Dujon et al. presents an interesting study that investigates the relationship between the selected phenotypic traits reflecting reproductive effort (including the type of placentation, litter size, gestation length and lactation length) and the risk of mortality from cancer in 144 mammalian species. Their study is based on data provided by Vincze et al. (2022, Nature 601: 263), Species360 and the Zoological Information Management System (ZIMS). They hypothesized that cancer mortality risk will increase with the increasing level of placentation, litter size, gestation length and lactation length. The authors found that species with a highly invasive (haemochorial) placentation type had a higher cancer mortality risk compared to those having a less invasive (epitheliochorial, endotheliochorial) placentation. The presented results seem to support the antagonistic pleiotropy hypothesis proposed by Williams (1957, Evolution 11: 398) that predicts a life-history trade-off between reproductive fitness and maintenance of the somatic tissues. However, the authors should address and clarify several conceptual, factual and methodological points in their manuscript before its possible publication.

Comments to address
1. I believe that the authors should clarify if a relationship exists between the type of placentation and reproductive effort in the mammalian species studied. They should also explain the potential evolutionary basis of such relationship and modify the text of the introduction to fully justify the hypotheses tested.
2. The cancer mortality risk was estimated as the ratio between the number of cancer-related deaths and the total number of individuals whose post-mortem pathological records were entered in the database. A species was considered to have cancer if at least one individual with post-mortem pathological record was diagnosed with cancer. Nevertheless, the authors did not take into account the potential contribution of the degree of cancer incidence in a given species, for example as the statistical weight – the proportion of individuals that died due to cancer. This factor could also influence the results of their statistical analyses. Could the authors, please, consider including the species-specific degree of cancer incidence in their analyses?
3. Data set used in this study is missing some taxa, for example Insectivora, Cetacea, Proboscidea and Lagomorpha, which are, in my opinion, crucial for the understanding of mammal evolution. I do understand that the authors excluded all species that were subject to domestication due to the potential effect of inbreeding on the risk of cancer development. But at the same time, I believe there is no reason to exclude these taxa from the analyses. Insectivora are the most primitive placental order and are the ones from which other extant placental mammals have evolved. Infraorder Cetacea and order Proboscidea contain two of the longest living mammal species in the world, Balaena mysticetus and Loxodonta africana, respectively. In addition, extant elephant species can live longer in captivity than in wild. Including representatives of these taxa could improve the strength of their analyses. Therefore, I think the authors should expand their data set by species from all of the above listed taxa.
4. To the best of my knowledge, representatives of the order Diprotodontia have epitheliochorial placenta, not endotheliochorial placenta as stated in the data set table; please see e.g. Skinner (2018, Encyclopedia of Reproduction, p. 459) who wrote, I quote: “All placentation in marsupials is epitheliochorial, in the sense that there is no sustained contact between the trophoblast of the fetus and the connective tissue of the uterine endometrium”. The authors should revise their classification and reanalyse their data.
5. I disagree with the statement that it is reasonable to pool male and female data. I agree with the authors that the majority of genes involved in placentation and reproduction are present in both sexes. Authors should support this claim with an appropriate citation. I have three main reasons for disagreeing with this methodological solution. First, there are marked sex differences in life histories and reproductive strategies in mammals. An extreme example are two marsupial families (Didelphidae and Dasyuridae) that contain species with male semelparity and female iteroparity. Second, these sex differences are reflected in a number of traits, including epigenetic aging (e.g. Anderson et al. 2021, eLife 10: e66128). Finally, third, the sexes are fundamentally different in cancer mechanisms (see Rubin et al. 2020, Biol. Sex Differ. 11: 17). Because this study is focused on reproduction in mammalian females and for the reasons stated above, I recommend using only female data.

Dujon et al. revised their manuscript in accordance with the comments I raised in the previous review process. I am satisfied with their responses and modifications of the manuscript. I agree with the authors’ interpretation of the results, including differences in reproductive effort and cancer defence mechanisms among the studied groups. However, I also believe the authors should address a few more points in their manuscript to improve its clarity and quality before its publication.

Comments to address
1. The authors should formulate clear, testable hypotheses (or predictions) regarding the expected effects of all key tested factors. They should mention them in the introduction and abstract of the manuscript. The results of the analyses should be discussed in the context of these hypotheses (predictions).
2. In my opinion, the authors should improve the presentation of their results (including supplementary materials 1-3). They stated that the selected models were compared using the Akaike’s Information Criterion (AIC) and AIC weights. I would recommend to add the values of delta AICc to show which of the candidate models are actually plausible (delta AICc < 9). The authors should then change the order of their models and discuss the results, including particular models, accordingly. This will allow them to better interpret their results.
3. Based on the results of Vincze et al. (2022, Nature 601: 263) the authors tested potential effect of diet type. I agree that diet is part of the cancer risk landscape of mammals in which multiple risk factors increase the probability of developing cancer during their lifetime. However, the presented results and their interpretation seem to be confusing. The authors stated that they found a significant interaction between diet and placentation, but a non-significant statistic is shown in the same sentence (L. 250). Could the authors please consider reformulating this sentence and discuss how the type of placentation relates to the type of diet and possible biological consequences of this interaction?
4. I also believe the authors should move discussion information from the Results (L. 261-262) to Discussion and discuss the observed relationship between gestation length and the incidence of cancer mortality (ICM).