I would like to thank the authors for their reply.
All of my major concerns were now addressed by revising the text and providing further explanations in the responses.
Concerning the issue of EE calibration, I did not want to be too focused on swim tunnel and in vivo metabolism measure, but to my knowledge, it is likely the best reliable system to measure energy expenditure in fish. I fully understand that the authors did not perform that kind of experiment, due to the expensive cost of this very specific material.
They added a whole paragraph about that limitation, and the cautiousness needed for the interpretation of their results. This is fine for me.
I totally agree that these results should not be “thrown away” and that they should be kept as a first step of a really nice experimental setup to get some interesting parameters, and especially the roundness of fish under field conditions through a time period, and therefore to follow the temporal variation of the fish body condition in their natural environment.

This manuscript presents empirical data issued from accelerometers born by female Allis shad to detect spawning events and infer associated energetic expenditure. The authors seek to link behaviour to energy expenditure and loss of body condition over the reproductive season. The empirical data indicated that female shad exhausted their energetic stock faster than their egg stock. The authors conclude that this approach using accelerometers is promising for monitoring behaviour-dependent energy expenditure in the wild.
This is something of a pilot study that investigates how high technology sensors can be employed in the wild to measure important physiological parameters such as energy expenditure and infer behaviours that are otherwise impossible to observe. As such, the sample size is small (N = 8), partly due to protocol failure that was beyond the control of the authors, and the monitoring quite short (1 month). However, the feasibility of this kind of study will be of interest to behavioural ecologists across a wide range of cryptic species. Furthermore, the monitoring of energy expenditure, the raw currency of evolution, is an exciting and promising technological advance.

Comments on the revision:
This is a revised version of a manuscript I previously refereed. Overall, the authors have done a good job of taking into account the main points that I highlighted on the previous version. However, I still have a couple of outstanding queries:
Comment 25: I still do not understand the match between Fig. 4B and the text that describes it. The authors write: “the observed mass loss was on average 1.5 times more than predicted (479 g difference on average)”, but in the Figure observed mass loss varies between around 530g and 780g, while the predicted mass loss varies between around 50 and 250g. I cannot see how this generates the ratio of 1.5 that the authors state. This discrepancy is what I was referring to as “wrong” in my original comment.
Comment 27: while R2 values provide an estimation of the proportion of observed variation explained by a model, they do not provide information on differences in means, which is what I was referring to here. Indeed, now that the authors have also provided the latter (note that standard errors should also be included), it becomes apparent that some of the reported effect sizes are in fact very low (e.g. higher probability of spawning on warmer nights, higher TBF and energy expenditure at night vs day, etc.). This may or may not be a problem, but at least the reader can now better assess the support for the stated interpretations.
Finally, although the manuscript is globally well-written, there is still further scope for minor language improvement.

Mark Hewison

The dynamics of spawning acts by a semelparous fish and its associated energetic expenses
This manuscript presents empirical data issued from accelerometers born by female Allis shad to detect spawning events and infer associated energetic expenditure. The authors seek to link behaviour to energy expenditure and loss of body condition over the reproductive season. The empirical data indicated that female shad exhausted their energetic stock faster than their egg stock. The authors conclude that this approach using accelerometers is promising for monitoring behaviour-dependent energy expenditure in the wild.
This is something of a pilot study that investigates how high technology sensors can be employed in the wild to measure important physiological parameters such as energy expenditure and infer behaviours that are otherwise impossible to observe. As such, the sample size is small (N = 8), partly due to protocol failure that was beyond the control of the authors, and the monitoring quite short (1 month). However, the feasibility of this kind of study will be of interest to behavioural ecologists across a wide range of cryptic species. Furthermore, the monitoring of energy expenditure, the raw currency of evolution, is an exciting and promising technological advance. The manuscript is globally well-written, although there is scope for minor language improvement (particularly the abstract, see below), the analyses appear sound, and there is a lot of novel information here (although I am no specialist of the literature on this system). Below I list the some points that the authors might like to consider:

