Author response:
The following is the authors’ response to the previous reviews.
We have carefully addressed all the reviewers' suggestions, and detailed responses are provided at the end of this letter. In summary:
• We conducted two additional replicates of the study to obtain more robust and reliable data.
• The Introduction has been revised for greater clarity and conciseness.
• The Results section was shortened and reorganized to highlight the key findings more effectively.
• The Discussion was modified according to the reviewers' suggestions, with a focus on reorganization and conciseness.
We hope you find this revised version of the manuscript satisfactory.
Reviewer #1 (Public Review):
Summary:
This study examines the role of host blood meal source, temperature, and photoperiod on the reproductive traits of Cx. quinquefasciatus, an important vector of numerous pathogens of medical importance. The host use pattern of Cx. quinquefasciatus is interesting in that it feeds on birds during spring and shifts to feeding on mammals towards fall. Various hypotheses have been proposed to explain the seasonal shift in host use in this species but have provided limited evidence. This study examines whether the shifting of host classes from birds to mammals towards autumn offers any reproductive advantages to Cx. quinquefasciatus in terms of enhanced fecundity, fertility, and hatchability of the offspring. The authors found no evidence of this, suggesting that alternate mechanisms may drive the seasonal shift in host use in Cx. quinquefasciatus.
Strengths:
Host blood meal source, temperature, and photoperiod were all examined together.
Weaknesses:
The study was conducted in laboratory conditions with a local population of Cx. quinquefasciatus from Argentina. I'm not sure if there is any evidence for a seasonal shift in the host use pattern in Cx. quinquefasciatus populations from the southern latitudes.
Comments on the revision:
Overall, I am not quite convinced about the possible shift in host use in the Argentinian populations of Cx. quinquefasciatus. The evidence from the papers that the authors cite is not strong enough to derive this conclusion. Therefore, I think that the introduction and discussion parts where they talk about host shift in Cx. quinquefasciatus should be removed completely as it misleads the readers. I suggest limiting the manuscript to talking only about the effects of blood meal source and seasonality on the reproductive outcomes of Cx. quinquefasciatus.
As mentioned in the previous revision, we agree on the reviewer observation about the lack of evidence on seasonal shift in the host use pattern in Cx. quinquefasciatus populations from Argentina. We include this topic in the discussion.
Additionally, we also added a paragraph in the discussion section to include the limitations of our study and conclusions. One of them is the fact that our results are based on controlled conditions experiments. Future studies are needed to elucidate if the same trend is found in the field.
Reviewer #1 (Recommendations for the authors):
Abstract
Line 73: shift in feeding behavior
Accepted as suggested.
Discussion
Line 258: addressed that Accepted as suggested.
Line 263: blood is nutritionally richer
Accepted as suggested.
Reviewer #2 (Public Review):
Summary:
Conceptually, this study is interesting and is the first attempt to account for the potentially interactive effects of seasonality and blood source on mosquito fitness, which the authors frame as a possible explanation for previously observed host-switching of Culex quinquefasciatus from birds to mammals in the fall. The authors hypothesize that if changes in fitness by blood source change between seasons, higher fitness on birds in the summer and on mammals in the autumn could drive observed host switching. To test this, the authors fed individuals from a colony of Cx. quinquefasciatus on chickens (bird model) and mice (mammal model) and subjected each of these two groups to two different environmental conditions reflecting the high and low temperatures and photoperiod experienced in summer and autumn in Córdoba, Argentina (aka seasonality). They measured fecundity, fertility, and hatchability over two gonotrophic cycles. The authors then used a generalized linear model to evaluate the impact of host species, seasonality, and gonotrophic cycle on fecundity, fertility, and hatchability. The authors were trying to test their hypothesis by determining whether there was an interactive effect of season and host species on mosquito fitness. This is an interesting hypothesis; if it had been supported, it would provide support for a new mechanism driving host switching. While the authors did report an interactive impact of seasonality and host species, the directionality of the effect was the opposite from that hypothesized. The authors have done a very good job of addressing many of the reviewer concerns, with several exception that continue to cause concern about the conclusions of the study.
Strengths:
(1) Using a combination of laboratory feedings and incubators to simulate seasonal environmental conditions is a good, controlled way to assess the potentially interactive impact of host species and seasonality on the fitness of Culex quinquefasciatus in the lab.
(2) The driving hypothesis is an interesting and creative way to think about a potential driver of host switching observed in the field.
(3) The manuscript has become a lot clearer and easier to read with the revisions - thank you to the authors for working hard to make many of the suggested changes.
