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  1. Author Response

    Reviewer #2 (Public Review):

    Areas for Improvement: While I believe the overall experiment seemed quite strong, the statistical approach does not seem in-line with current recommendations. Most importantly, the authors appear to have used stepwise model reduction-including, importantly, removing non-significant fixed effects-to test the significance of predictors. Several simulation studies have shown that this increases the likelihood of false positive results (e.g., Mundry & Nunn 2009 Am. Nat., Forstmeier & Schielzeth 2001 Behav. Ecol. Sociobiol.). The above concern related to the fact that the authors reported some "trending" results (e.g., 0.05 < P < 0.10) as being relevant, but not others. A revised statistical approach may clear up confusion with this. I give recommendations to the authors regarding these issues in the "recommendations for authors" section.

    We have changed our statistical approach as per the reviewer’s suggestions (see responses to essential point 1 above and specific comments below). The reanalyses did not qualitatively change any of our original findings.

    The authors also appeared to "Gaussianise" response variable distributions. As a reader, I could not understand whether this took the place of fitting models using an appropriate error distributions for the response variable (e.g., Poisson), or whether this was a necessary step just for the distributions of the model residuals. It is important to give more details on this, to know if did or did not affect the conclusions of the study.

    We have reanalysed the number of caring events using a GLMM with a negative binomial distribution (Table S4b), and time spent caring for clutches using a GLMM with a Gaussian distribution and log link function (Table S5b), rather than “Gaussanising” these response variables (lines 649–655). This new analytical approach did not qualitatively change our findings.

    Finally, but perhaps most importantly, the lack of a clear set of hypotheses relevant to the specific variables measured here made it hard to understand the Results section. In the Results, the relevance of a given predictor was only described after the statistical significance of that predictor was revealed. This gives the appearance that the authors measured a wide range of factors and only describe the relevance of the ones revealed as significant.

    We have included a paragraph at the end of the Introduction (line 86ff.) in which we provide a clear set of hypotheses relating to potential effects of chronic outgroup conflict on reproductive rate, investment and output. These hypotheses are supported by relevant background information and references, and we explicitly mention all our specific response variables that are analysed.

    Reviewer #3 (Public Review):

    In my opinion the striking thing this about these results is that the intrusions were not physical encounters: it is not that the incurred groups were physically attacked or that eggs were eaten. Similarly, it wasn't that the 'invading' individuals were directly competing for food with the target group (or if they were eating some residual food then it would be no more than in the control condition). Although the strength of the paper is in the neat experimental design, this is unfortunately obscured due to insufficient explanation of the experiment prior to the results. But this shortcoming is superficial - the authors could move up some more details from the methods.

    We have expanded the description of our methods at the start of the Results section (line 114ff.).

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  2. Evaluation Summary:

    This paper uses controlled exposure to territorial intrusion to show that repeated exposure to conflict between groups compromises fitness in social fish. With a host of results relating to fertility, behavior, and parental investment, its findings will increase confidence in the argument that intergroup conflict is an important factor in social evolution. There are several statistical issues that should be addressed to minimize the possibility of false-positive results.

    (This preprint has been reviewed by eLife. We include the public reviews from the reviewers here; the authors also receive private feedback with suggested changes to the manuscript. Reviewer #3 agreed to share their name with the authors.)

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  3. Reviewer #1 (Public Review):

    Between-group competition is thought to be an important selective force shaping animal social behavior and social structure. However, because levels of between-group competition often covary with other aspects of the environment (e.g., food/resource density), it is difficult to evaluate how conflict between groups affects fitness outcomes per se, especially over longer time scales. To address this question, Braga Goncalves and Radford experimentally manipulate intergroup conflict in daffodil cichlids to compare fitness-related outcomes between groups chronically exposed to intruders versus those that were not. They find evidence that repeated exposure to intergroup conflict affects rates of clutch production, parental care behavior, egg size and composition, and, crucially, the overall rate of surviving offspring.

    The manuscript is clear and compelling, with a simple experimental design that is exploited to investigate a range of outcomes. The results indicate that repeated exposure to intergroup conflict has multimodal effects on fitness, not only for breeding adults, but also for the next generation (offspring of fish regularly exposed to intruders are smaller, slower to respond to a sudden stimulus, and less likely to survive their first month of life). Interestingly, these consequences are observable even in the absence of differences in resource availability, and without physical contact between intruders and resident fish. These findings highlight the importance of social stress caused by intergroup conflict, and suggest that species that encounter frequent conflict have experienced strong selection pressures to sense and respond to intrusion. Although the generalizability of these findings remains to be tested, they provide convincing empirical evidence in favor of the importance of between-group competition in social evolution.