Major comments:
1. Lines 120-21: it is a bit of a shame to just put this at the end of the introduction, it reads like a throw away; while earlier the authors nicely set up the context around optimality of coincidence between gamete exhaustion and energetic exhaustion (Lines 72-78). Why not translate this into a hypothesis about what to expect in terms of mismatch, for example, in relation to water temperature, as they appear to do in the Abstract (although this needs to be more explicit, see below).
2. Hypotheses (end of Introduction): indeed, following on from the previous comment, it would be nice to have explicit hypotheses rather than just description at this point in the manuscript. What are the expectations for the link between temperature and spawning schedule? And how should this translate into energy expenditure? Much of the required contextual information for this actually appears in the first part of the methods, describing the study system and the predictions, which is unusual to say the least. I would much prefer to see much of this information in the Introduction leading to clear predictions. Please try to re-work the text to improve this aspect, providing enough contextual information on the study system to generate predictions in the Introduction, while keeping accessory detail (e.g. life cycle) in the Methods.
3. Calibration: The use of accelerometer data to estimate roundness is an interesting and novel application which the authors have calibrated against a traditional measure of body condition. However, I do feel that behavioural calibration for Tail Beat Frequency would also be useful, but there is no information provided. What information is available about the reliability of estimating tail beat frequency with accelerometer data? For spawning events, the authors did indeed do a calibration experiment, which is convincing, although it was based on a single couple. Could there be any inter-individual heterogeneity (see point 5) in the signal which might lead to faulty inference? This might be worth discussing.
4. Analysis: eg Line 325: what is considered night vs. day changes very fast across the spring. If activity is linked to daylight cycles, then it might be worthwhile considering a moving window for what is actually night-time determined by the times of sunrise and sunset. This could provide better precision when contrasting behaviour and energy expenditure across the 24h cycle.
5. Inter-individual heterogeneity: while I appreciate that the sample size is small, it would still be nice to discuss the inter-individual variability that the authors observed. For example, Line 545 there is a total energetic expenditure that varies by a factor of 2, which is considerable. Could this be linked to reproductive phenology? behaviour (eg swimming depth)? or reproductive allocation (eg spawning events)? This discussion (eg following on from line 566) would be of course a little speculative given the sample size, but an interesting perspective.

