CJFAS: 1ª Revisão

The paper is not well written. I have listed major comments below. More specific comments and some grammatical corrections are inserted directly in the attached pdf file. The authors advocate a fairly complex model for limited data. They need to better measure and describe the advantages of their proposed approach versus the simpler and commonly used design-based approach.

A: See letter to editor point 1).

1. The authors estimate age compositions separately from spatial stock density, or more specifically the component of stock density sampled by the trawl. However, this will not usually be appropriate because there will be both spatial variations in stock density and stock age compositions. For example, if juveniles are distributed closer to shore, near or in nursery areas, then one cannot estimate the age composition separately from spatial stock density. This is common for many groundfish species. The authors recognize that fish tend to distribute differently by size categories, and they should also recognize that the local abundance of the size categories will be different as well, with greater numbers of smaller sized fish for a species. For example, consider the very simple situation of separate inshore and offshore areas, within which a species is homogeneously distributed in two size classes: 100 small and 900 large offshore, and 3900 small and 100 large inshore. The combined age composition for both areas is (S,L)=(0.8,0.2), whereas averaging the age compositions for the two regions gives (S,L)=(0.54,0.46). The latter result is wrong because the total age-composition for both regions should be computed as a weighted-average, where the weights depend on total stock numbers in each region. L162-163. The authors describe a procedure to check if age-proportions are related to stock density. It seems incomplete. If local abundance (C_ih) and age proportions (P_ijh) are statistically independent then the proposed approach is OK. However, testing for independence by fitting a model with total catch as a covariate may not be enough.

A: See letter to editor point 2).

2. The authors need to better describe the procedure used to calibrate the survey data. For example, if there are no covariate effects so that the GLM contained only a constant intercept term, would the calibrated and un-calibrated data be identical? If not, then the authors should defend why this is appropriate.

A: See letter to editor point 3).

3. The authors should ground-truth their proposed methods using some simulations. They should assess if their methods produce mean or median unbiased estimates, and if their 95% credibility intervals have a frequentist interpretation (i.e. cover the true values 95% of the time).

A: Under the new specification it is clear that the procedure is not biased. Both methods, model based geostatistics and compositional data analysis, are validated statistically so there's no reason why the combination of both shouldn't give valid results. On the other hand a simulation study is outside the scope of the paper and will contribute to increase its size significantly and make it more difficult to follow. Anyway we're providing a limited simulation study to show that the method is providing valid results.

4. lines 6 - 8 “methods, providing means to overcome difficulties in obtaining the analytical expression of abundance at age.” This sentence is too vague to be useful. What problems are overcome?

A: See letter to editor point 4).

5. lines 13 – 14 “provide an overview of abundance along different perspectives.” This sentence is too vague to be useful.

A: See letter to editor point 4).

6. line 45 - correlations will have nothing to do with the modeling methods.

A: See letter to editor point 4).

7. line 57 - A general style comment. Sections do not present anything - they are just places where text is presented.

A: See letter to editor point 4).

8. line 94 - Sample size was said to be limited to 97 hauls per year; however, there are usually fewer hauls than this reported in Table 1. Why the difference? Also, if there are 48 strata then there needs to be at least 96 hauls to achieve 2 hauls per strata. Clearly in most years many strata had no or one haul. How were design-based standard deviations computed in this case?

A: The sampling programme is not always achiaveable in practice due to operational constraints. This imposes no problems for the model-based approach for the analysis but requires some sort decision within the design-based in which case the variance is computed with a linear regression between variance and mean computed for the strata with 2 samples. This is now explained on Section "Material".

9. line 97 - How were ages determined? Were age-length keys used? Were ages estimated or measured for each fish? This should be described.

A: Yes, we use ALK as now mentioned on Section "Material".

10. line 109 “and taking into account the nature of each one” what does this mean? For example, how is abundance taken into account when estimating P_i?

A: This sentence reffers to the fact that sub-models were adjusted to the specific type of variables, counts for the spatial behaviour and proportions for the population structure. See letter to editor point 4).

11. line 115 - Should give a "heads-up" that the choice of a will be described later.

A: Done.

