I would like to congratulate the authors on their interesting approach on modelling abundance of game species from harvest data. Although, inhomogeneous Poisson point patterns (iPPP) are not new to ecology, they are still underrepresented in practice. Therefore, I enjoyed reading your manuscript. The manuscript describes a framework to utilize harvest data to estimate animal abundance of game species. As the authors describe knowledge on animal abundance is often essential to inform wildlife management. However abundances are not always readily available, while harvest data is usually available across large geographical extents and for long time periods. This makes harvest data a popular choice for the modelling of abundance of game species. In this paper, the authors present a statistical framework, based on a thinned iPPP, that accommodates for lack of hunting effort information and the misalignment in the resolution of harvest data.
Given the increasing abundance of some game species (i.e. wild boar, roe deer in Europe and America), and the need for targeted management actions in these cases, this paper is timely and relevant. Overall, the paper is well-written and the statistical methods are sound. Nevertheless, I have some remarks about the work present in the manuscript.
Main remarks:
While the introduction naturally introduces many of the important topics of the article, I now miss a more in-depth introduction on the methods used (inhomogeneous Poisson point process model) and how precisely they overcome issues of harvest data. From L63-74 the limitations of harvest data are discussed and then on L75-77 it is implied that the iPPP overcomes these limitations, but it is not specifically pinpointed how it does so.
Most of the methods are clearly covered in the Materials and methods sections. However, I miss some critical information in this section.
First, precise information on harvest yields is missing. I would at least include the mean (and range) harvest yield per hunting estate at L106. Especially since this is your response variable in the iPPP model.

For some methods it was unclear to me what the exact sample sizes were. For example: density estimates derived from the Random Ecounter Model, distance sampling model and KAI (L118-125). What are locations in these settings? Individual locations or hunting estates? If they are hunting estates, are there multiple samples per hunting estate?

I would also appreciate it if the authors would more elaborately describe the change-of-support procedure on L141, which is unclear to me from the main text alone.

Parameters in the formulas on L135-136 and L143 are defined, the range of indices (i and h) are not specified.

More fundamental, Methods in Ecology and Evolution aspires to publish novel methodology, yet the authors acknowledge on L155-156 that the iPPP has already been used in the context of abundance-estimation from presence-only data. Ok, the specific data-source may be different. Still, I think the authors would highlight the novelty (in terms of methodology) of their work relative to that of (Dorazio 2014; Renner et al. 2019; Lauret et al. 2021).

L199: I do not agree with the authors using non-informative priors for all parameters. Example: in the discussion they mention that values of ~1 are unrealistic for the thinning parameter, yet they use a non-informative prior. In this setting I would expect a more informative prior to regularize the thinning parameter to some extent. Also, please, include some more information on what “non-informative prior” means. Are they uniform priors? normal priors? student t priors? what is the mean and scale?

L213: Please mention why you choose to remove the change-of-support process from your simulation study. This is an essential part of your model, as you mention earlier there is often a spatial misalignment in harvest data. Hence, if I am interested in using your model I will most likely need the change-of-support procedure. And thus I am interested in how the model including this procedure performs in a simulation study. If run times are the reason for simplifying the simulations, I would encourage the authors to use a high-performance computing environment. If you have a reason to think that a model without the change-of-support procedure performs similar to the full model, please mention it explicitly.
Apart from my doubts about excluding the change-of-support procedure in your simulations, I think the article would benefit from a more extensive simulation setup. I would extend the simulation to include at least:
3 different values of the parameters α_0 en β_0. For example: β_0 = 0.5 (low), 2 (med) and 4 (high) and similar for the intercept of the thinning parmeter α_0 = -1.5 (low), -0.5 (med), 0.5 (high).
A situation where precise information about hunting effort is available vs. the game target-group.
Change-of-support included vs excluded.

I consider these scenarios important as they assess model performance in some of the key aspects of its intended use. As a reader, I would want to know how my model performs under different scenarios of species catchability and overall abundance (a). I would also want to know how much the performance suffers from the lack of precise information on hunting effort (b) or from the exclusion of the change-of-support procedure (c).

Additionally, I think the authors should consider extending their approach with the inclusion of latent random effects (spatially structured and unstructured), at least in the ecological process model. Currently, they mention these effects on L377-381 in their discussion. However, these random effects are essential for estimating latent spatial correlations in the data. Including them would make their framework an even more “general framework for modelling harvest data”, which is what the authors aim for. In that sense, the Log-Gaussian Cox process seems a natural framework. Moreover the sharing of latent random effects between the thinning process and the ecological process may allow for estimating the degree to which abundance and harvest efficiency (percentage of population culled) are stochastically dependent, see Watson et al. 2019.

Watson J., Zidek J.V. & Shaddick G. (2019). A general theory for preferential sampling in environmental networks. The Annals of Applied Statistics 13 (4): 2662–2700.
In general the results and discussion section are well-structured and report the most important findings. However I sometimes miss a comparison of the study results to the literature.
L342-343 (example): severe bias in the observational process (here thinning parameter model) are a well-known issue in hierarchical models (see paper by Barker et al. 2018, and some other as weel). In my opinion, the authors should at least mention some of these previous works.

Barker R.J., Schofield M.R., Link W.A. & Sauer J.R. (2018). On the reliability of N-mixture models for count data. Biometrics 74 (1): 369–377. https://doi.org/10.1111/biom.12734.

Lastly the authors should warn the readers about using the model to predict absolute abundances from harvest data. This should be explicitly mentioned at L367-369. Also see Barker et al. 2018, and your own simulation results, i.e., biased β_0.

Minor remarks:
I have highlighted minor remarks in the annotated pdf in the attachment.

Compared to the previous round of revision, the manuscript presented by the authors has improved in many regards. Two of the reviewers asked to perform additional simulations exploring the impact of overall catchability, abundance and unmodelled heterogeneity on parameter estimates. I am delighted to see that the authors have expanded upon their original simulations to meet these demands. Furthermore, the authors have made efforts to clarify their use of non-informative priors and the change-of-support procedures. While the authors have also made an effort to provide technical aspects on inhomogeneous Poisson point patterns (iPPP) at the beginning of their Methods section, the manuscript currently lacks an introduction on the historic and current use of this method in ecology, which would help to situate the approach relative to the literature. The authors should include a few lines providing this background in the introduction, including references to applications of iPPP in ecology (for instance before L84).
I appreciate that the authors have now clearly indicated the limitations of their approach regarding the estimation of absolute abundances, something that was missing from the previous manuscript. My suggestion on including spatial random effects in their modelling exercise is rebutted by the authors. However, as I understand it, they prefer this manuscript to be accessible to a wider audience, including ecologist without a strong analytical background. I can relate to the challenges that come with finding the right balance between model complexity and accessibility. Therefore I will not require that authors extend their model prior to recommending acceptation of their work. However, I encourage authors to make future amendments in this regard. I am happy to help them with the implementation of efficient ways of addressing spatial autocorrelation in their data should they be interested to work on this in the future.
Provided that the authors include additional background on the iPPP in their introduction, I recommend to accept their manuscript for publication in Methods in Ecology and Evolution. They have adequately addressed all my other comments, for which I congratulate them. I consider their work a meaningful contribution to the journal, which I believe to be of interest to its readership. Finally, I advise the authors to carefully scrutinize their manuscript before final publication, as I could still find minor errors throughout.