Weaknesses:
(1) The authors have decided not to follow the suggestion of conducting experimental replicates of the study. This is understandable given the significant investment of resources and time necessary, however, it leaves the study lacking support. Experimental replication is an important feature of a strong study and helps to provide confidence that the observed patterns are real and replicable. Without replication, I continue to lack confidence in the conclusions of the study.
We included replicates as suggested.
(2) The authors have included some additional discussion about the counterintuitive nature of their results, but the paragraph discussing this in the discussion was confusing. I believe that this should be revised. This is a key point of the paper and needs to be clear to the reader.
Revised as suggested.
(3) There should be more discussion of the host switching observed in the two studies conducted in Argentina referenced by the authors. Since host switching is the foundation for the hypothesis tested in this paper, it is important to fully explain what is currently known in Argentina.
Accepted as suggested.
(4) In some cases, the explanations of referenced papers are not entirely accurate. For example, when referencing Erram et al 2022, I think the authors misrepresented the paper's discussion regarding pre-diuresis- Erram et al. are suggesting that pre-diuresis might be the mechanism by which C. furens compensates for the lower nutritional value of avian blood, leading to no significant difference between avian/mammal blood on fecundity/fertility (rather than leading to higher fecundity on birds, as stated in this manuscript). The study performed by Erram et al. also didn't prove this phenomenon, they just suggest it as a possible mechanism to explain their results, so that should be made clear when referencing the paper.
Changed as suggested.
(5) In some cases, the conclusions continue to be too strongly worded for the evidence available. For example, lines 322-324: I don't think the data is sufficient to conclude that a different physiological state is induced, nor that they are required to feed on a blood source that results in higher fitness.
Redaction was modified as suggested to tight our discussion with results.
(6) There is limited mention of the caveat that this experiment performed with simulated seasonality that does not perfectly replicate seasonality in the field. I think this caveat should be discussed in the discussion (e.g. that humidity is held constant).
This topic is now included in the discussion as suggested.
Reviewer #2 (Recommendations for the authors):
59-60: These terms should end with -phagic instead of -philic. These papers study blood feeding patterns, not preference. I understand that the Janssen papers calls it "mammalophilic" in their title, but this was an incorrect use of the term in their paper. There are some review papers that explain the difference in this terminology if it's helpful.
Accepted as suggested.
73: edit to "in" feeding behavior
Accepted as suggested.
77-78: Given that the premise of your study is based on the phenomenon of host switching, I suggest that you expand your discussion of these two papers. What did they observe? Which hosts did they switch from / to and how dramatic was the shift?
Accepted as suggested.
79: replace acknowledged with experienced
Accepted as suggested.
79-80: the way that this is written is misleading. It suggests that Spinsanti showed that seasonal variation in SLEV could be attributed to a host shift, which isn't true. This citation should come before the comma and then you should use more cautious language in the second half. E.g which MIGHT be possible to attribute to ....
Accepted as suggested.
80-82: this is not convincing. Even if the Robin isn't in Argentina, Argentina does have migrating birds, so couldn't this be the case for other species of birds? Do any of the birds observed in previous blood meal analyses in Argentina migrate? If so, couldn't this hypothesis indeed play a role?
A paragraph about this topic was added to the discussion as suggested.
90: hypotheses for what? The fall peak in cases? Or host switching?
Changed to be clearer.
98: where was this mentioned before? I think "as mentioned before" can be removed.
Accepted as suggested.
101: edit to "whether an interaction effect exists"
Accepted as suggested.
104: edit to "We hypothesize that..."
Accepted as suggested.
106: reported host USE changes, not host PREFERENCE changes, right?
All the terminology was change to host pattern and not preference to avoid confusion.
200: Briefly reading Carsey and Harden, it looks like the methodology was developed for social science. Is there anything you can cite to show this applied to other types of data? If not, I think this requires more explanation in your MS.
This was removed as replicates were included.
237-239: I think it is best not to make a definitive statement about greater/higher if it isn't statistically significant; I suggest modifying the sentences to state that the differences you are listing were not significantly different up front rather than at the end, otherwise if people aren't reading carefully, they may get the wrong impression.
Accepted as suggested.
245: you only use the term MS-I once before and I forgot what it meant since it wasn't repeated, so I had to search back through with command-F. I suggest writing this out rather than using the acronym.
Accepted as suggested.
249: edit to: "an interaction exists between the effect of..."
Accepted as suggested.
253-254: greater compared to what?
Change for clearness. 258-260: edit for grammar
Accepted as suggested.