12. line 120 “μˆi = μ¯i, the vector of marginal arithmetic means” This will usually not be appropriate. See Major Comment 1, attached.

A: See letter to editor point 2).

13. lines 131 – 132 “the reference conditions and adding the deviance residuals” This requires further explanation. See note 2 in attachment.

A: GLM is no longer used. See letter to editor point 3).

14. lines 133 – 134 A NB GLM will also be sensitive to large catch. Keep in mind that the mle of the NB mean is the sample mean, which is not robust.

A: GLM is no longer used. See letter to editor point 3).

15. lines 161 – 163 The second model needs to be described better. Write it down.

A: See letter to editor point 3).

16. lines 165 – 168 I did not understand this. What is meant by inducing a small average change? Try being simple. Are the results sensitive to a difference choice of a and the constant? What happens if a=5 and the constant=0.01?

A: The results are not dependent on the choice of age. Null values brings usual problems as for other models involving logarithms and there is not a standard way of dealing with it. We have adopted the multiplicative replacement strategy (Martín-Fernández et.al 2003). This is now explained in the manuscript on subsection "Compositional Data Analysis".

17. line 170 A dome in the age-proportions does not mean survey catchability is domed. The right-hand part of the curve may decrease because of mortality and not catchability.

A: Yes, agreed. The manuscript was revised to account for this comment.

18. line 191 - Need to better describe the rationale for this. It seems to be that the authors are potentially removing variability in the calibrated observations, and this would not get captured in the Bayesian inferences. But perhaps I have missed something. If so, the authors should improve their description of the procedure. See Note 2 above.

A: The procedure was detrending and filtering the observations and calibrating the observations to the same catch conditions. However, the improvements on the analysis were marginal and a square root transformation works well with the advantage of simplifying the model removing the need for such adjustments. See letter to editor point 3).

19. line 192 “Geostatistical analysis adopted” poor style

A: See letter to editor point 4).

20. line 203 - Seems odd to use a discrete distribution for a variance parameter prior. The rationale for the choice should be described.

A: This is an approach used in Bayesian analysis to reduce complexity of the sampling algorithms, see Gelman et. at. (2000) and references were added to the MS. In out model this is used for the correlation and relative nugget parameter and not for the variance of the Gaussian field follow the software implementation by Ribeiro and Diggle, 2001. In practice this can be tested with different number of support points allowing for the control of the approximation in the predictions.

21. lines 204 – 205 “These probabilities…..0 and 2” Not clear what is going on here. Describe better.

A: This is an ad-hoc prior that proved reasonable for our application. Our main objective was to set a prior that included a high probability of values below 0.5 but still give some probability of having values between 1 and 2. High values, greater than one would already imply little or hardly to detect spatial effect. We decide to set 2 as an upper limit. In our analysis we have also tried with different values in assess the sensitivity.

22. line 215 - This seems too subjective. I think for survey analysis that people like more objective inferences. How sensitive are the statistical inferences (medians and credible intervals) to the choice of priors? Is it a problem? See Major note 3 above.

A: A sensitivity analysis was carried out and the impact is small but in those years with less information about the parameters, in particular \tau^2, different priors will result in different posteriors once that the data are not able to update the prior. Under this circumstances our decision was to set priors based on our knowledge and experience about the stochastic process, as expected on Bayesian analysis.

As a general point we emphasize tried to set (subjective) priors which reflect our previous experience analysing data. There are no definitive pointers for reference and/or non-informative priors for correlation (and relative nugget) parameters for geostatistical models.

23. line 218 - it would be better to defend this when introducing the GLM. Explain why the log link is better to use.

A: GLM's are no longer used. See letter to editor point 3).

24. line 224 - Describe how the design-based standard error were computed, particularly when the sampling design was changed to systematic since 2005? Also, as mentioned previously, it seems that there are many strata with less than 2 samples.

A: See answer to Q8.

25. line 227 - what values? Y or RMAD. The precision is higher.

A: See letter to editor point 4).

26. line 232 - This does not seem to be a good reason. I think you could also argue that groups of null catches would get less weight in the geostatistical analysis, which would lead to higher estimates compared to the sample mean. A more convincing explanation is required.

