without reweighting survivors, so the resulting estimator is biased unless discarded histories have exactly zero model probability. Rejection control, by contrast, maintains unbiasedness by multiplying surviving particle weights by the reciprocal of the survival probability at each step. The claim that the earlier strategy is 'a less sophisticated version' of rejection control is therefore not accurate: the two procedures have different bias properties, and the earlier one is not a special case of the later one unless the survival probability is always 0 or 1. It would be helpful to rewrite the parenthetical as: 'Unlike the earlier strategy of Griffiths and Tavaré (1994a) and Nielsen (1997), which discards trees without reweighting and therefore introduces bias, rejection control maintains unbiasedness by multiplying surviving weights by the reciprocal of the retention probability at each step.'

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### 21. Rao–Blackwellization formula in Beaumont's discussion is missing a factor of 1/2

**Status**: [Pending]

**Quote**:
> $$ \pi(\theta|\mathcal{H}^{i}, A_{n}) = T^{i} \frac { (T^{i} \theta/2)^{m^{i}} \exp (-T^{i} \theta/2) }{ m^{i} ! } $$

**Feedback**:
Re-deriving from first principles: given genealogy H^i with total branch length T^i and m^i mutations, the likelihood is proportional to (θ/2)^{m^i} exp(−T^i θ/2). With a uniform prior, the posterior is Gamma(m^i+1, 2/T^i) with normalizing constant (T^i/2)^{m^i+1}/m^i!. The correctly normalized density is π(θ|H^i, A_n) = (T^i/2)^{m^i+1} θ^{m^i} exp(−T^i θ/2)/m^i!. The displayed formula T^i(T^i θ/2)^{m^i} exp(−T^i θ/2)/m^i! expands to (T^i)^{m^i+1} θ^{m^i} exp(−T^i θ/2)/(2^{m^i} m^i!), which is missing a factor of 1/2 in the leading prefactor compared to the correct (T^i/2)^{m^i+1}/m^i! = (T^i)^{m^i+1}/(2^{m^i+1} m^i!). The formula as written is unnormalized. It would be helpful to rewrite as π(θ|H^i, A_n) = (T^i/2)^{m^i+1} θ^{m^i} exp(−T^i θ/2)/m^i!.

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### 22. Control variate variance reduction factor stated as (1−ρ²)⁻¹ instead of (1−ρ²)

**Status**: [Pending]

**Quote**:
> Its asymptotic variance is $(1 - \rho_{\theta}^{2})^{-1}$ times smaller than that of expression (12), where typically $\rho_{\theta}^{2} = \operatorname{corr}^{2}\{l_{\theta}(\mathcal{H}^{(i)}), w_{\theta}^{\prime (i)}\}$ is large since $Q_{\theta}^{\mathrm{SD}} \doteq P_{\theta}(\mathcal{H}|A_n)$ implies $l_{\theta}(\mathcal{H}^{(i)}) \propto w_{\theta}^{\prime (i)}$.

**Feedback**:
Standard control variate theory states that Var(CV estimator) = (1 − ρ²) · Var(original estimator). The text states the asymptotic variance is '(1 − ρ_θ²)^{−1} times smaller,' which would mean the variance is larger by a factor (1 − ρ_θ²)^{−1} ≥ 1 — the opposite of the intended claim. Since ρ_θ² is stated to be large (close to 1), the factor (1 − ρ_θ²) is small, giving a large variance reduction. The correct statement is that the asymptotic variance of estimator (38) is (1 − ρ_θ²) times that of estimator (12). It would be helpful to rewrite as 'Its asymptotic variance is $(1 - \rho_{\theta}^{2})$ times that of expression (12).'

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### 23. Griffiths–Tavaré IS representation omits stationary distribution boundary term

**Status**: [Pending]

**Quote**:
> leading to an importance sampling representation
> 
> $$ p \left(H _ {0}\right) = E _ {q} \left\{f \left(H _ {0}\right) f \left(H _ {- 1}\right) \ldots f \left(H _ {- m}\right) \right\}, $$
> 
> with absorption at $-m$, where there first is a single ancestor of the sample.

**Feedback**:
Chen and Liu's contribution in the same discussion explicitly notes: 'The scale difference between these curves and those in Fig. 3 is due to the fact that the authors omit the term p_θ(H_{−m}), the stationary distribution of the mutation transition matrix' (caption to Fig. 10). In the Stephens–Donnelly representation (equation 35), the corresponding term p(H_{−m}) appears explicitly in the numerator. The Griffiths representation as displayed is therefore missing the boundary term for the stationary distribution of the single ancestor. It would be helpful to rewrite the displayed equation as p(H_0) = E_q{f(H_0) f(H_{−1}) … f(H_{−(m−1)}) p(H_{−m})} to include the boundary term confirmed missing by the scale discrepancy in Fig. 10.

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### 24. Consistency claim for Appendix A approximation conflates Monte Carlo consistency with quadrature accuracy

**Status**: [Pending]

**Quote**:
> 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 consistency invoked here is in M (number of IS replicates), not in s (number of quadrature points) or in the truncation of the matrix power series. A reader could incorrectly infer that using s=4 quadrature points is justified by this consistency argument, when in fact the argument says nothing about the error introduced by the Gaussian quadrature approximation itself — that error is fixed for any given s and does not vanish as M → ∞. It would be helpful to rewrite as: 'leads to an estimator (9) which is unbiased and consistent in the number of IS replicates M; however, the variance of the estimator will depend on the quality of the quadrature approximation, and the choice s=4 has not been validated against a finer quadrature rule.'

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### 25. Stationarity assumption for MRCA type may be distorted by truncated type space in five-locus NSE analysis

**Status**: [Pending]

**Quote**:
> Under this mutation model the joint distribution of sample configurations is invariant under the addition of any fixed number of repeats to each sampled allele (Moran, 1975).

**Feedback**:
The coalescent framework requires the MRCA type to be drawn from the stationary distribution ψ(·) of the mutation chain P. For the stepwise mutation model on the integers, the stationary distribution on an infinite state space is improper. The paper handles this by truncating to E = {0,…,19} with reflecting boundaries, inducing a proper but boundary-dependent stationary distribution. For the five-locus NSE dataset the joint type space is {0,…,19}^5, and the stationarity assumption for the MRCA type is now an artefact of five independent truncations whose combined effect on the likelihood surface has not been assessed. Readers might note that reporting how far the observed allele lengths at each locus sit from the truncation boundaries, or varying those boundaries in a sensitivity analysis, would strengthen confidence that the stationarity approximation is not distorting the estimated likelihood surface for the real data.

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