260-262: edit for grammar; e.g. "However, this assumption lacks solid evidence; there is a scarcity of studies regarding nutritional quality of avian blood and its impact on mosquito fitness."
Accepted as suggested.
263: edit: blood is nutritionally...
Accepted as suggested.
264-267: This doesn't sound like an accurate interpretation of what the paper suggests regarding pre-diuresis in their discussion - they are suggesting that pre-diuresis might be the mechanism by which C. furens compensates for the lower nutritional value of avian blood, leading to no significant difference between avian/mammal blood on fecundity/fertility. They also don't show this, they just suggest it as a possible mechanism to explain their results.
This topic was removed given the restructuring of discussion.
253-269: You should tie this paragraph back to your results to explicitly compare/contrast your findings with the previous literature.
Accepted as suggested.
270-282: This paragraph would be a good place to explain the caveat of working in the laboratory - for example, humidity was the same across the two seasons which I'm guessing isn't the case in the field in Argentina. You can discuss what aspects of laboratory season simulation do not accurately replicate field conditions and how this can impact your findings. You said in your response to the reviewers that you weren't interested in measuring other variables (which is fair, and not expected!), but the beauty of the discussion section is to be able to think about how your experimental design might impact your results - one possibility is that your season simulation may not have produced the results produced by true seasonal shifts.
Accepted as suggested.
279-281: You say your experiment was conducted within the optimal range, which would suggest that both summer and autumn were within that range, but then you only talk about summer as optimal in the following sentence.
Changed for clearness.
281-282: You should clarify this sentence - state what the interaction has an effect on.
Accepted as suggested.
283-291: I appreciate that your discussion now acknowledges the small sample size and the questions that remain unanswered due to the results being opposite to that of the hypothesis, but this paragraph lacks some details and in places doesn't make sense.
I think you need to emphasize which groups had small sample size and which conclusions that might impact. I also think you need to explain why the sample size was substantially smaller for some groups (e.g. did they refuse to feed on the mouse in the autumn?). I appreciate that sample sizes are hard to keep high across many groups and two gonotrophic periods, but unfortunately, that is why fitness experiments are so hard to do and by their nature, take a long time. I understand that other papers have even lower sample size, but I was not asked to review those papers and would have had the same critique of them. I don't believe that creating simulated data via a Monte Carlo approach can make up for generating real data. As I understand it from your explanation, you are parametrizing the Monte Carlo simulations with your original data, which was small to begin with for autumn mouse. Using this simulation doesn't seem like a satisfactory replacement for an experimental replicate in my opinion. I maintain that at least a second replicate is necessary to see whether the patterns that you have observed hold.
The performing of a power analysis and addition of more replicates tried to solve the issue of sample size. More about this critic is added in the discussion. The simulation approach was totally removed.
Regarding the directionality of the interaction effect, I think this warrants more discussion. Lines 287-291 don't make sense to me. You suggest that feeding on birds in the autumn may confer a reproductive advantage when conditions are more challenging. But then why wouldn't they preferentially feed on birds in the autumn, rather than mammals? I suggest rewriting this paragraph to make it clearer.
Accepted as suggested.
297: earlier mentioned treatments? Do you mean compared to the first gonotrophic cycle? This isn't clear.
Changed for clearness.
302-303: Did you clarify whether you are allowed to reference unpublished data in eLife?
This was removed to follow the guidelines of eLife.
316-317: "it becomes apparent" sounds awkward, I suggest rewording and also explaining how this conclusion was made.
Accepted as suggested.
322-324: I think that this statement is too strongly worded. I don't think your data is sufficient to conclude that a different physiological state is induced, nor that they are required to feed on a blood source that results in higher fitness. Please modify this and make your conclusions more cautious and closely linked to what you actually demonstrated.
Accepted as suggested.
325: change will perform to would have
Accepted as suggested.
326: add to the sentence: "and vice versa in the summer"
Accepted as suggested.
330: possible explanations, not explaining scenarios.
Accepted as suggested.
517: I think you should repeat the abbreviation definitions in the caption to make it easier for readers, otherwise they have to flip back and forth which can be difficult depending on formatting.
Accepted as suggested.
In general, I think that your captions need more information. I think the best captions explain the figure relatively thoroughly such that the reader can look at the figure and caption and understand without reading the paper in depth. (e.g. the statistical test used).
Data availability: The eLife author instructions do say that data must be made available, so there should be a statement on data availability in your MS. I also suggest you make the code available.
Accepted as suggested.