Minor comments:
1. Title: “costs” not “expenses” (also Line 589)
2. Abstract – this is the first time I have seen the expression “gametic budget”, and it is not immediately clear what that means. Consider modifying.
3. Line 45: synchronised among individuals? This needs to be clearer throughout.
4. Line 45-47: this sentence is not clear; perhaps “When daytime temperature was higher, they remained at greater depths, and spent more energy on nights when they swam at faster pace”.
5. Line 53-54: this is not easy to understand, can you help the reader interpret this prediction?
6. Line 77: “steep” is a bit strange here, “pronounced”?
7. Lines 78-80: not explicit enough ‘eg “social factors” is very vague, what do you mean by that? This sentence reads like an add-on which needs a mini-paragraph in itself.
8. Line 84: not “supervision”, “recording”?
9. lines 96-105: I am no expert here, but I was surprised that the authors did not refer to the use of dynamic body acceleration to index energy expenditure (e.g. in the Introduction,), reviewed in Wilson et al. 2019 J Anim Ecol (https://doi.org/10.1111/1365-2656.13040
10. Line 109: add “pattern”.
11. Line 117: “vertical plane” (and throughout the text)
12. Line 118 (and throughout): “thinning” is a bit strange, I would suggest “weight loss” or “loss of body condition”, but I acknowledge its not quite the same thing.
13. Line 132: although I understand the link, capital breeding is not necessarily associated with fasting. It is strictly related to the fact that energy for offsetting increased needs during reproduction are sourced from stored reserves, rather than from current intake (see Jonsson 1997 Oikos 78).
14. Line 149: replace “with a regular delay” by “by a consistent time elapse”
15. L163: “deviate” not “depart”
16. Line 181-3: not clear
17. Line 292: do you mean “compared with” ?
18. Line 319: this is fine, but be careful to be clear throughout the text that the synchronisation you wish to look for is “among” not “within” individuals.
19. Line 341: it’s a bit odd to come back to predictions at this stage of the manuscript. These aims/predictions should be clearer earlier (see above).
20. Fig 2: you do not have a measure of “longevity”. I presume this is supposed to be the number of days between capture and death, which may be related to longevity, but not necessarily. Please modify label.
21. Results: while the relationships are not strong, this is likely due to a lack of statistical power; it is notable however that the number of spawning acts seems to be negatively correlated with all the size/condition parameters, which is surprising to me, who knows nothing about this particular model. Worth discussing (eg Line 515)?
22. Line 418: “total energy expenditure” not “energy expenditure cumulated”
23. Line 421: “representing” not “making”
24. Fig 4 legend: spell out what TBF is in the legend
25. Line 426-7: unless I have misunderstood something, this seems to be wrong. The authors say “the predicted weight loss was on average 1.5 times less than the actual loss”, but the Fig 4 indicates that real weight loss was much higher than predicted, by up to 4 fold! Also, it would be more usual to turn the thing around, to say “observed weight loss was XX times more than predicted…”
26. Line 439: “experienced” not “underwent”
27. Lines 437-445: I would like to see the effect sizes for each of these also in the text, as they are not easy to judge in the Fig 5.
28. Fig 6B: this figure is the wrong way round, it would be more logical to show a decrease in condition over time from initial release until death
29. Line 468-73: it would be nice to have the full table of AIC values for all tested models as a Table in the Supplementary materials.
30. Lines 473-5: I do not really understand what this result means (or indeed why the period of the day is included in the model). Does this mean that the fish get fatter at night then thinner again during the day? Is body shape expected to vary at this temporal scale, within a 24h cycle?
31. Line 489: delete “individual”
32. Line 493: give effect size, by how much?
33. Line 494: “too high to allow shad to spawn all their eggs” is not clear, please clarify (females could not spawn all eggs prior to death due to energetic exhaustion? Or something like that).
34. Line 494: “novel”, not “original”
35. Line 496: for what? Be explicit as to the use of this approach
36. Line 529: “are reminiscent” not “remind”
37. Line 540: “end” not “final”
38. Line 541: “occurred in” not “struck”
39. Line 543 “with” not “to”
40. Line 557: “by” not “of”
41. Line 591: “fish have to conserve protein” not “fishes have to spare proteins”
42. Line 607: “wiped away” – this is not clear.
43. Line 633: while this is true, it is difficult to conclude that the two are not related; from Fig 6B, it seems that there is some degree of consistency in the two measures with the exception of the individual represented by the green line which has a much steeper slope than the others

Mark Hewison

This study deals with a really great idea to improve the protocols of non-invasive technics, to accurately estimate the energy expenditure of fish in the wild. Throughout the introduction, the authors explain the central role of studying energy allocation in the ecological context of spawning periods, using a highly relevant model, the anadromous Allis shad, which is a semelparous fish. This latter point is of interest, because the cost of reproduction corresponds almost to the total energy expenditure of the spawning period. And as a capital breeder, no food supply is expected. As stated line 81-82, the energy budget estimation of wild fish is really challenging. And with this study, the authors give some new tools for measuring some proxies. For example, using the accelerometers for evaluating the roundness of fishes is really interesting, but as highlighted by the authors, this method needs further investigation to be improved.