A: There was an error on the code used to run the analysis and the back transformation was using the wrong variance estimate, inducing a bias on the results. The new transformation, square root, was checked and the correct variance estimate is being used.

27. line 233 – why was the higher precision obtained with design estimators apparently over-optimistic for BTS?

A: The analysis was extended to include a comparison between the average distance between locations within each strata and the estimate of \phi, were it is shown that the observations are likely to be correlated and the variance under-estimated. See end of Section "Results".

28. line 235 - But the designed-based approach is highly stratified (less than 2 observations per strata). There can be little residual correlation in the responses in this situation. The mean-model has 48 parameters (i.e. the strata) in the design-based approach. I am again unconvinced by this explanation, more is required.

A: See answer to Q27.

29. line 249 - So does the design-based approach?

A: See answer to Q27.

30. line 250 - and I also do not accept it, for the same reasons.

A: See answer to Q27.

31. line 251 - I would prefer the author show the unstandardized results.

A: Done.

32. line 259 - Defend why this is an improvement.

A: The discussion was revised deeply focusing more on supporting the advantages of the model. This doubt is now clarified.

33. line 274 - vague text

A: See letter to editor point 4).

34. line 281 – “supporting our decision on exploratory data analysis” What does this mean? Explain.

A: This comment is not relevant anymore due to model development. See letter to editor point 2).

35. line 287 - This again raises the issue of robustness to assumptions. The authors are advocating a fairly complex model for limited data? What are the advantages? See major note 3 above.

A: The new model is now simpler and more focused to the point being made. See letter to editor point 1).

a) The authors proposed a new methodology to estimate abundance at age from trawl surveys and obtained different results from an existing method. However, the current manuscript does not show clearly the novelty and superiority of this new method compared to others. I would prefer structure in the introduction section, in which problems regarding existing methods are pointed out, if any, and then new methods are proposed as a solution. It would also be necessary to emphasize the generality of this methodology.

A: Regarding differences in the results for both approaches, see letter to editor point 2) and answer to Q26 of referee #1. The methodology and discussion were revised following this comment to clarify the novelty and advantages of the proposed model and how it fits in the framework of multivariate space-time modeling.

b) The two sub-models of this study analyze separately the same age composition data from trawl surveys and results from the two are integrated at the final stage. My major concern is that the age composition analysis does not consider spatial correlation in estimating age-structure in each year. As the authors point out in line 235, ignoring spatial correlation is likely to lead to an underestimation of variances. In particular, since sampling designs, including sampling locations, were changed in 2005, spatial effects should be incorporated by some kind of method in estimating age structures. In addition, if hake distribution is highly dependent on age, it would be proper to apply geostatistical models to different ages instead of age-aggregated data. Thus, I am suspicious about the validity of this new methodology, in which the two sub-models analyze the same data independently. I think that a statistically rigorous model to analyze age and spatial effects simultaneously is necessary to solve issues the authors raised.

A: The discussion was revised to focus on the comparison of this method with other methods available, replying to this comment. Also, see previous answer and comments to the editor regarding the factoring of the joint distribution.

c) The authors often refer to the small sample size of the BTS as a reason that more complicated models are difficult to apply. However, one of the major advantages of Bayesian methods is that they can deal with small data sets by incorporating proper prior information. I suspect that this model does not sufficiently take advantage of Bayesian approaches.

A: There is a balance between the information contained on the data and the information contain on the priors. If the dataset is too small the information contained is limited and the prior may condition the results too much. Note that referee #1 on Q22 comments on the opposite direction, stating that our analysis is "too subjective". This reflects a controversy in the arena of adoption of Bayesian methods. The methodology used keeps a good balance between both as we tried to expose in our new version. We have tried to further discuss and justify our choice of priors based on previous knowledgement and understanding of the process.

d) The length of this manuscript is compact and I prefer such shorter papers. However, this manuscript is not easy to understand as to what the authors really did in this analysis. For example, what is meant by “abundance” that is used frequently in the text, though I assumed "abundance in number". Additionally, some texts in the results section (lines 163-168, 175-181, 192-193, 199-210, 216-218 etc) should be included in the methods section. I would prefer an explanation style regarding geostatistics used in Jardim and Ribeiro (2007).

