Overall it seems there is strong disagreement over competing data analyses on what is already a highly contentious issue, which has significant implications in terms of ecology and agriculture. I have been asked to comment on one small part of the ongoing discussion, which I will do - however, my overall, strongest recommendation is that, given the importance of the underlying issue (both scientifically and politically) that a proper investigation be conducted to establish an agreed position involving all parties. A continuing to-and-fro among different sets of authors - each, I am sure, well-meaning in their own ways - serves little purpose, and there are better, more efficient and effective ways of resolving disagreements than in the pages of an academic journal.

1) Section 2.1. I agree with the authors of the current contribution here that use of an offset here is likely a requirement, and that the comments from the Mills et al. (4) are naïve at best - it isn't helpful to think of an offset as equivalent to setting a regression coefficient to 1.0, as of course the issue is that this is a log-linear scale and the point is that (under the Poisson) we assume proportional rates. I agree that it does not seem to make sense that the herd breakdowns vary only very slightly (the parameter value of 0.04) with the number of herds, although I would caution here only that it is possible some other variable/term in the model might be related to the number of herds, hence suppressing the parameter value (when including number of herds as a regression term rather than as an offset) owing to collinearity.

2) I have personally written (Brewer et al, 2016 - https://doi.org/10.1111/2041-210X.12541 ) about the dangers of relying on the theoretical distinctions between AIC/AICc and BIC, so it should be no surprise that I share the current authors' suspicions on the preference expressed in Mills et al. (4) for BIC. Also, why are the AICc values for Models 1 and 3 so much higher than the null model in Table 1? Is this just a feature of the small-sample correction? Otherwise I would not expect this at all (if I'm understand what the null model is, correctly); in the absence of other explanations here, given the high number of parameters in models 1 and 3 I would suspect poor model fitting with inflated variances due to collinearity. So, I agree with the current authors here, on the basis of the evidence in front of me (Sections 2.2+2.3, Table 1, supplementary material).

3) The discussion on Bayesian models claims that the authors of Mills et al. (4) made coding errors. I do feel that then Mills et al. should be able to examine and (if relevant) correct these errors, and formally issue a correction in the pages of the journal. Otherwise, I don't feel I have sufficient information to comment further here.

4) I agree with the current authors' concerns on the statistical audit. I would go so far as to say that, given the important of the topic of this discussion, any audit should be carried out openly and transparently.

5) Section 5 on the neighbouring area study - again, from what I can see here, I would broadly agree with the concerns of the current authors.

6) To clarify; I have no issue with the modelling of counts, as the use of a Poisson-form log-linear model is, in effect, modelling rates. To be more precise, I would suggest that the problem is not that Mills et al. (4) modelled counts, but that they did not properly scale those counts by use of an appropriate offset - and again, I am saying this on the basis of the evidence of the current work (only).

7) Finally, I would like to address the quotation from Donnelly (16):
"the suggestion of requiring independent replication of specific statistical analyses as a general check before publication seems not merely unnecessary but a misuse of relatively scarce expertise".
The point to me here is not that work should be "replicated" as such, but that work should be verifiable. The authors of Mills et al. (4) have apparently made their work - at least that related to the 2024 journal papers - available openly, and this is the key; openness and transparency are vital. I would even go as far to say that, in such a contentious area as this, it is naïve to imagine that a single analysis by a particular group of scientists should be seen as sufficient.

Minor points:
I assume line 2 of Section 1 should have "affect", not "effect". (Page 1 Line 41/42).

Page 2 line 36/37 - presume this should be "Biological plausibility"?

The short sentence in line 59 of Page 2 beginning "LOOCV,..." does not make sense.