I however have some concerns about the other methods, which are described below. - The first concern is about the choice of external tags. Intuitively, I would think that this kind of device would negatively impact the locomotion, and the cost of transport, through an increase of drag force, for example, which is intensively commented in the literature in diving birds (Ropert-Coudert et al. 2000) or in fish (reviewed in Cooke et al. 2012). The authors referred to Breine et al. 2017 for the tagging protocol, and therefore, fish body mass should be higher than 900 g to be in accordance with the limit of 2% cited in Breine. Unfortunately, the morphological characteristics of fish (body mass, body length, width and height) are missing, but seem highly relevant to estimate the effect of tags on fish used in this experiment. I would suggest to add a table with these characteristics.

• As they did for characterizing the spawning act with the accelerometers, I wonder why the authors did not perform any preliminary test (i.e. in swim tunnel, in vivo respirometry) to validate their tagging protocol. A comparison among tagged, sham and control Allis shad would have been great to disentangle the consequences of these external tags in the fish performance. Indeed, some studies show that kind of results: Jepsen et al. (2015) described a list of possible effects of external tag, especially on swimming performance. Tagged fish get exhausted earlier than control ones, which could mean a higher energetic cost of locomotion with external tags. But Breine et al. explained that the effect of such external tag was still unknown in 2017.

• Line 613: “tagging did not seem to impair swimming activity either, as TBF was not lower in the three days following tagging than in the remaining of the season.” Could the authors clarify this sentence: is it the “spawning” season? Therefore, I did not catch the argument that the TBF was not lower in the 3 days after tagging. It would have been great to compare fish locomotion parameters before and after tagging, instead.

• For estimating the energy expenditure (EE) from the Tail Beat Frequency, the authors referred to equations from Leonard et al. (1999) and Castro-santos & Letcher (2010), which were fitted for adult American shad, during migration. In addition, these fish are iteroparous, which is an important point, when dealing with EE. The authors discuss about that very thoroughly in the “methodological considerations” (line 568 and beyond). I therefore wonder about the accuracy of the equations the authors used for EE calculations and if they are correct for Allis fish. Indeed, figure 4 B shows a huge difference between the modelled and the observed “weight” loss. Estimations of energy expenditure from biologgers need to be cautiously taken, due to the several parameters which are playing major roles. For instance, considering the fact that American shad were migrating and that Allis shad were spawning, swimming gaits are likely different and are sustained by two different muscle types, such as red and white fibers. As they are relying to two different metabolic pathways, red and white muscle would need separate equations to estimate EE (Gleiss et al., 2011). Again, preliminary studies in experimental conditions (swim tunnel + respirometry + accelerometers + video) would have been great to validate the EE calculation.

• In line with my last comment, concerning the metabolic fuels: even if carbohydrates only represent a small part of energetic substrates for long-term exercise, glycogen and lactate are commonly used for burst swimming (Moyes and West, 1995; Weber and Haman, 1996), which appears closely related to spawning effort. I do not understand why the authors assumed that shad get 69% of their energy from lipids and 31% of energy from proteins (lines 280-284). They cited the study of Leonard and McCormick (1999), which reports the energy use pattern of migrating American shad. Here, the main goal is about estimating the energy expenditure during spawning period, which is unlikely relying on the same pattern of swimming effort. Indeed, line 586, the authors wrote about recovery after sprint, citing Kieffer 2000.

I also have minor interrogations, Please find them below: - How to discriminate females from males? Is there any specific sexual character? - A picture of the equipped fish could be useful, in addition to the figure 1. - Roundness estimation is a great idea but is the position of the accelerometer accurate enough to generate good data? But I totally agree with the authors, if this new method could be fine-tuned, it will be of great interest for field eco-physiological studies.

• Figure 5.D needed? I did not understand the message, because this graph shows average cumulated EE per 8h. It does not take into account the duration (in contrast with the Fig. 4A) and did not give any further information. It would have been great to get the same graph for each spawning event. For example, what the EE for fish #1 (grey plot), which got 7 or 8 spawning acts the 11/06 (Fig. 3A).

• I am puzzled about using body weight instead of body mass.