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  4. Reviewer #2 (Public Review):

    Overall, this study has the potential to be illuminating to research in both intergroup conflict and social evolution. By staging repeated conflicts in a controlled environment, the researchers (to their knowledge, for the first time) measured a greater array of relevant responses to chronic intergroup conflict. They also discuss how they reveal indirect effects on offspring-i.e., not just immediate death or injury as a result of conflict. However, there may be some significant statistical issues to be addressed before the results are fully accepted.

    Pros: The authors made clear how this study was relevant, important, and timely. Intergroup conflict is a fast-growing field of research because we are beginning to understand that it might affect fitness, and therefore evolution, more than previously appreciated. By directly, and experimentally, studying impacts on fitness-not just in the short term (e.g., egg production) but in the longer term (e.g., young survival to one month)-the authors suggest important negative effects of intergroup conflict on fitness. It is also useful to note that these types of fitness effects have generally only been studied in mammals. Showing similar results in fish lends broader relevance to the importance of intergroup conflict to social evolution.

    Areas for Improvement: While I believe the overall experiment seemed quite strong, the statistical approach does not seem in-line with current recommendations. Most importantly, the authors appear to have used stepwise model reduction-including, importantly, removing non-significant fixed effects-to test the significance of predictors. Several simulation studies have shown that this increases the likelihood of false positive results (e.g., Mundry & Nunn 2009 Am. Nat., Forstmeier & Schielzeth 2001 Behav. Ecol. Sociobiol.). The above concern related to the fact that the authors reported some "trending" results (e.g., 0.05 < P < 0.10) as being relevant, but not others. A revised statistical approach may clear up confusion with this. I give recommendations to the authors regarding these issues in the "recommendations for authors" section.

    The authors also appeared to "Gaussianise" response variable distributions. As a reader, I could not understand whether this took the place of fitting models using an appropriate error distributions for the response variable (e.g., Poisson), or whether this was a necessary step just for the distributions of the model residuals. It is important to give more details on this, to know if did or did not affect the conclusions of the study.

    Finally, but perhaps most importantly, the lack of a clear set of hypotheses relevant to the specific variables measured here made it hard to understand the Results section. In the Results, the relevance of a given predictor was only described after the statistical significance of that predictor was revealed. This gives the appearance that the authors measured a wide range of factors and only describe the relevance of the ones revealed as significant.

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  5. Reviewer #3 (Public Review):

    In this paper, Goncalves and Radford report the results of two treatment/control experiments in which they simulated territorial incursions between groups of daffodil cichlids in the lab. In the treatment condition, fish from a neighbouring tank were temporarily placed behind a transparent panel in the tank of the focal group. The results of the experiments are quantified in great detail: the authors describe findings relating to the effect of the experimental treatment on (to name but a few measures): egg count, interclutch interval, offspring size and survival to one month, egg protein, and parental care. With so many results (I counted 43 p-values in the Results section) and several LMMs, there is a lot to consider the results. But the key finding is that the absolute number of offspring surviving to one month decreased over time in the treatment group. In my view, this is an important finding that will provide an experimental basis for solidifying the commonly made assumption that the well-established short-term costs of intergroup conflict is wild vertebrates will have fitness consequences in the medium/long term.

    In my opinion the striking thing this about these results is that the intrusions were not physical encounters: it is not that the incurred groups were physically attacked or that eggs were eaten. Similarly, it wasn't that the 'invading' individuals were directly competing for food with the target group (or if they were eating some residual food then it would be no more than in the control condition). Although the strength of the paper is in the neat experimental design, this is unfortunately obscured due to insufficient explanation of the experiment prior to the results. But this shortcoming is superficial - the authors could move up some more details from the methods. Apart from some minor changes suggested to the authors in another section I have no major concerns about this paper. I expect that these results will be of interest to a broad audience in behavioural ecology - they make an important contribution to our understanding of intergroup conflict, a phenomenon of clear importance to the evolution of animal behaviour which has been relatively neglected in the literature compared to studies of intragroup cooperation.

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