A: See letter to editor point 4).

Lines 55-67. Most of the last paragraph of the introduction section is redundant and, if necessary, some texts should be moved to the material section.

A: See letter to editor point 4).

Lines 80-95. I would like to clarify one point regarding sample design: was sampling conducted in all 4 depth ranges in each location? Or depth was selected randomly as well? If the latter is correct and hake abundance and/or age composition depend on trawl depth, how was this depth effect standardized through this analysis?

A: The stratification combines 12 sectors with 4 depth ranges creating 48 strata. The sampling design allocates 2 locations to each stratum. Within the stratum the locations are not fully randomized to avoid non-trawlable grounds. The procedure was built so that all depths are covered. We have revised the description in the MS.

Lines 104-124. Subscripts of parameters should be explained more carefully, though most of them might be expected. For example, what is “n” and “m” in line 106 and “H” in line 113? A parameter P has subscripts "ij" in line105 and "ijh" in line 113. H has subscript i in line 121. These are very confusing.

A: A major revision was carried out in the notation, also considering the modifications in the model. See letter to editor point 4).

Lines 112-114. My understanding is that this model does not consider abundance (sample size) differences among locations in analyzing age composition. If sample size is too small as a representative value in a location, such age composition data could impact final results wrongly. Did the authors conduct any pre-treatments like omitting data sets with small sample sizes?

A: See letter to editor point 2). Also notice the geoestatistical model with square root transformation will induce a mean-variance relation.

Lines 114-116. The explanation is unclear.

A: See letter to editor point 4).

Lines 122-124. When parametric bootstrap is conducted, back-transformed P will not be between 0 and 1 in some cases. Were any constraints placed to D in the bootstrap?

A: Yes, the "closure operation" is applied to the back transformed data ensuring the compositional structure. The description in subsection "compositional data analysis" was revised accordingly.

Lines 161-163. I did not quite follow the explanation. What did the authors actually conduct?

A: See letter to editor point 3).

Line 167. What is the unit of "3"?

A: percentual. The missing symbol "%", it is now included.

Lines 171-173. As the authors point out, ageing errors seem to be large for hake. It would have been interesting to know the impact of this source of uncertainty. Even if this factor is difficult to incorporate in the model, it would be nice to add information on how large ageing errors potentially are.

A: There is not a clear knowledge about the size of the ageing errors. Recent tagging experiments show it exists but the experiments were quite limited and its still difficult to extrapolate for the population. We agree with the comment but the subject is outside the scope of the paper.

Line 175. Diagnostics regarding model fitting should be shown.

A: See letter to editor point 3).

Line 192. What is the reason for selecting the exponential correlation function? If there is not strong evidence, it would be necessary to explore sensitivity to other function forms.

A: The exponential function is common and was used in previous papers dealing with the same data (Jardim and Ribeiro Jr 2007, 2008). The main relevant difference with other functions is the behavior at short distances, which is impossible to infer from available data due tot the lack of observations at shor distances and limitations on replicating observations. The only impact expected by considering another function with a more unstructured behavior at short distances, like Gaussian correlation function, would increase values of \tau^2.

Lines 196-198. Probably the authors' judgment is proper, but the "90 degree rotation" does not really impact the final results?

A: Considering the rectangular shape of the Portuguese coast it is not expected to have a relevant impact. The main idea is to borrow information from booth areas to improve the estimates of the covariance function parameters. It is a very technical subject that we consider of minor importance for the main message of the paper and it was removed from the manuscript.

Lines 204-205. This sentence is not clear.

A: See letter to editor point 4).

Line 209. What is "flat prior"? What is the range of the prior distribution?

A: Priors are further explained now and references given when adopting usual choices. See also letter to editor point 4).

Line 213. The data did not update tau distribution considerably. In this case, it would be better to use different prior distribution functions as sensitivity tests.

A: See answer to Q22 of referee #1.

Line 226. Replace "seem" with "seen".

A: Done.

Lines 216-238. The authors consider that this geostatistical model showed considerably lower estimates than the design statistics due to "screen effect". However, they do not provide a distinct reason why this new model is considered to be more proper. Though I realize this may not be easy to implement, methods such as cross validation and operating model approach can be used to show the geostatistical model works effectively and reasonably.

A: See answer to Q26 of referee #1.

Line 236. The unit of "14 and 25" is "%"?

A: Yes, text was revised.

Lines 255-257. This sentence is unclear.

A: See letter to editor point 4).

Lines 280-281. It would be better to elaborate on what was done in more detail, since this point may be critical.

A: See letter to editor point 2).

Tables 1,2. What is the unit of abundance?

A: Number of individuals per hour. Table headings fixed.

Figure 4. The order of sub-panels looks strange to me (1998-2006 and 1989-1997). Lower panels should be moved to the upper section to arrange panels in the order of time.

A: Done.

Figure 5. It might be nice to add design-based estimates to the figure.

A: Done.

Figure 7. The order of sub-panels looks strange to me (3, 4, 5, 0, 1, 2). If possible, it would be nice to include information on estimate uncertainties.

A: Done.

The two reviewers have identified major flaws in the MS and recommend rejection. However, both reviewers encourage resubmission of a new manuscript. Both reviewers also found that the MS was poorly prepared and hard to follow. I agree with the reviewers’ assessment and recommend that the MS be rejected in its current form, but submission of a new MS encouraged. The revised MS would be treated as a new submission, and a response letter is needed from the authors detailing how they address the reviewers' comments.

A: The reviewers comments were carefully considered and a major revision was undertaken focusing on removing unnecessary complexities in the modelling strategies whereas preserving the essence of the proposal which is to combine compositional data analysis with the Bayesian geostatistical analysis which we belive is the core contribution in the MS. For instance we now follow a transformed Gaussian model for the geostatistical analysis, which has a more straighforward implementation and interpretation. This avoids issues raised by the referees which has being discussed and questioned concerning the previously adopted negative-binomial GLM model, without impact on the quality of the results. Discussions on the the standardizations used before are no longer needed which has also prevented some bias in the analyses. More importantly ths allows for a shorter and more objective description of the proposed approach, removing unnecessary distractions.

The referee's comments highlighted the need to extend the model in order to make it more general. Some of the subjects included on the data analysis were removed and the core of the paper and more focus was given to the combined model. The combined model is now presented as factoring the joint distribution of total abundance and age compositions which avoids explicity assumption of independence between both sub-models. The text was restructured in a more clear format, with an attempt to set a better to follow mathematical notation. Replies to specific points are included on the next bullet points. The reply to the referees comments refers to these bullet points when relevant.

1) Both referees asked for comparisons between the model proposed and the design-based estimates in order to show the its superiority. Note that a major part of this discussion is about the design-based versus model-based approaches which is clearly outside the scope of the paper. Our usage of the design-based estimates is mainly to provide a reference given by an usually adopted strategy of analysis.for comparison and the Discussions on the differences between both are constrained to the relevant purposes of the paper. We refer to further a discussion on design versus model based approaches given by Jardim and Ribeiro Jr (2008???) and references thereof.

2) Referees' comments claims for a more generic model, worring about bias possibly induced by the independence assumption between the population structure and abundance levels sub-models in the previous submission. Our decision was to further develop the model addressing this problem by defining sub-models as a result of factoring the joint distribution in a product of the marginal abundance distribution and conditional on that, a population structure distribution. This clarifies the fitting in the space-time modeling framework applied to fish abundance. The entire manuscript was revised as a consequence of this development.

3) Several referees' comments, albeit pertinent, were related with issues that we did not considered central to the main subject of the paper highlighting the fact there were distracting topics. For the sake of objectivity we have critically revised the real contribution of such topics. Among them there was the calibration with a GLM which lead to little if any improvement on the expense of higher complexity and bringin issues on possible bias caused by the usage of the residuals. The GLM was replaced by the square root transformation showing comparable results in accordance with earlier work by Jardim & Ribeiro (2008) and avoiding the problem with null observations caused by the log transform.

4) The manuscript was criticized by the poor writing style, unclear mathematical notation and inconsistencies regarding the objectives. A deep revision was carried out addressing these issues and the paper has now more focused on the model compared with the study case, reflecting its mais objective. Mathematical notation was revised aiming for greater consistency and clarity and better explained.